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Title: The Foundations of Science: Science and Hypothesis, The Value of
Science, Science and Method

Author: Henri Poincaré

Author of introduction, etc.: Josiah Royce

Translator: George Bruce Halsted

Release date: May 16, 2012 [eBook #39713]

Language: English

Other information and formats: www.gutenberg.org/ebooks/39713

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*** START OF THE PROJECT GUTENBERG EBOOK THE
FOUNDATIONS OF SCIENCE: SCIENCE AND HYPOTHESIS, THE

VALUE OF SCIENCE, SCIENCE AND METHOD ***
SCIENCE AND EDUCATION

A SERIES OF VOLUMES FOR THE PROMOTION OF
SCIENTIFIC RESEARCH AND EDUCATIONAL PROGRESS

Edited by J. McKEEN CATTELL

VOLUME I—THE FOUNDATIONS OF SCIENCE

UNDER THE SAME EDITORSHIP

SCIENCE AND EDUCATION. A series of
volumes for the promotion of
scientific research and educational
progress.
Volume I. The Foundations of Science.
By H. Poincaré. Containing the
authorised English translation by
George Bruce Halsted of "Science
and Hypothesis," "The Value of
Science," and "Science and Method."
Volume II. Medical Research and
Education. By Richard Mills Pearce,
William H. Welch, W. H. Howell,
Franklin P. Mall, Lewellys F. Barker,
Charles S. Minot, W. B. Cannon, W.
T. Councilman Theobald Smith, G. N.

Stewart, C. M. Jackson, E. P. Lyon,
James B. Herrick, John M. Dodson,
C. R. Bardeen, W. Ophuls, S. J.
Meltzer, James Ewing, W. W. Keen,
Henry H. Donaldson, Christian A.
Herter, and Henry P. Bowditch.
Volume III. University Control. By J.
McKeen Cattell and other authors.
AMERICAN MEN OF SCIENCE. A
Biographical Directory.
SCIENCE. A weekly journal devoted to
the advancement of science. The
official organ of the American
Association for the Advancement of
Science.
THE POPULAR SCIENCE MONTHLY.
A monthly magazine devoted to the
diffusion of science.
THE AMERICAN NATURALIST. A
monthly journal devoted to the
biological sciences, with special
reference to the factors of evolution.

THE SCIENCE PRESS
NEW YORK GARRISON, N. Y.

THE FOUNDATIONS
OF SCIENCE

SCIENCE AND HYPOTHESIS
THE VALUE OF SCIENCE
SCIENCE AND METHOD

BY
H. POINCARÉ

AUTHORIZED TRANSLATION BY
GEORGE BRUCE HALSTED

WITH A SPECIAL PREFACE BY POINCARÉ, AND AN INTRODUCTION
BY JOSIAH ROYCE, HARVARD UNIVERSITY

THE SCIENCE PRESS
NEW YORK AND GARRISON, N. Y.
1913

Copyright, 1913
BY The Science Press

PRESS OF
THE NEW ERA PRINTING COMPANY
LANCASTER, PA.

CONTENTS
PAGE
Henri Poincaré ix
Author's Preface to the Translation 3
SCIENCE AND HYPOTHESIS
Introduction by Royce 9
Introduction 27
Part I. Number and Magnitude
Chapter I.—On the Nature of Mathematical Reasoning 31
Syllogistic Deduction 31
Verification and Proof 32
Elements of Arithmetic 33
Reasoning by Recurrence 37
Induction 40
Mathematical Construction 41
Chapter II.—Mathematical Magnitude and Experience 43
Definition of Incommensurables 44
The Physical Continuum 46
Creation of the Mathematical Continuum 46
Measurable Magnitude 49
Various Remarks (Curves without Tangents) 50
The Physical Continuum of Several Dimensions 52
The Mathematical Continuum of Several Dimensions 53
Part II. Space
Chapter III.—The Non-Euclidean Geometries 55
The Bolyai-Lobachevski Geometry 56
Riemann's Geometry 57
The Surfaces of Constant Curvature 58
Interpretation of Non-Euclidean Geometries 59
The Implicit Axioms 60

The Fourth Geometry 62
Lie's Theorem 62
Riemann's Geometries 63
On the Nature of Axioms 63
Chapter IV.—Space and Geometry 66
Geometric Space and Perceptual Space 66
Visual Space 67
Tactile Space and Motor Space 68
Characteristics of Perceptual Space 69
Change of State and Change of Position 70
Conditions of Compensation 72
Solid Bodies and Geometry 72
Law of Homogeneity 74
The Non-Euclidean World 75
The World of Four Dimensions 78
Conclusions 79
Chapter V.—Experience and Geometry 81
Geometry and Astronomy 81
The Law of Relativity 83
Bearing of Experiments 86
Supplement (What is a Point?) 89
Ancestral Experience 91
Part III. Force
Chapter VI.—The Classic Mechanics 92
The Principle of Inertia 93
The Law of Acceleration 97
Anthropomorphic Mechanics 103
The School of the Thread 104
Chapter VII.—Relative Motion and Absolute Motion 107
The Principle of Relative Motion 107
Newton's Argument 108
Chapter VIII.—Energy and Thermodynamics 115
Energetics 115
Thermodynamics 119

General Conclusions on Part III 123
Part IV. Nature
Chapter IX.—Hypotheses in Physics 127
The Rôle of Experiment and Generalization 127
The Unity of Nature 130
The Rôle of Hypothesis 133
Origin of Mathematical Physics 136
Chapter X.—The Theories of Modern Physics 140
Meaning of Physical Theories 140
Physics and Mechanism 144
Present State of the Science 148
Chapter XI.—The Calculus of Probabilities 155
Classification of the Problems of Probability 158
Probability in Mathematics 161
Probability in the Physical Sciences 164
Rouge et noir 167
The Probability of Causes 169
The Theory of Errors 170
Conclusions 172
Chapter XII.—Optics and Electricity 174
Fresnel's Theory 174
Maxwell's Theory 175
The Mechanical Explanation of Physical Phenomena 177
Chapter XIII.—Electrodynamics 184
Ampère's Theory 184
Closed Currents 185
Action of a Closed Current on a Portion of Current 186
Continuous Rotations 187
Mutual Action of Two Open Currents 189
Induction 190
Theory of Helmholtz 191
Difficulties Raised by these Theories 193
Maxwell's Theory 193
Rowland's Experiment 194

The Theory of Lorentz 196
THE VALUE OF SCIENCE
Translator's Introduction 201
Does the Scientist Create Science? 201
The Mind Dispelling Optical Illusions 202
Euclid not Necessary 202
Without Hypotheses, no Science 203
What Outcome? 203
Introduction 205
Part I. The Mathematical Sciences
Chapter I.—Intuition and Logic in Mathematics 210
Chapter II.—The Measure of Time 223
Chapter III.—The Notion of Space 235
Qualitative Geometry 238
The Physical Continuum of Several Dimensions 240
The Notion of Point 244
The Notion of Displacement 247
Visual Space 252
Chapter IV.—Space and its Three Dimensions 256
The Group of Displacements 256
Identity of Two Points 259
Tactile Space 264
Identity of the Different Spaces 268
Space and Empiricism 271
Rôle of the Semicircular Canals 276
Part II. The Physical Sciences
Chapter V.—Analysis and Physics 279
Chapter VI.—Astronomy 289
Chapter VII.—The History of Mathematical Physics 297
The Physics of Central Forces 297
The Physics of the Principles 299
Chapter VIII.—The Present Crisis in Physics 303
The New Crisis 303
Carnot's Principle 303

The Principle of Relativity 305
Newton's Principle 308
Lavoisier's Principle 310
Mayer's Principle 312
Chapter IX.—The Future of Mathematical Physics 314
The Principles and Experiment 314
The Rôle of the Analyst 314
Aberration and Astronomy 315
Electrons and Spectra 316
Conventions preceding Experiment 317
Future Mathematical Physics 319
Part III. The Objective Value of Science
Chapter X.—Is Science Artificial? 321
The Philosophy of LeRoy 321
Science, Rule of Action 323
The Crude Fact and the Scientific Fact 325
Nominalism and the Universal Invariant 333
Chapter XI.—Science and Reality 340
Contingence and Determinism 340
Objectivity of Science 347
The Rotation of the Earth 353
Science for Its Own Sake 354
SCIENCE AND METHOD
Introduction 359
Book I. Science and the Scientist
Chapter I.—The Choice of Facts 362
Chapter II.—The Future of Mathematics 369
Chapter III.—Mathematical Creation 383
Chapter IV.—Chance 395
Book II. Mathematical Reasoning
Chapter I.—The Relativity of Space 413
Chapter II.—Mathematical Definitions and Teaching 430
Chapter III.—Mathematics and Logic 448
Chapter IV.—The New Logics 460

Chapter V.—The Latest Efforts of the Logisticians 472
Book III. The New Mechanics
Chapter I.—Mechanics and Radium 486
Chapter II.—Mechanics and Optics 496
Chapter III.—The New Mechanics and Astronomy 512
Book IV. Astronomic Science
Chapter I.—The Milky Way and the Theory of Gases 523
Chapter II.—French Geodesy 535
General Conclusions 544
Index 547

HENRI POINCARÉ
Sir George Darwin, worthy son of an immortal father, said, referring to
what Poincaré was to him and to his work: "He must be regarded as the
presiding genius—or, shall I say, my patron saint?"
Henri Poincaré was born April 29, 1854, at Nancy, where his father was a
physician highly respected. His schooling was broken into by the war of
1870-71, to get news of which he learned to read the German newspapers.
He outclassed the other boys of his age in all subjects and in 1873 passed
highest into the École Polytechnique, where, like John Bolyai at Maros
Vásárhely, he followed the courses in mathematics without taking a note
and without the syllabus. He proceeded in 1875 to the School of Mines, and
was Nommé, March 26, 1879. But he won his doctorate in the University of
Paris, August 1, 1879, and was appointed to teach in the Faculté des
Sciences de Caen, December 1, 1879, whence he was quickly called to the
University of Paris, teaching there from October 21, 1881, until his death,
July 17, 1912. So it is an error to say he started as an engineer. At the early
age of thirty-two he became a member of l'Académie des Sciences, and,
March 5, 1908, was chosen Membre de l'Académie Française. July 1, 1909,
the number of his writings was 436.
His earliest publication was in 1878, and was not important. Afterward
came an essay submitted in competition for the Grand Prix offered in 1880,
but it did not win. Suddenly there came a change, a striking fire, a bursting
forth, in February, 1881, and Poincaré tells us the very minute it happened.
Mounting an omnibus, "at the moment when I put my foot upon the step,
the idea came to me, without anything in my previous thoughts seeming to
foreshadow it, that the transformations I had used to define the Fuchsian
functions were identical with those of non-Euclidean geometry." Thereby
was opened a perspective new and immense. Moreover, the magic wand of
his whole life-work had been grasped, the Aladdin's lamp had been rubbed,
non-Euclidean geometry, whose necromancy was to open up a new theory
of our universe, whose brilliant exposition was commenced in his book
Science and Hypothesis, which has been translated into six languages and

has already had a circulation of over 20,000. The non-Euclidean notion is
that of the possibility of alternative laws of nature, which in the
Introduction to the Électricité et Optique, 1901, is thus put: "If therefore a
phenomenon admits of a complete mechanical explanation, it will admit of
an infinity of Others which will account equally well for all the peculiarities
disclosed by experiment."
The scheme of laws of nature so largely due to Newton is merely one of
an infinite number of conceivable rational schemes for helping us master
and make experience; it is commode, convenient; but perhaps another may
be vastly more advantageous. The old conception of true has been revised.
The first expression of the new idea occurs on the title page of John
Bolyai's marvelous Science Absolute of Space, in the phrase "haud unquam
a priori decidenda."
With bearing on the history of the earth and moon system and the origin
of double stars, in formulating the geometric criterion of stability, Poincaré
proved the existence of a previously unknown pear-shaped figure, with the
possibility that the progressive deformation of this figure with increasing
angular velocity might result in the breaking up of the rotating body into
two detached masses. Of his treatise Les Méthodes nouvelles de la
Méchanique céleste, Sir George Darwin says: "It is probable that for half a
century to come it will be the mine from which humbler investigators will
excavate their materials." Brilliant was his appreciation of Poincaré in
presenting the gold medal of the Royal Astronomical Society. The three
others most akin in genius are linked with him by the Sylvester medal of the
Royal Society, the Lobachevski medal of the Physico-Mathematical Society
of Kazan, and the Bolyai prize of the Hungarian Academy of Sciences. His
work must be reckoned with the greatest mathematical achievements of
mankind.
The kernel of Poincaré's power lies in an oracle Sylvester often quoted to
me as from Hesiod: The whole is less than its part.
He penetrates at once the divine simplicity of the perfectly general case,
and thence descends, as from Olympus, to the special concrete earthly
particulars.

A combination of seemingly extremely simple analytic and geometric
concepts gave necessary general conclusions of immense scope from which
sprang a disconcerting wilderness of possible deductions. And so he leaves
a noble, fruitful heritage.
Says Love: "His right is recognized now, and it is not likely that future
generations will revise the judgment, to rank among the greatest
mathematicians of all time."
George Bruce Halsted.

SCIENCE AND HYPOTHESIS

AUTHOR'S PREFACE TO THE
TRANSLATION
I am exceedingly grateful to Dr. Halsted, who has been so good as to
present my book to American readers in a translation, clear and faithful.
Every one knows that this savant has already taken the trouble to
translate many European treatises and thus has powerfully contributed to
make the new continent understand the thought of the old.
Some people love to repeat that Anglo-Saxons have not the same way of
thinking as the Latins or as the Germans; that they have quite another way
of understanding mathematics or of understanding physics; that this way
seems to them superior to all others; that they feel no need of changing it,
nor even of knowing the ways of other peoples.

In that they would beyond question be wrong, but I do not believe that is
true, or, at least, that is true no longer. For some time the English and
Americans have been devoting themselves much more than formerly to the
better understanding of what is thought and said on the continent of Europe.
To be sure, each people will preserve its characteristic genius, and it
would be a pity if it were otherwise, supposing such a thing possible. If the
Anglo-Saxons wished to become Latins, they would never be more than
bad Latins; just as the French, in seeking to imitate them, could turn out
only pretty poor Anglo-Saxons.
And then the English and Americans have made scientific conquests they
alone could have made; they will make still more of which others would be
incapable. It would therefore be deplorable if there were no longer Anglo-
Saxons.
But continentals have on their part done things an Englishman could not
have done, so that there is no need either for wishing all the world Anglo-
Saxon.
Each has his characteristic aptitudes, and these aptitudes should be
diverse, else would the scientific concert resemble a quartet where every
one wanted to play the violin.
And yet it is not bad for the violin to know what the violon-cello is
playing, and vice versa.
This it is that the English and Americans are comprehending more and
more; and from this point of view the translations undertaken by Dr.
Halsted are most opportune and timely.
Consider first what concerns the mathematical sciences. It is frequently
said the English cultivate them only in view of their applications and even
that they despise those who have other aims; that speculations too abstract
repel them as savoring of metaphysic.
The English, even in mathematics, are to proceed always from the
particular to the general, so that they would never have an idea of entering
mathematics, as do many Germans, by the gate of the theory of aggregates.
They are always to hold, so to speak, one foot in the world of the senses,

and never burn the bridges keeping them in communication with reality.
They thus are to be incapable of comprehending or at least of appreciating
certain theories more interesting than utilitarian, such as the non-Euclidean
geometries. According to that, the first two parts of this book, on number
and space, should seem to them void of all substance and would only baffle
them.
But that is not true. And first of all, are they such uncompromising
realists as has been said? Are they absolutely refractory, I do not say to
metaphysic, but at least to everything metaphysical?
Recall the name of Berkeley, born in Ireland doubtless, but immediately
adopted by the English, who marked a natural and necessary stage in the
development of English philosophy.
Is this not enough to show they are capable of making ascensions
otherwise than in a captive balloon?
And to return to America, is not the Monist published at Chicago, that
review which even to us seems bold and yet which finds readers?
And in mathematics? Do you think American geometers are concerned
only about applications? Far from it. The part of the science they cultivate
most devotedly is the theory of groups of substitutions, and under its most
abstract form, the farthest removed from the practical.
Moreover, Dr. Halsted gives regularly each year a review of all
productions relative to the non-Euclidean geometry, and he has about him a
public deeply interested in his work. He has initiated this public into the
ideas of Hilbert, and he has even written an elementary treatise on 'Rational
Geometry,' based on the principles of the renowned German savant.
To introduce this principle into teaching is surely this time to burn all
bridges of reliance upon sensory intuition, and this is, I confess, a boldness
which seems to me almost rashness.
The American public is therefore much better prepared than has been
thought for investigating the origin of the notion of space.

Moreover, to analyze this concept is not to sacrifice reality to I know not
what phantom. The geometric language is after all only a language. Space is
only a word that we have believed a thing. What is the origin of this word
and of other words also? What things do they hide? To ask this is
permissible; to forbid it would be, on the contrary, to be a dupe of words; it
would be to adore a metaphysical idol, like savage peoples who prostrate
themselves before a statue of wood without daring to take a look at what is
within.
In the study of nature, the contrast between the Anglo-Saxon spirit and
the Latin spirit is still greater.
The Latins seek in general to put their thought in mathematical form; the
English prefer to express it by a material representation.
Both doubtless rely only on experience for knowing the world; when they
happen to go beyond this, they consider their foreknowledge as only
provisional, and they hasten to ask its definitive confirmation from nature
herself.
But experience is not all, and the savant is not passive; he does not wait
for the truth to come and find him, or for a chance meeting to bring him
face to face with it. He must go to meet it, and it is for his thinking to reveal
to him the way leading thither. For that there is need of an instrument; well,
just there begins the difference—the instrument the Latins ordinarily choose
is not that preferred by the Anglo-Saxons.
For a Latin, truth can be expressed only by equations; it must obey laws
simple, logical, symmetric and fitted to satisfy minds in love with
mathematical elegance.
The Anglo-Saxon to depict a phenomenon will first be engrossed in
making a model, and he will make it with common materials, such as our
crude, unaided senses show us them. He also makes a hypothesis, he
assumes implicitly that nature, in her finest elements, is the same as in the
complicated aggregates which alone are within the reach of our senses. He
concludes from the body to the atom.
Both therefore make hypotheses, and this indeed is necessary, since no
scientist has ever been able to get on without them. The essential thing is

never to make them unconsciously.
From this point of view again, it would be well for these two sorts of
physicists to know something of each other; in studying the work of minds
so unlike their own, they will immediately recognize that in this work there
has been an accumulation of hypotheses.
Doubtless this will not suffice to make them comprehend that they on
their part have made just as many; each sees the mote without seeing the
beam; but by their criticisms they will warn their rivals, and it may be
supposed these will not fail to render them the same service.
The English procedure often seems to us crude, the analogies they think
they discover to us seem at times superficial; they are not sufficiently
interlocked, not precise enough; they sometimes permit incoherences,
contradictions in terms, which shock a geometric spirit and which the
employment of the mathematical method would immediately have put in
evidence. But most often it is, on the other hand, very fortunate that they
have not perceived these contradictions; else would they have rejected their
model and could not have deduced from it the brilliant results they have
often made to come out of it.
And then these very contradictions, when they end by perceiving them,
have the advantage of showing them the hypothetical character of their
conceptions, whereas the mathematical method, by its apparent rigor and
inflexible course, often inspires in us a confidence nothing warrants, and
prevents our looking about us.
From another point of view, however, the two conceptions are very
unlike, and if all must be said, they are very unlike because of a common
fault.
The English wish to make the world out of what we see. I mean what we
see with the unaided eye, not the microscope, nor that still more subtile
microscope, the human head guided by scientific induction.
The Latin wants to make it out of formulas, but these formulas are still
the quintessenced expression of what we see. In a word, both would make
the unknown out of the known, and their excuse is that there is no way of
doing otherwise.

And yet is this legitimate, if the unknown be the simple and the known
the complex?
Shall we not get of the simple a false idea, if we think it like the complex,
or worse yet if we strive to make it out of elements which are themselves
compounds?
Is not each great advance accomplished precisely the day some one has
discovered under the complex aggregate shown by our senses something far
more simple, not even resembling it—as when Newton replaced Kepler's
three laws by the single law of gravitation, which was something simpler,
equivalent, yet unlike?
One is justified in asking if we are not on the eve of just such a
revolution or one even more important. Matter seems on the point of losing
its mass, its solidest attribute, and resolving itself into electrons. Mechanics
must then give place to a broader conception which will explain it, but
which it will not explain.
So it was in vain the attempt was made in England to construct the ether
by material models, or in France to apply to it the laws of dynamic.
The ether it is, the unknown, which explains matter, the known; matter is
incapable of explaining the ether.
Poincaré.

INTRODUCTION

BY PROFESSOR JOSIAH ROYCE

Harvard University
The treatise of a master needs no commendation through the words of a
mere learner. But, since my friend and former fellow student, the translator
of this volume, has joined with another of my colleagues, Professor Cattell,
in asking me to undertake the task of calling the attention of my fellow

students to the importance and to the scope of M. Poincaré's volume, I
accept the office, not as one competent to pass judgment upon the book, but
simply as a learner, desirous to increase the number of those amongst us
who are already interested in the type of researches to which M. Poincaré
has so notably contributed.

I
The branches of inquiry collectively known as the Philosophy of Science
have undergone great changes since the appearance of Herbert Spencer's
First Principles, that volume which a large part of the general public in this
country used to regard as the representative compend of all modern wisdom
relating to the foundations of scientific knowledge. The summary which M.
Poincaré gives, at the outset of his own introduction to the present work,
where he states the view which the 'superficial observer' takes of scientific
truth, suggests, not indeed Spencer's own most characteristic theories, but
something of the spirit in which many disciples of Spencer interpreting their
master's formulas used to conceive the position which science occupies in
dealing with experience. It was well known to them, indeed, that experience
is a constant guide, and an inexhaustible source both of novel scientific
results and of unsolved problems; but the fundamental Spencerian
principles of science, such as 'the persistence of force,' the 'rhythm of
motion' and the rest, were treated by Spencer himself as demonstrably
objective, although indeed 'relative' truths, capable of being tested once for
all by the 'inconceivability of the opposite,' and certain to hold true for the
whole 'knowable' universe. Thus, whether one dwelt upon the results of
such a mathematical procedure as that to which M. Poincaré refers in his
opening paragraphs, or whether, like Spencer himself, one applied the 'first
principles' to regions of less exact science, this confidence that a certain
orthodoxy regarding the principles of science was established forever was
characteristic of the followers of the movement in question. Experience,
lighted up by reason, seemed to them to have predetermined for all future
time certain great theoretical results regarding the real constitution of the
'knowable' cosmos. Whoever doubted this doubted 'the verdict of science.'
Some of us well remember how, when Stallo's 'Principles and Theories of
Modern Physics' first appeared, this sense of scientific orthodoxy was
shocked amongst many of our American readers and teachers of science. I

myself can recall to mind some highly authoritative reviews of that work in
which the author was more or less sharply taken to task for his ignorant
presumption in speaking with the freedom that he there used regarding such
sacred possessions of humanity as the fundamental concepts of physics.
That very book, however, has quite lately been translated into German as a
valuable contribution to some of the most recent efforts to reconstitute a
modern 'philosophy of nature.' And whatever may be otherwise thought of
Stallo's critical methods, or of his results, there can be no doubt that, at the
present moment, if his book were to appear for the first time, nobody would
attempt to discredit the work merely on account of its disposition to be
agnostic regarding the objective reality of the concepts of the kinetic theory
of gases, or on account of its call for a logical rearrangement of the
fundamental concepts of the theory of energy. We are no longer able so
easily to know heretics at first sight.
For we now appear to stand in this position: The control of natural
phenomena, which through the sciences men have attained, grows daily
vaster and more detailed, and in its details more assured. Phenomena men
know and predict better than ever. But regarding the most general theories,
and the most fundamental, of science, there is no longer any notable
scientific orthodoxy. Thus, as knowledge grows firmer and wider,
conceptual construction becomes less rigid. The field of the theoretical
philosophy of nature—yes, the field of the logic of science—this whole
region is to-day an open one. Whoever will work there must indeed accept
the verdict of experience regarding what happens in the natural world. So
far he is indeed bound. But he may undertake without hindrance from mere
tradition the task of trying afresh to reduce what happens to conceptual
unity. The circle-squarers and the inventors of devices for perpetual motion
are indeed still as unwelcome in scientific company as they were in the days
when scientific orthodoxy was more rigidly defined; but that is not because
the foundations of geometry are now viewed as completely settled, beyond
controversy, nor yet because the 'persistence of force' has been finally so
defined as to make the 'opposite inconceivable' and the doctrine of energy
beyond the reach of novel formulations. No, the circle-squarers and the
inventors of devices for perpetual motion are to-day discredited, not
because of any unorthodoxy of their general philosophy of nature, but
because their views regarding special facts and processes stand in conflict

with certain equally special results of science which themselves admit of
very various general theoretical interpretations. Certain properties of the
irrational number π are known, in sufficient multitude to justify the
mathematician in declining to listen to the arguments of the circle-squarer;
but, despite great advances, and despite the assured results of Dedekind, of
Cantor, of Weierstrass and of various others, the general theory of the logic
of the numbers, rational and irrational, still presents several important
features of great obscurity; and the philosophy of the concepts of geometry
yet remains, in several very notable respects, unconquered territory, despite
the work of Hilbert and of Pieri, and of our author himself. The ordinary
inventors of the perpetual motion machines still stand in conflict with
accepted generalizations; but nobody knows as yet what the final form of
the theory of energy will be, nor can any one say precisely what place the
phenomena of the radioactive bodies will occupy in that theory. The
alchemists would not be welcome workers in modern laboratories; yet some
sorts of transformation and of evolution of the elements are to-day matters
which theory can find it convenient, upon occasion, to treat as more or less
exactly definable possibilities; while some newly observed phenomena tend
to indicate, not indeed that the ancient hopes of the alchemists were well
founded, but that the ultimate constitution of matter is something more
fluent, less invariant, than the theoretical orthodoxy of a recent period
supposed. Again, regarding the foundations of biology, a theoretical
orthodoxy grows less possible, less definable, less conceivable (even as a
hope) the more knowledge advances. Once 'mechanism' and 'vitalism' were
mutually contradictory theories regarding the ultimate constitution of living
bodies. Now they are obviously becoming more and more 'points of view,'
diverse but not necessarily conflicting. So far as you find it convenient to
limit your study of vital processes to those phenomena which distinguish
living matter from all other natural objects, you may assume, in the modern
'pragmatic' sense, the attitude of a 'neo-vitalist.' So far, however, as you are
able to lay stress, with good results, upon the many ways in which the life
processes can be assimilated to those studied in physics and in chemistry,
you work as if you were a partisan of 'mechanics.' In any case, your special
science prospers by reason of the empirical discoveries that you make. And
your theories, whatever they are, must not run counter to any positive
empirical results. But otherwise, scientific orthodoxy no longer

predetermines what alone it is respectable for you to think about the nature
of living substance.
This gain in the freedom of theory, coming, as it does, side by side with a
constant increase of a positive knowledge of nature, lends itself to various
interpretations, and raises various obvious questions.

II
One of the most natural of these interpretations, one of the most obvious
of these questions, may be readily stated. Is not the lesson of all these recent
discussions simply this, that general theories are simply vain, that a
philosophy of nature is an idle dream, and that the results of science are
coextensive with the range of actual empirical observation and of successful
prediction? If this is indeed the lesson, then the decline of theoretical
orthodoxy in science is—like the eclipse of dogma in religion—merely a
further lesson in pure positivism, another proof that man does best when he
limits himself to thinking about what can be found in human experience,
and in trying to plan what can be done to make human life more
controllable and more reasonable. What we are free to do as we please—is
it any longer a serious business? What we are free to think as we please—is
it of any further interest to one who is in search of truth? If certain general
theories are mere conceptual constructions, which to-day are, and to-
morrow are cast into the oven, why dignify them by the name of
philosophy? Has science any place for such theories? Why be a 'neo-
vitalist,' or an 'evolutionist,' or an 'atomist,' or an 'Energetiker'? Why not
say, plainly: "Such and such phenomena, thus and thus described, have been
observed; such and such experiences are to be expected, since the
hypotheses by the terms of which we are required to expect them have been
verified too often to let us regard the agreement with experience as due
merely to chance; so much then with reasonable assurance we know; all
else is silence—or else is some matter to be tested by another experiment?"
Why not limit our philosophy of science strictly to such a counsel of
resignation? Why not substitute, for the old scientific orthodoxy, simply a
confession of ignorance, and a resolution to devote ourselves to the
business of enlarging the bounds of actual empirical knowledge?

Such comments upon the situation just characterized are frequently
made. Unfortunately, they seem not to content the very age whose revolt
from the orthodoxy of traditional theory, whose uncertainty about all
theoretical formulations, and whose vast wealth of empirical discoveries
and of rapidly advancing special researches, would seem most to justify
these very comments. Never has there been better reason than there is to-
day to be content, if rational man could be content, with a pure positivism.
The splendid triumphs of special research in the most various fields, the
constant increase in our practical control over nature—these, our positive
and growing possessions, stand in glaring contrast to the failure of the
scientific orthodoxy of a former period to fix the outlines of an ultimate
creed about the nature of the knowable universe. Why not 'take the cash and
let the credit go'? Why pursue the elusive theoretical 'unification' any
further, when what we daily get from our sciences is an increasing wealth of
detailed information and of practical guidance?
As a fact, however, the known answer of our own age to these very
obvious comments is a constant multiplication of new efforts towards large
and unifying theories. If theoretical orthodoxy is no longer clearly
definable, theoretical construction was never more rife. The history of the
doctrine of evolution, even in its most recent phases, when the theoretical
uncertainties regarding the 'factors of evolution' are most insisted upon, is
full of illustrations of this remarkable union of scepticism in critical work
with courage regarding the use of the scientific imagination. The history of
those controversies regarding theoretical physics, some of whose principal
phases M. Poincaré, in his book, sketches with the hand of the master, is
another illustration of the consciousness of the time. Men have their
freedom of thought in these regions; and they feel the need of making
constant and constructive use of this freedom. And the men who most feel
this need are by no means in the majority of cases professional
metaphysicians—or students who, like myself, have to view all these
controversies amongst the scientific theoreticians from without as learners.
These large theoretical constructions are due, on the contrary, in a great
many cases to special workers, who have been driven to the freedom of
philosophy by the oppression of experience, and who have learned in the
conflict with special problems the lesson that they now teach in the form of
general ideas regarding the philosophical aspects of science.

Why, then, does science actually need general theories, despite the fact
that these theories inevitably alter and pass away? What is the service of a
philosophy of science, when it is certain that the philosophy of science
which is best suited to the needs of one generation must be superseded by
the advancing insight of the next generation? Why must that which
endlessly grows, namely, man's knowledge of the phenomenal order of
nature, be constantly united in men's minds with that which is certain to
decay, namely, the theoretical formulation of special knowledge in more or
less completely unified systems of doctrine?
I understand our author's volume to be in the main an answer to this
question. To be sure, the compact and manifold teachings which this text
contains relate to a great many different special issues. A student interested
in the problems of the philosophy of mathematics, or in the theory of
probabilities, or in the nature and office of mathematical physics, or in still
other problems belonging to the wide field here discussed, may find what
he wants here and there in the text, even in case the general issues which
give the volume its unity mean little to him, or even if he differs from the
author's views regarding the principal issues of the book. But in the main,
this volume must be regarded as what its title indicates—a critique of the
nature and place of hypothesis in the work of science and a study of the
logical relations of theory and fact. The result of the book is a substantial
justification of the scientific utility of theoretical construction—an
abandonment of dogma, but a vindication of the rights of the constructive
reason.

III
The most notable of the results of our author's investigation of the logic
of scientific theories relates, as I understand his work, to a topic which the
present state of logical investigation, just summarized, makes especially
important, but which has thus far been very inadequately treated in the text-
books of inductive logic. The useful hypotheses of science are of two kinds:
1. The hypotheses which are valuable precisely because they are either
verifiable or else refutable through a definite appeal to the tests furnished
by experience; and

2. The hypotheses which, despite the fact that experience suggests them,
are valuable despite, or even because, of the fact that experience can neither
confirm nor refute them. The contrast between these two kinds of
hypotheses is a prominent topic of our author's discussion.
Hypotheses of the general type which I have here placed first in order are
the ones which the text-books of inductive logic and those summaries of
scientific method which are customary in the course of the elementary
treatises upon physical science are already accustomed to recognize and to
characterize. The value of such hypotheses is indeed undoubted. But
hypotheses of the type which I have here named in the second place are far
less frequently recognized in a perfectly explicit way as useful aids in the
work of special science. One usually either fails to admit their presence in
scientific work, or else remains silent as to the reasons of their usefulness.
Our author's treatment of the work of science is therefore especially marked
by the fact that he explicitly makes prominent both the existence and the
scientific importance of hypotheses of this second type. They occupy in his
discussion a place somewhat analogous to each of the two distinct positions
occupied by the 'categories' and the 'forms of sensibility,' on the one hand,
and by the 'regulative principles of the reason,' on the other hand, in the
Kantian theory of our knowledge of nature. That is, these hypotheses which
can neither be confirmed nor refuted by experience appear, in M. Poincaré's
account, partly (like the conception of 'continuous quantity') as devices of
the understanding whereby we give conceptual unity and an invisible
connectedness to certain types of phenomenal facts which come to us in a
discrete form and in a confused variety; and partly (like the larger
organizing concepts of science) as principles regarding the structure of the
world in its wholeness; i. e., as principles in the light of which we try to
interpret our experience, so as to give to it a totality and an inclusive unity
such as Euclidean space, or such as the world of the theory of energy is
conceived to possess. Thus viewed, M. Poincaré's logical theory of this
second class of hypotheses undertakes to accomplish, with modern means
and in the light of to-day's issues, a part of what Kant endeavored to
accomplish in his theory of scientific knowledge with the limited means
which were at his disposal. Those aspects of science which are determined
by the use of the hypotheses of this second kind appear in our author's
account as constituting an essential human way of viewing nature, an

interpretation rather than a portrayal or a prediction of the objective facts of
nature, an adjustment of our conceptions of things to the internal needs of
our intelligence, rather than a grasping of things as they are in themselves.
To be sure, M. Poincaré's view, in this portion of his work, obviously
differs, meanwhile, from that of Kant, as well as this agrees, in a measure,
with the spirit of the Kantian epistemology. I do not mean therefore to class
our author as a Kantian. For Kant, the interpretations imposed by the 'forms
of sensibility,' and by the 'categories of the understanding,' upon our
doctrine of nature are rigidly predetermined by the unalterable 'form' of our
intellectual powers. We 'must' thus view facts, whatever the data of sense
must be. This, of course, is not M. Poincaré's view. A similarly rigid
predetermination also limits the Kantian 'ideas of the reason' to a certain set
of principles whose guidance of the course of our theoretical investigations
is indeed only 'regulative,' but is 'a priori,' and so unchangeable. For M.
Poincaré, on the contrary, all this adjustment of our interpretations of
experience to the needs of our intellect is something far less rigid and
unalterable, and is constantly subject to the suggestions of experience. We
must indeed interpret in our own way; but our way is itself only relatively
determinate; it is essentially more or less plastic; other interpretations of
experience are conceivable. Those that we use are merely the ones found to
be most convenient. But this convenience is not absolute necessity.
Unverifiable and irrefutable hypotheses in science are indeed, in general,
indispensable aids to the organization and to the guidance of our
interpretation of experience. But it is experience itself which points out to
us what lines of interpretation will prove most convenient. Instead of Kant's
rigid list of a priori 'forms,' we consequently have in M. Poincaré's account
a set of conventions, neither wholly subjective and arbitrary, nor yet
imposed upon us unambiguously by the external compulsion of experience.
The organization of science, so far as this organization is due to hypotheses
of the kind here in question, thus resembles that of a constitutional
government—neither absolutely necessary, nor yet determined apart from
the will of the subjects, nor yet accidental—a free, yet not a capricious
establishment of good order, in conformity with empirical needs.
Characteristic remains, however, for our author, as, in his decidedly
contrasting way, for Kant, the thought that without principles which at every
stage transcend precise confirmation through such experience as is then

accessible the organization of experience is impossible. Whether one views
these principles as conventions or as a priori 'forms,' they may therefore be
described as hypotheses, but as hypotheses that, while lying at the basis of
our actual physical sciences, at once refer to experience and help us in
dealing with experience, and are yet neither confirmed nor refuted by the
experiences which we possess or which we can hope to attain.
Three special instances or classes of instances, according to our author's
account, may be used as illustrations of this general type of hypotheses.
They are: (1) The hypothesis of the existence of continuous extensive
quanta in nature; (2) The principles of geometry; (3) The principles of
mechanics and of the general theory of energy. In case of each of these
special types of hypotheses we are at first disposed, apart from reflection, to
say that we find the world to be thus or thus, so that, for instance, we can
confirm the thesis according to which nature contains continuous
magnitudes; or can prove or disprove the physical truth of the postulates of
Euclidean geometry; or can confirm by definite experience the objective
validity of the principles of mechanics. A closer examination reveals,
according to our author, the incorrectness of all such opinions. Hypotheses
of these various special types are needed; and their usefulness can be
empirically shown. They are in touch with experience; and that they are not
merely arbitrary conventions is also verifiable. They are not a priori
necessities; and we can easily conceive intelligent beings whose experience
could be best interpreted without using these hypotheses. Yet these
hypotheses are not subject to direct confirmation or refutation by
experience. They stand then in sharp contrast to the scientific hypotheses of
the other, and more frequently recognized, type, i. e., to the hypotheses
which can be tested by a definite appeal to experience. To these other
hypotheses our author attaches, of course, great importance. His treatment
of them is full of a living appreciation of the significance of empirical
investigation. But the central problem of the logic of science thus becomes
the problem of the relation between the two fundamentally distinct types of
hypotheses, i. e., between those which can not be verified or refuted
through experience, and those which can be empirically tested.

IV

The detailed treatment which M. Poincaré gives to the problem thus
defined must be learned from his text. It is no part of my purpose to
expound, to defend or to traverse any of his special conclusions regarding
this matter. Yet I can not avoid observing that, while M. Poincaré strictly
confines his illustrations and his expressions of opinion to those regions of
science wherein, as special investigator, he is himself most at home, the
issues which he thus raises regarding the logic of science are of even more
critical importance and of more impressive interest when one applies M.
Poincaré's methods to the study of the concepts and presuppositions of the
organic and of the historical and social sciences, than when one confines
one's attention, as our author here does, to the physical sciences. It belongs
to the province of an introduction like the present to point out, however
briefly and inadequately, that the significance of our author's ideas extends
far beyond the scope to which he chooses to confine their discussion.
The historical sciences, and in fact all those sciences such as geology,
and such as the evolutionary sciences in general, undertake theoretical
constructions which relate to past time. Hypotheses relating to the more or
less remote past stand, however, in a position which is very interesting from
the point of view of the logic of science. Directly speaking, no such
hypothesis is capable of confirmation or of refutation, because we can not
return into the past to verify by our own experience what then happened.
Yet indirectly, such hypotheses may lead to predictions of coming
experience. These latter will be subject to control. Thus, Schliemann's
confidence that the legend of Troy had a definite historical foundation led to
predictions regarding what certain excavations would reveal. In a sense
somewhat different from that which filled Schliemann's enthusiastic mind,
these predictions proved verifiable. The result has been a considerable
change in the attitude of historians toward the legend of Troy. Geological
investigation leads to predictions regarding the order of the strata or the
course of mineral veins in a district, regarding the fossils which may be
discovered in given formations, and so on. These hypotheses are subject to
the control of experience. The various theories of evolutionary doctrine
include many hypotheses capable of confirmation and of refutation by
empirical tests. Yet, despite all such empirical control, it still remains true
that whenever a science is mainly concerned with the remote past, whether
this science be archeology, or geology, or anthropology, or Old Testament

history, the principal theoretical constructions always include features
which no appeal to present or to accessible future experience can ever
definitely test. Hence the suspicion with which students of experimental
science often regard the theoretical constructions of their confrères of the
sciences that deal with the past. The origin of the races of men, of man
himself, of life, of species, of the planet; the hypotheses of anthropologists,
of archeologists, of students of 'higher criticism'—all these are matters
which the men of the laboratory often regard with a general incredulity as
belonging not at all to the domain of true science. Yet no one can doubt the
importance and the inevitableness of endeavoring to apply scientific method
to these regions also. Science needs theories regarding the past history of
the world. And no one who looks closer into the methods of these sciences
of past time can doubt that verifiable and unverifiable hypotheses are in all
these regions inevitably interwoven; so that, while experience is always the
guide, the attitude of the investigator towards experience is determined by
interests which have to be partially due to what I should call that 'internal
meaning,' that human interest in rational theoretical construction which
inspires the scientific inquiry; and the theoretical constructions which
prevail in such sciences are neither unbiased reports of the actual
constitution of an external reality, nor yet arbitrary constructions of fancy.
These constructions in fact resemble in a measure those which M. Poincaré
in this book has analyzed in the case of geometry. They are constructions
molded, but not predetermined in their details, by experience. We report
facts; we let the facts speak; but we, as we investigate, in the popular
phrase, 'talk back' to the facts. We interpret as well as report. Man is not
merely made for science, but science is made for man. It expresses his
deepest intellectual needs, as well as his careful observations. It is an effort
to bring internal meanings into harmony with external verifications. It
attempts therefore to control, as well as to submit, to conceive with rational
unity, as well as to accept data. Its arts are those directed towards self-
possession as well as towards an imitation of the outer reality which we
find. It seeks therefore a disciplined freedom of thought. The discipline is as
essential as the freedom; but the latter has also its place. The theories of
science are human, as well as objective, internally rational, as well as (when
that is possible) subject to external tests.

In a field very different from that of the historical sciences, namely, in a
science of observation and of experiment, which is at the same time an
organic science, I have been led in the course of some study of the history
of certain researches to notice the existence of a theoretical conception
which has proved extremely fruitful in guiding research, but which
apparently resembles in a measure the type of hypotheses of which M.
Poincaré speaks when he characterizes the principles of mechanics and of
the theory of energy. I venture to call attention here to this conception,
which seems to me to illustrate M. Poincaré's view of the functions of
hypothesis in scientific work.
The modern science of pathology is usually regarded as dating from the
earlier researches of Virchow, whose 'Cellular Pathology' was the outcome
of a very careful and elaborate induction. Virchow, himself, felt a strong
aversion to mere speculation. He endeavored to keep close to observation,
and to relieve medical science from the control of fantastic theories, such as
those of the Naturphilosophen had been. Yet Virchow's researches were, as
early as 1847, or still earlier, already under the guidance of a theoretical
presupposition which he himself states as follows: "We have learned to
recognize," he says, "that diseases are not autonomous organisms, that they
are no entities that have entered into the body, that they are no parasites
which take root in the body, but that they merely show us the course of the
vital processes under altered conditions" ('dasz sie nur Ablauf der
Lebenserscheinungen unter veränderten Bedingungen darstellen').
The enormous importance of this theoretical presupposition for all the
early successes of modern pathological investigation is generally
recognized by the experts. I do not doubt this opinion. It appears to be a
commonplace of the history of this science. But in Virchow's later years this
very presupposition seemed to some of his contemporaries to be called in
question by the successes of recent bacteriology. The question arose
whether the theoretical foundations of Virchow's pathology had not been set
aside. And in fact the theory of the parasitical origin of a vast number of
diseased conditions has indeed come upon an empirical basis to be
generally recognized. Yet to the end of his own career Virchow stoutly
maintained that in all its essential significance his own fundamental
principle remained quite untouched by the newer discoveries. And, as a
fact, this view could indeed be maintained. For if diseases proved to be the

consequences of the presence of parasites, the diseases themselves, so far as
they belonged to the diseased organism, were still not the parasites, but
were, as before, the reaction of the organism to the veränderte Bedingungen
which the presence of the parasites entailed. So Virchow could well insist.
And if the famous principle in question is only stated with sufficient
generality, it amounts simply to saying that if a disease involves a change in
an organism, and if this change is subject to law at all, then the nature of the
organism and the reaction of the organism to whatever it is which causes
the disease must be understood in case the disease is to be understood.
For this very reason, however, Virchow's theoretical principle in its most
general form could be neither confirmed nor refuted by experience. It would
remain empirically irrefutable, so far as I can see, even if we should learn
that the devil was the true cause of all diseases. For the devil himself would
then simply predetermine the veränderte Bedingungen to which the
diseased organism would be reacting. Let bullets or bacteria, poisons or
compressed air, or the devil be the Bedingungen to which a diseased
organism reacts, the postulate that Virchow states in the passage just quoted
will remain irrefutable, if only this postulate be interpreted to meet the case.
For the principle in question merely says that whatever entity it may be,
bullet, or poison, or devil, that affects the organism, the disease is not that
entity, but is the resulting alteration in the process of the organism.
I insist, then, that this principle of Virchow's is no trial supposition, no
scientific hypothesis in the narrower sense—capable of being submitted to
precise empirical tests. It is, on the contrary, a very precious leading idea, a
theoretical interpretation of phenomena, in the light of which observations
are to be made—'a regulative principle' of research. It is equivalent to a
resolution to search for those detailed connections which link the processes
of disease to the normal process of the organism. Such a search undertakes
to find the true unity, whatever that may prove to be, wherein the
pathological and the normal processes are linked. Now without some such
leading idea, the cellular pathology itself could never have been reached;
because the empirical facts in question would never have been observed.
Hence this principle of Virchow's was indispensable to the growth of his
science. Yet it was not a verifiable and not a refutable hypothesis. One value
of unverifiable and irrefutable hypotheses of this type lies, then, in the sort
of empirical inquiries which they initiate, inspire, organize and guide. In

these inquiries hypotheses in the narrower sense, that is, trial propositions
which are to be submitted to definite empirical control, are indeed
everywhere present. And the use of the other sort of principles lies wholly
in their application to experience. Yet without what I have just proposed to
call the 'leading ideas' of a science, that is, its principles of an unverifiable
and irrefutable character, suggested, but not to be finally tested, by
experience, the hypotheses in the narrower sense would lack that guidance
which, as M. Poincaré has shown, the larger ideas of science give to
empirical investigation.

V
I have dwelt, no doubt, at too great length upon one aspect only of our
author's varied and well-balanced discussion of the problems and concepts
of scientific theory. Of the hypotheses in the narrower sense and of the
value of direct empirical control, he has also spoken with the authority and
the originality which belong to his position. And in dealing with the
foundations of mathematics he has raised one or two questions of great
philosophical import into which I have no time, even if I had the right, to
enter here. In particular, in speaking of the essence of mathematical
reasoning, and of the difficult problem of what makes possible novel results
in the field of pure mathematics, M. Poincaré defends a thesis regarding the
office of 'demonstration by recurrence'—a thesis which is indeed
disputable, which has been disputed and which I myself should be disposed,
so far as I at present understand the matter, to modify in some respects,
even in accepting the spirit of our author's assertion. Yet there can be no
doubt of the importance of this thesis, and of the fact that it defines a
characteristic that is indeed fundamental in a wide range of mathematical
research. The philosophical problems that lie at the basis of recurrent proofs
and processes are, as I have elsewhere argued, of the most fundamental
importance.
These, then, are a few hints relating to the significance of our author's
discussion, and a few reasons for hoping that our own students will profit
by the reading of the book as those of other nations have already done.
Of the person and of the life-work of our author a few words are here, in
conclusion, still in place, addressed, not to the students of his own science,

to whom his position is well known, but to the general reader who may seek
guidance in these pages.
Jules Henri Poincaré was born at Nancy, in 1854, the son of a professor
in the Faculty of Medicine at Nancy. He studied at the École Polytechnique
and at the École des Mines, and later received his doctorate in mathematics
in 1879. In 1883 he began courses of instruction in mathematics at the
École Polytechnique; in 1886 received a professorship of mathematical
physics in the Faculty of Sciences at Paris; then became member of the
Academy of Sciences at Paris, in 1887, and devoted his life to instruction
and investigation in the regions of pure mathematics, of mathematical
physics and of celestial mechanics. His list of published treatises relating to
various branches of his chosen sciences is long; and his original memoirs
have included several momentous investigations, which have gone far to
transform more than one branch of research. His presence at the
International Congress of Arts and Science in St. Louis was one of the most
noticeable features of that remarkable gathering of distinguished foreign
guests. In Poincaré the reader meets, then, not one who is primarily a
speculative student of general problems for their own sake, but an original
investigator of the highest rank in several distinct, although interrelated,
branches of modern research. The theory of functions—a highly recondite
region of pure mathematics—owes to him advances of the first importance,
for instance, the definition of a new type of functions. The 'problem of the
three bodies,' a famous and fundamental problem of celestial mechanics,
has received from his studies a treatment whose significance has been
recognized by the highest authorities. His international reputation has been
confirmed by the conferring of more than one important prize for his
researches. His membership in the most eminent learned societies of
various nations is widely extended; his volumes bearing upon various
branches of mathematics and of mathematical physics are used by special
students in all parts of the learned world; in brief, he is, as geometer, as
analyst and as a theoretical physicist, a leader of his age.
Meanwhile, as contributor to the philosophical discussion of the bases
and methods of science, M. Poincaré has long been active. When, in 1893,
the admirable Revue de Métaphysique et de Morale began to appear, M.
Poincaré was soon found amongst the most satisfactory of the contributors
to the work of that journal, whose office it has especially been to bring

philosophy and the various special sciences (both natural and moral) into a
closer mutual understanding. The discussions brought together in the
present volume are in large part the outcome of M. Poincaré's contributions
to the Revue de Métaphysique et de Morale. The reader of M. Poincaré's
book is in presence, then, of a great special investigator who is also a
philosopher.

SCIENCE AND HYPOTHESIS
INTRODUCTION
For a superficial observer, scientific truth is beyond the possibility of
doubt; the logic of science is infallible, and if the scientists are sometimes
mistaken, this is only from their mistaking its rules.
"The mathematical verities flow from a small number of self-evident
propositions by a chain of impeccable reasonings; they impose themselves
not only on us, but on nature itself. They fetter, so to speak, the Creator and
only permit him to choose between some relatively few solutions. A few
experiments then will suffice to let us know what choice he has made. From
each experiment a crowd of consequences will follow by a series of
mathematical deductions, and thus each experiment will make known to us
a corner of the universe."
Behold what is for many people in the world, for scholars getting their
first notions of physics, the origin of scientific certitude. This is what they
suppose to be the rôle of experimentation and mathematics. This same
conception, a hundred years ago, was held by many savants who dreamed
of constructing the world with as little as possible taken from experiment.
On a little more reflection it was perceived how great a place hypothesis
occupies; that the mathematician can not do without it, still less the
experimenter. And then it was doubted if all these constructions were really
solid, and believed that a breath would overthrow them. To be skeptical in
this fashion is still to be superficial. To doubt everything and to believe
everything are two equally convenient solutions; each saves us from
thinking.
Instead of pronouncing a summary condemnation, we ought therefore to
examine with care the rôle of hypothesis; we shall then recognize, not only
that it is necessary, but that usually it is legitimate. We shall also see that
there are several sorts of hypotheses; that some are verifiable, and once
confirmed by experiment become fruitful truths; that others, powerless to

lead us astray, may be useful to us in fixing our ideas; that others, finally,
are hypotheses only in appearance and are reducible to disguised definitions
or conventions.
These last are met with above all in mathematics and the related sciences.
Thence precisely it is that these sciences get their rigor; these conventions
are the work of the free activity of our mind, which, in this domain,
recognizes no obstacle. Here our mind can affirm, since it decrees; but let
us understand that while these decrees are imposed upon our science,
which, without them, would be impossible, they are not imposed upon
nature. Are they then arbitrary? No, else were they sterile. Experiment
leaves us our freedom of choice, but it guides us by aiding us to discern the
easiest way. Our decrees are therefore like those of a prince, absolute but
wise, who consults his council of state.
Some people have been struck by this character of free convention
recognizable in certain fundamental principles of the sciences. They have
wished to generalize beyond measure, and, at the same time, they have
forgotten that liberty is not license. Thus they have reached what is called
nominalism, and have asked themselves if the savant is not the dupe of his
own definitions and if the world he thinks he discovers is not simply created
by his own caprice.[1] Under these conditions science would be certain, but
deprived of significance.
If this were so, science would be powerless. Now every day we see it
work under our very eyes. That could not be if it taught us nothing of
reality. Still, the things themselves are not what it can reach, as the naïve
dogmatists think, but only the relations between things. Outside of these
relations there is no knowable reality.
Such is the conclusion to which we shall come, but for that we must
review the series of sciences from arithmetic and geometry to mechanics
and experimental physics.
What is the nature of mathematical reasoning? Is is really deductive, as is
commonly supposed? A deeper analysis shows us that it is not, that it
partakes in a certain measure of the nature of inductive reasoning, and just
because of this is it so fruitful. None the less does it retain its character of
rigor absolute; this is the first thing that had to be shown.

Knowing better now one of the instruments which mathematics puts into
the hands of the investigator, we had to analyze another fundamental notion,
that of mathematical magnitude. Do we find it in nature, or do we ourselves
introduce it there? And, in this latter case, do we not risk marring
everything? Comparing the rough data of our senses with that extremely
complex and subtile concept which mathematicians call magnitude, we are
forced to recognize a difference; this frame into which we wish to force
everything is of our own construction; but we have not made it at random.
We have made it, so to speak, by measure and therefore we can make the
facts fit into it without changing what is essential in them.
Another frame which we impose on the world is space. Whence come the
first principles of geometry? Are they imposed on us by logic? Lobachevski
has proved not, by creating non-Euclidean geometry. Is space revealed to us
by our senses? Still no, for the space our senses could show us differs
absolutely from that of the geometer. Is experience the source of geometry?
A deeper discussion will show us it is not. We therefore conclude that the
first principles of geometry are only conventions; but these conventions are
not arbitrary and if transported into another world (that I call the non-
Euclidean world and seek to imagine), then we should have been led to
adopt others.
In mechanics we should be led to analogous conclusions, and should see
that the principles of this science, though more directly based on
experiment, still partake of the conventional character of the geometric
postulates. Thus far nominalism triumphs; but now we arrive at the physical
sciences, properly so called. Here the scene changes; we meet another sort
of hypotheses and we see their fertility. Without doubt, at first blush, the
theories seem to us fragile, and the history of science proves to us how
ephemeral they are; yet they do not entirely perish, and of each of them
something remains. It is this something we must seek to disentangle, since
there and there alone is the veritable reality.
The method of the physical sciences rests on the induction which makes
us expect the repetition of a phenomenon when the circumstances under
which it first happened are reproduced. If all these circumstances could be
reproduced at once, this principle could be applied without fear; but that
will never happen; some of these circumstances will always be lacking. Are

we absolutely sure they are unimportant? Evidently not. That may be
probable, it can not be rigorously certain. Hence the important rôle the
notion of probability plays in the physical sciences. The calculus of
probabilities is therefore not merely a recreation or a guide to players of
baccarat, and we must seek to go deeper with its foundations. Under this
head I have been able to give only very incomplete results, so strongly does
this vague instinct which lets us discern probability defy analysis.
After a study of the conditions under which the physicist works, I have
thought proper to show him at work. For that I have taken instances from
the history of optics and of electricity. We shall see whence have sprung the
ideas of Fresnel, of Maxwell, and what unconscious hypotheses were made
by Ampère and the other founders of electrodynamics.

PART I

NUMBER AND MAGNITUDE

CHAPTER I

On the Nature of Mathematical Reasoning

I
The very possibility of the science of mathematics seems an insoluble
contradiction. If this science is deductive only in appearance, whence does
it derive that perfect rigor no one dreams of doubting? If, on the contrary,
all the propositions it enunciates can be deduced one from another by the
rules of formal logic, why is not mathematics reduced to an immense
tautology? The syllogism can teach us nothing essentially new, and, if
everything is to spring from the principle of identity, everything should be
capable of being reduced to it. Shall we then admit that the enunciations of
all those theorems which fill so many volumes are nothing but devious
ways of saying A is A?
Without doubt, we can go back to the axioms, which are at the source of
all these reasonings. If we decide that these can not be reduced to the
principle of contradiction, if still less we see in them experimental facts
which could not partake of mathematical necessity, we have yet the
resource of classing them among synthetic a priori judgments. This is not to
solve the difficulty, but only to baptize it; and even if the nature of synthetic
judgments were for us no mystery, the contradiction would not have
disappeared, it would only have moved back; syllogistic reasoning remains
incapable of adding anything to the data given it: these data reduce

themselves to a few axioms, and we should find nothing else in the
conclusions.
No theorem could be new if no new axiom intervened in its
demonstration; reasoning could give us only the immediately evident
verities borrowed from direct intuition; it would be only an intermediary
parasite, and therefore should we not have good reason to ask whether the
whole syllogistic apparatus did not serve solely to disguise our borrowing?
The contradiction will strike us the more if we open any book on
mathematics; on every page the author will announce his intention of
generalizing some proposition already known. Does the mathematical
method proceed from the particular to the general, and, if so, how then can
it be called deductive?
If finally the science of number were purely analytic, or could be
analytically derived from a small number of synthetic judgments, it seems
that a mind sufficiently powerful could at a glance perceive all its truths;
nay more, we might even hope that some day one would invent to express
them a language sufficiently simple to have them appear self-evident to an
ordinary intelligence.
If we refuse to admit these consequences, it must be conceded that
mathematical reasoning has of itself a sort of creative virtue and
consequently differs from the syllogism.
The difference must even be profound. We shall not, for example, find
the key to the mystery in the frequent use of that rule according to which
one and the same uniform operation applied to two equal numbers will give
identical results.
All these modes of reasoning, whether or not they be reducible to the
syllogism properly so called, retain the analytic character, and just because
of that are powerless.

II
The discussion is old; Leibnitz tried to prove 2 and 2 make 4; let us look
a moment at his demonstration.

I will suppose the number 1 defined and also the operation x + 1 which
consists in adding unity to a given number x.
These definitions, whatever they be, do not enter into the course of the
reasoning.
I define then the numbers 2, 3 and 4 by the equalities
(1) 1 + 1 = 2; (2) 2 + 1 = 3; (3) 3 + 1 = 4.
In the same way, I define the operation x + 2 by the relation:
(4) x + 2 = (x + 1) + 1.
That presupposed, we have

2+1+1=3+1 (Definition 2),
3+1=4 (Definition 3),
2 + 2 = (2 + 1) + 1 (Definition 4),
whence
2 + 2 = 4 Q.E.D.
It can not be denied that this reasoning is purely analytic. But ask any
mathematician: 'That is not a demonstration properly so called,' he will say
to you: 'that is a verification.' We have confined ourselves to comparing two
purely conventional definitions and have ascertained their identity; we have
learned nothing new. Verification differs from true demonstration precisely
because it is purely analytic and because it is sterile. It is sterile because the
conclusion is nothing but the premises translated into another language. On
the contrary, true demonstration is fruitful because the conclusion here is in
a sense more general than the premises.
The equality 2 + 2 = 4 is thus susceptible of a verification only because it
is particular. Every particular enunciation in mathematics can always be
verified in this same way. But if mathematics could be reduced to a series of
such verifications, it would not be a science. So a chess-player, for example,
does not create a science in winning a game. There is no science apart from
the general.

It may even be said the very object of the exact sciences is to spare us
these direct verifications.

III
Let us, therefore, see the geometer at work and seek to catch his process.
The task is not without difficulty; it does not suffice to open a work at
random and analyze any demonstration in it.
We must first exclude geometry, where the question is complicated by
arduous problems relative to the rôle of the postulates, to the nature and the
origin of the notion of space. For analogous reasons we can not turn to the
infinitesimal analysis. We must seek mathematical thought where it has
remained pure, that is, in arithmetic.
A choice still is necessary; in the higher parts of the theory of numbers,
the primitive mathematical notions have already undergone an elaboration
so profound that it becomes difficult to analyze them.
It is, therefore, at the beginning of arithmetic that we must expect to find
the explanation we seek, but it happens that precisely in the demonstration
of the most elementary theorems the authors of the classic treatises have
shown the least precision and rigor. We must not impute this to them as a
crime; they have yielded to a necessity; beginners are not prepared for real
mathematical rigor; they would see in it only useless and irksome subtleties;
it would be a waste of time to try prematurely to make them more exacting;
they must pass over rapidly, but without skipping stations, the road
traversed slowly by the founders of the science.
Why is so long a preparation necessary to become habituated to this
perfect rigor, which, it would seem, should naturally impress itself upon all
good minds? This is a logical and psychological problem well worthy of
study.
But we shall not take it up; it is foreign to our purpose; all I wish to insist
on is that, not to fail of our purpose, we must recast the demonstrations of
the most elementary theorems and give them, not the crude form in which

they are left, so as not to harass beginners, but the form that will satisfy a
skilled geometer.
Definition of Addition.—I suppose already defined the operation x + 1,
which consists in adding the number 1 to a given number x.
This definition, whatever it be, does not enter into our subsequent
reasoning.
We now have to define the operation x + a, which consists in adding the
number a to a given number x.
Supposing we have defined the operation
x + (a − 1),
the operation x + a will be defined by the equality
(1) x + a = [x + (a − 1)] + 1.
We shall know then what x + a is when we know what x + (a − 1) is, and
as I have supposed that to start with we knew what x + 1 is, we can define
successively and 'by recurrence' the operations x + 2, x + 3, etc.
This definition deserves a moment's attention; it is of a particular nature
which already distinguishes it from the purely logical definition; the
equality (1) contains an infinity of distinct definitions, each having a
meaning only when one knows the preceding.
Properties of Addition.—Associativity.—I say that
a + (b + c) = (a + b) + c.
In fact the theorem is true for c = 1; it is then written
a + (b + 1) = (a + b) + 1,
which, apart from the difference of notation, is nothing but the equality (1),
by which I have just defined addition.
Supposing the theorem true for c = γ, I say it will be true for c = γ + 1.
In fact, supposing

(a + b) + γ = a + (b + γ),
it follows that
[(a + b) + γ] + 1 = [a + (b + γ)] + 1
or by definition (1)
(a + b) + (γ + 1) = a + (b + γ + 1) = a + [b + (γ + 1)],
which shows, by a series of purely analytic deductions, that the theorem is
true for γ + 1.
Being true for c = 1, we thus see successively that so it is for c = 2, for c
= 3, etc.
Commutativity.—1º I say that
a + 1 = 1 + a.
The theorem is evidently true for a = 1; we can verify by purely analytic
reasoning that if it is true for a = γ it will be true for a = γ + 1; for then
(γ + 1) + 1 = (1 + γ) + 1 = 1 + (γ + 1);
now it is true for a = 1, therefore it will be true for a = 2, for a = 3, etc.,
which is expressed by saying that the enunciated proposition is
demonstrated by recurrence.
2º I say that
a + b = b + a.
The theorem has just been demonstrated for b = 1; it can be verified
analytically that if it is true for b = β, it will be true for b = β + 1.
The proposition is therefore established by recurrence.
Definition of Multiplication.—We shall define multiplication by the
equalities.
(1) a × 1 = a.

(2) a × b = [a × (b − 1)] + a.
Like equality (1), equality (2) contains an infinity of definitions; having
defined a × 1, it enables us to define successively: a × 2, a × 3, etc.
Properties of Multiplication.—Distributivity.—I say that
(a + b) × c = (a × c) + (b × c).
We verify analytically that the equality is true for c = 1; then that if the
theorem is true for c = γ, it will be true for c = γ + 1.
The proposition is, therefore, demonstrated by recurrence.
Commutativity.—1º I say that
a × 1 = 1 × a.
The theorem is evident for a = 1.
We verify analytically that if it is true for a = α, it will be true for a = α +
1.
2º I say that
a × b = b × a.
The theorem has just been proven for b = 1. We could verify analytically
that if it is true for b = β, it will be true for b = β + 1.

IV
Here I stop this monotonous series of reasonings. But this very monotony
has the better brought out the procedure which is uniform and is met again
at each step.
This procedure is the demonstration by recurrence. We first establish a
theorem for n = 1; then we show that if it is true of n − 1, it is true of n, and
thence conclude that it is true for all the whole numbers.
We have just seen how it may be used to demonstrate the rules of
addition and multiplication, that is to say, the rules of the algebraic calculus;

this calculus is an instrument of transformation, which lends itself to many
more differing combinations than does the simple syllogism; but it is still an
instrument purely analytic, and incapable of teaching us anything new. If
mathematics had no other instrument, it would therefore be forthwith
arrested in its development; but it has recourse anew to the same procedure,
that is, to reasoning by recurrence, and it is able to continue its forward
march.
If we look closely, at every step we meet again this mode of reasoning,
either in the simple form we have just given it, or under a form more or less
modified.
Here then we have the mathematical reasoning par excellence, and we
must examine it more closely.

V
The essential characteristic of reasoning by recurrence is that it contains,
condensed, so to speak, in a single formula, an infinity of syllogisms.
That this may the better be seen, I will state one after another these
syllogisms which are, if you will allow me the expression, arranged in
'cascade.'
These are of course hypothetical syllogisms.
The theorem is true of the number 1.
Now, if it is true of 1, it is true of 2.
Therefore it is true of 2.
Now, if it is true of 2, it is true of 3.
Therefore it is true of 3, and so on.
We see that the conclusion of each syllogism serves as minor to the
following.
Furthermore the majors of all our syllogisms can be reduced to a single
formula.

If the theorem is true of n − 1, so it is of n.
We see, then, that in reasoning by recurrence we confine ourselves to
stating the minor of the first syllogism, and the general formula which
contains as particular cases all the majors.
This never-ending series of syllogisms is thus reduced to a phrase of a
few lines.
It is now easy to comprehend why every particular consequence of a
theorem can, as I have explained above, be verified by purely analytic
procedures.
If instead of showing that our theorem is true of all numbers, we only
wish to show it true of the number 6, for example, it will suffice for us to
establish the first 5 syllogisms of our cascade; 9 would be necessary if we
wished to prove the theorem for the number 10; more would be needed for
a larger number; but, however great this number might be, we should
always end by reaching it, and the analytic verification would be possible.
And yet, however far we thus might go, we could never rise to the
general theorem, applicable to all numbers, which alone can be the object of
science. To reach this, an infinity of syllogisms would be necessary; it
would be necessary to overleap an abyss that the patience of the analyst,
restricted to the resources of formal logic alone, never could fill up.
I asked at the outset why one could not conceive of a mind sufficiently
powerful to perceive at a glance the whole body of mathematical truths.
The answer is now easy; a chess-player is able to combine four moves,
five moves, in advance, but, however extraordinary he may be, he will
never prepare more than a finite number of them; if he applies his faculties
to arithmetic, he will not be able to perceive its general truths by a single
direct intuition; to arrive at the smallest theorem he can not dispense with
the aid of reasoning by recurrence, for this is an instrument which enables
us to pass from the finite to the infinite.
This instrument is always useful, for, allowing us to overleap at a bound
as many stages as we wish, it spares us verifications, long, irksome and
monotonous, which would quickly become impracticable. But it becomes

indispensable as soon as we aim at the general theorem, to which analytic
verification would bring us continually nearer without ever enabling us to
reach it.
In this domain of arithmetic, we may think ourselves very far from the
infinitesimal analysis, and yet, as we have just seen, the idea of the
mathematical infinite already plays a preponderant rôle, and without it there
would be no science, because there would be nothing general.

VI
The judgment on which reasoning by recurrence rests can be put under
other forms; we may say, for example, that in an infinite collection of
different whole numbers there is always one which is less than all the
others.
We can easily pass from one enunciation to the other and thus get the
illusion of having demonstrated the legitimacy of reasoning by recurrence.
But we shall always be arrested, we shall always arrive at an
undemonstrable axiom which will be in reality only the proposition to be
proved translated into another language.
We can not therefore escape the conclusion that the rule of reasoning by
recurrence is irreducible to the principle of contradiction.
Neither can this rule come to us from experience; experience could teach
us that the rule is true for the first ten or hundred numbers; for example, it
can not attain to the indefinite series of numbers, but only to a portion of
this series, more or less long but always limited.
Now if it were only a question of that, the principle of contradiction
would suffice; it would always allow of our developing as many syllogisms
as we wished; it is only when it is a question of including an infinity of
them in a single formula, it is only before the infinite that this principle
fails, and there too, experience becomes powerless. This rule, inaccessible
to analytic demonstration and to experience, is the veritable type of the
synthetic a priori judgment. On the other hand, we can not think of seeing
in it a convention, as in some of the postulates of geometry.

Why then does this judgment force itself upon us with an irresistible
evidence? It is because it is only the affirmation of the power of the mind
which knows itself capable of conceiving the indefinite repetition of the
same act when once this act is possible. The mind has a direct intuition of
this power, and experience can only give occasion for using it and thereby
becoming conscious of it.
But, one will say, if raw experience can not legitimatize reasoning by
recurrence, is it so of experiment aided by induction? We see successively
that a theorem is true of the number 1, of the number 2, of the number 3 and
so on; the law is evident, we say, and it has the same warranty as every
physical law based on observations, whose number is very great but limited.
Here is, it must be admitted, a striking analogy with the usual procedures
of induction. But there is an essential difference. Induction applied to the
physical sciences is always uncertain, because it rests on the belief in a
general order of the universe, an order outside of us. Mathematical
induction, that is, demonstration by recurrence, on the contrary, imposes
itself necessarily because it is only the affirmation of a property of the mind
itself.

VII
Mathematicians, as I have said before, always endeavor to generalize the
propositions they have obtained, and, to seek no other example, we have
just proved the equality:
a+1=1+a
and afterwards used it to establish the equality
a+b=b+a
which is manifestly more general.
Mathematics can, therefore, like the other sciences, proceed from the
particular to the general.
This is a fact which would have appeared incomprehensible to us at the
outset of this study, but which is no longer mysterious to us, since we have

ascertained the analogies between demonstration by recurrence and
ordinary induction.
Without doubt recurrent reasoning in mathematics and inductive
reasoning in physics rest on different foundations, but their march is
parallel, they advance in the same sense, that is to say, from the particular to
the general.
Let us examine the case a little more closely.
To demonstrate the equality
a+2=2+a
it suffices to twice apply the rule
(1) a + 1 = 1 + a
and write
(2) a + 2 = a + 1 + 1 = 1 + a + 1 = 1 + 1 + a = 2 + a.
The equality (2) thus deduced in purely analytic way from the equality
(1) is, however, not simply a particular ease of it; it is something quite
different.
We can not therefore even say that in the really analytic and deductive
part of mathematical reasoning we proceed from the general to the
particular in the ordinary sense of the word.
The two members of the equality (2) are simply combinations more
complicated than the two members of the equality (1), and analysis only
serves to separate the elements which enter into these combinations and to
study their relations.
Mathematicians proceed therefore 'by construction,' they 'construct'
combinations more and more complicated. Coming back then by the
analysis of these combinations, of these aggregates, so to speak, to their
primitive elements, they perceive the relations of these elements and from
them deduce the relations of the aggregates themselves.

This is a purely analytical proceeding, but it is not, however, a
proceeding from the general to the particular, because evidently the
aggregates can not be regarded as more particular than their elements.
Great importance, and justly, has been attached to this procedure of
'construction,' and some have tried to see in it the necessary and sufficient
condition for the progress of the exact sciences.
Necessary, without doubt; but sufficient, no.
For a construction to be useful and not a vain toil for the mind, that it
may serve as stepping-stone to one wishing to mount, it must first of all
possess a sort of unity enabling us to see in it something besides the
juxtaposition of its elements.
Or, more exactly, there must be some advantage in considering the
construction rather than its elements themselves.
What can this advantage be?
Why reason on a polygon, for instance, which is always decomposable
into triangles, and not on the elementary triangles?
It is because there are properties appertaining to polygons of any number
of sides and that may be immediately applied to any particular polygon.
Usually, on the contrary, it is only at the cost of the most prolonged
exertions that they could be found by studying directly the relations of the
elementary triangles. The knowledge of the general theorem spares us these
efforts.
A construction, therefore, becomes interesting only when it can be ranged
beside other analogous constructions, forming species of the same genus.
If the quadrilateral is something besides the juxtaposition of two
triangles, this is because it belongs to the genus polygon.
Moreover, one must be able to demonstrate the properties of the genus
without being forced to establish them successively for each of the species.

To attain that, we must necessarily mount from the particular to the
general, ascending one or more steps.
The analytic procedure 'by construction' does not oblige us to descend,
but it leaves us at the same level.
We can ascend only by mathematical induction, which alone can teach us
something new. Without the aid of this induction, different in certain
respects from physical induction, but quite as fertile, construction would be
powerless to create science.
Observe finally that this induction is possible only if the same operation
can be repeated indefinitely. That is why the theory of chess can never
become a science, for the different moves of the same game do not
resemble one another.

CHAPTER II

Mathematical Magnitude and Experience
To learn what mathematicians understand by a continuum, one should not
inquire of geometry. The geometer always seeks to represent to himself
more or less the figures he studies, but his representations are for him only
instruments; in making geometry he uses space just as he does chalk; so too
much weight should not be attached to non-essentials, often of no more
importance than the whiteness of the chalk.
The pure analyst has not this rock to fear. He has disengaged the science
of mathematics from all foreign elements, and can answer our question:
'What exactly is this continuum about which mathematicians reason?' Many
analysts who reflect on their art have answered already; Monsieur Tannery,
for example, in his Introduction à la théorie des fonctions d'une variable.
Let us start from the scale of whole numbers; between two consecutive
steps, intercalate one or more intermediary steps, then between these new
steps still others, and so on indefinitely. Thus we shall have an unlimited

number of terms; these will be the numbers called fractional, rational or
commensurable. But this is not yet enough; between these terms, which,
however, are already infinite in number, it is still necessary to intercalate
others called irrational or incommensurable. A remark before going further.
The continuum so conceived is only a collection of individuals ranged in a
certain order, infinite in number, it is true, but exterior to one another. This
is not the ordinary conception, wherein is supposed between the elements of
the continuum a sort of intimate bond which makes of them a whole, where
the point does not exist before the line, but the line before the point. Of the
celebrated formula, 'the continuum is unity in multiplicity,' only the
multiplicity remains, the unity has disappeared. The analysts are none the
less right in defining their continuum as they do, for they always reason on
just this as soon as they pique themselves on their rigor. But this is enough
to apprise us that the veritable mathematical continuum is a very different
thing from that of the physicists and that of the metaphysicians.
It may also be said perhaps that the mathematicians who are content with
this definition are dupes of words, that it is necessary to say precisely what
each of these intermediary steps is, to explain how they are to be
intercalated and to demonstrate that it is possible to do it. But that would be
wrong; the only property of these steps which is used in their reasonings[2]
is that of being before or after such and such steps; therefore also this alone
should occur in the definition.
So how the intermediary terms should be intercalated need not concern
us; on the other hand, no one will doubt the possibility of this operation,
unless from forgetting that possible, in the language of geometers, simply
means free from contradiction.
Our definition, however, is not yet complete, and I return to it after this
over-long digression.
Definition of Incommensurables.—The mathematicians of the Berlin
school, Kronecker in particular, have devoted themselves to constructing
this continuous scale of fractional and irrational numbers without using any
material other than the whole number. The mathematical continuum would
be, in this view, a pure creation of the mind, where experience would have
no part.

The notion of the rational number seeming to them to present no
difficulty, they have chiefly striven to define the incommensurable number.
But before producing here their definition, I must make a remark to forestall
the astonishment it is sure to arouse in readers unfamiliar with the customs
of geometers.
Mathematicians study not objects, but relations between objects; the
replacement of these objects by others is therefore indifferent to them,
provided the relations do not change. The matter is for them unimportant,
the form alone interests them.
Without recalling this, it would scarcely be comprehensible that
Dedekind should designate by the name incommensurable number a mere
symbol, that is to say, something very different from the ordinary idea of a
quantity, which should be measurable and almost tangible.
Let us see now what Dedekind's definition is:
The commensurable numbers can in an infinity of ways be partitioned
into two classes, such that any number of the first class is greater than any
number of the second class.
It may happen that among the numbers of the first class there is one
smaller than all the others; if, for example, we range in the first class all
numbers greater than 2, and 2 itself, and in the second class all numbers less
than 2, it is clear that 2 will be the least of all numbers of the first class. The
number 2 may be chosen as symbol of this partition.
It may happen, on the contrary, that among the numbers of the second
class is one greater than all the others; this is the case, for example, if the
first class comprehends all numbers greater than 2, and the second all
numbers less than 2, and 2 itself. Here again the number 2 may be chosen as
symbol of this partition.
But it may equally well happen that neither is there in the first class a
number less than all the others, nor in the second class a number greater
than all the others. Suppose, for example, we put in the first class all
commensurable numbers whose squares are greater than 2 and in the second
all whose squares are less than 2. There is none whose square is precisely 2.
Evidently there is not in the first class a number less than all the others, for,

however near the square of a number may be to 2, we can always find a
commensurable number whose square is still closer to 2.
In Dedekind's view, the incommensurable number

√2 or (2)½
is nothing but the symbol of this particular mode of partition of
commensurable numbers; and to each mode of partition corresponds thus a
number, commensurable or not, which serves as its symbol.
But to be content with this would be to forget too far the origin of these
symbols; it remains to explain how we have been led to attribute to them a
sort of concrete existence, and, besides, does not the difficulty begin even
for the fractional numbers themselves? Should we have the notion of these
numbers if we had not previously known a matter that we conceive as
infinitely divisible, that is to say, a continuum?
The Physical Continuum.—We ask ourselves then if the notion of the
mathematical continuum is not simply drawn from experience. If it were,
the raw data of experience, which are our sensations, would be susceptible
of measurement. We might be tempted to believe they really are so, since in
these latter days the attempt has been made to measure them and a law has
even been formulated, known as Fechner's law, according to which
sensation is proportional to the logarithm of the stimulus.
But if we examine more closely the experiments by which it has been
sought to establish this law, we shall be led to a diametrically opposite
conclusion. It has been observed, for example, that a weight A of 10 grams
and a weight B of 11 grams produce identical sensations, that the weight B
is just as indistinguishable from a weight C of 12 grams, but that the weight
A is easily distinguished from the weight C. Thus the raw results of
experience may be expressed by the following relations:
A = B, B = C, A < C,
which may be regarded as the formula of the physical continuum.
But here is an intolerable discord with the principle of contradiction, and
the need of stopping this has compelled us to invent the mathematical

continuum.
We are, therefore, forced to conclude that this notion has been created
entirely by the mind, but that experience has given the occasion.
We can not believe that two quantities equal to a third are not equal to
one another, and so we are led to suppose that A is different from B and B
from C, but that the imperfection of our senses has not permitted of our
distinguishing them.
Creation of the Mathematical Continuum.—First Stage. So far it would
suffice, in accounting for the facts, to intercalate between A and B a few
terms, which would remain discrete. What happens now if we have recourse
to some instrument to supplement the feebleness of our senses, if, for
example, we make use of a microscope? Terms such as A and B, before
indistinguishable, appear now distinct; but between A and B, now become
distinct, will be intercalated a new term, D, that we can distinguish neither
from A nor from B. Despite the employment of the most highly perfected
methods, the raw results of our experience will always present the
characteristics of the physical continuum with the contradiction which is
inherent in it.
We shall escape it only by incessantly intercalating new terms between
the terms already distinguished, and this operation must be continued
indefinitely. We might conceive the stopping of this operation if we could
imagine some instrument sufficiently powerful to decompose the physical
continuum into discrete elements, as the telescope resolves the milky way
into stars. But this we can not imagine; in fact, it is with the eye we observe
the image magnified by the microscope, and consequently this image must
always retain the characteristics of visual sensation and consequently those
of the physical continuum.
Nothing distinguishes a length observed directly from the half of this
length doubled by the microscope. The whole is homogeneous with the
part; this is a new contradiction, or rather it would be if the number of terms
were supposed finite; in fact, it is clear that the part containing fewer terms
than the whole could not be similar to the whole.

The contradiction ceases when the number of terms is regarded as
infinite; nothing hinders, for example, considering the aggregate of whole
numbers as similar to the aggregate of even numbers, which, however, is
only a part of it; and, in fact, to each whole number corresponds an even
number, its double.
But it is not only to escape this contradiction contained in the empirical
data that the mind is led to create the concept of a continuum, formed of an
indefinite number of terms.
All happens as in the sequence of whole numbers. We have the faculty of
conceiving that a unit can be added to a collection of units; thanks to
experience, we have occasion to exercise this faculty and we become
conscious of it; but from this moment we feel that our power has no limit
and that we can count indefinitely, though we have never had to count more
than a finite number of objects.
Just so, as soon as we have been led to intercalate means between two
consecutive terms of a series, we feel that this operation can be continued
beyond all limit, and that there is, so to speak, no intrinsic reason for
stopping.
As an abbreviation, let me call a mathematical continuum of the first
order every aggregate of terms formed according to the same law as the
scale of commensurable numbers. If we afterwards intercalate new steps
according to the law of formation of incommensurable numbers, we shall
obtain what we will call a continuum of the second order.
Second Stage.—We have made hitherto only the first stride; we have
explained the origin of continua of the first order; but it is necessary to see
why even they are not sufficient and why the incommensurable numbers
had to be invented.
If we try to imagine a line, it must have the characteristics of the physical
continuum, that is to say, we shall not be able to represent it except with a
certain breadth. Two lines then will appear to us under the form of two
narrow bands, and, if we are content with this rough image, it is evident that
if the two lines cross they will have a common part.

But the pure geometer makes a further effort; without entirely renouncing
the aid of the senses, he tries to reach the concept of the line without
breadth, of the point without extension. This he can only attain to by
regarding the line as the limit toward which tends an ever narrowing band,
and the point as the limit toward which tends an ever lessening area. And
then, our two bands, however narrow they may be, will always have a
common area, the smaller as they are the narrower, and whose limit will be
what the pure geometer calls a point.
This is why it is said two lines which cross have a point in common, and
this truth seems intuitive.
But it would imply contradiction if lines were conceived as continua of
the first order, that is to say, if on the lines traced by the geometer should be
found only points having for coordinates rational numbers. The
contradiction would be manifest as soon as one affirmed, for example, the
existence of straights and circles.
It is clear, in fact, that if the points whose coordinates are commensurable
were alone regarded as real, the circle inscribed in a square and the diagonal
of this square would not intersect, since the coordinates of the point of
intersection are incommensurable.
That would not yet be sufficient, because we should get in this way only
certain incommensurable numbers and not all those numbers.
But conceive of a straight line divided into two rays. Each of these rays
will appear to our imagination as a band of a certain breadth; these bands
moreover will encroach one on the other, since there must be no interval
between them. The common part will appear to us as a point which will
always remain when we try to imagine our bands narrower and narrower, so
that we admit as an intuitive truth that if a straight is cut into two rays their
common frontier is a point; we recognize here the conception of Dedekind,
in which an incommensurable number was regarded as the common frontier
of two classes of rational numbers.
Such is the origin of the continuum of the second order, which is the
mathematical continuum properly so called.

Résumé.—In recapitulation, the mind has the faculty of creating symbols,
and it is thus that it has constructed the mathematical continuum, which is
only a particular system of symbols. Its power is limited only by the
necessity of avoiding all contradiction; but the mind only makes use of this
faculty if experience furnishes it a stimulus thereto.
In the case considered, this stimulus was the notion of the physical
continuum, drawn from the rough data of the senses. But this notion leads
to a series of contradictions from which it is necessary successively to free
ourselves. So we are forced to imagine a more and more complicated
system of symbols. That at which we stop is not only exempt from internal
contradiction (it was so already at all the stages we have traversed), but
neither is it in contradiction with various propositions called intuitive,
which are derived from empirical notions more or less elaborated.
Measurable Magnitude.—The magnitudes we have studied hitherto are
not measurable; we can indeed say whether a given one of these
magnitudes is greater than another, but not whether it is twice or thrice as
great.
So far, I have only considered the order in which our terms are ranged.
But for most applications that does not suffice. We must learn to compare
the interval which separates any two terms. Only on this condition does the
continuum become a measurable magnitude and the operations of
arithmetic applicable.
This can only be done by the aid of a new and special convention. We
will agree that in such and such a case the interval comprised between the
terms A and B is equal to the interval which separates C and D. For
example, at the beginning of our work we have set out from the scale of the
whole numbers and we have supposed intercalated between two
consecutive steps n intermediary steps; well, these new steps will be by
convention regarded as equidistant.
This is a way of defining the addition of two magnitudes, because if the
interval AB is by definition equal to the interval CD, the interval AD will be
by definition the sum of the intervals AB and AC.

This definition is arbitrary in a very large measure. It is not completely
so, however. It is subjected to certain conditions and, for example, to the
rules of commutativity and associativity of addition. But provided the
definition chosen satisfies these rules, the choice is indifferent, and it is
useless to particularize it.
Various Remarks.—We can now discuss several important questions:
1º Is the creative power of the mind exhausted by the creation of the
mathematical continuum?
No: the works of Du Bois-Reymond demonstrate it in a striking way.
We know that mathematicians distinguish between infinitesimals of
different orders and that those of the second order are infinitesimal, not only
in an absolute way, but also in relation to those of the first order. It is not
difficult to imagine infinitesimals of fractional or even of irrational order,
and thus we find again that scale of the mathematical continuum which has
been dealt with in the preceding pages.
Further, there are infinitesimals which are infinitely small in relation to
those of the first order, and, on the contrary, infinitely great in relation to
those of order 1 + ε, and that however small ε may be. Here, then, are new
terms intercalated in our series, and if I may be permitted to revert to the
phraseology lately employed which is very convenient though not
consecrated by usage, I shall say that thus has been created a sort of
continuum of the third order.
It would be easy to go further, but that would be idle; one would only be
imagining symbols without possible application, and no one will think of
doing that. The continuum of the third order, to which the consideration of
the different orders of infinitesimals leads, is itself not useful enough to
have won citizenship, and geometers regard it only as a mere curiosity. The
mind uses its creative faculty only when experience requires it.
2º Once in possession of the concept of the mathematical continuum, is
one safe from contradictions analogous to those which gave birth to it?
No, and I will give an example.

One must be very wise not to regard it as evident that every curve has a
tangent; and in fact if we picture this curve and a straight as two narrow
bands we can always so dispose them that they have a part in common
without crossing. If we imagine then the breadth of these two bands to
diminish indefinitely, this common part will always subsist and, at the limit,
so to speak, the two lines will have a point in common without crossing,
that is to say, they will be tangent.
The geometer who reasons in this way, consciously or not, is only doing
what we have done above to prove two lines which cut have a point in
common, and his intuition might seem just as legitimate.
It would deceive him however. We can demonstrate that there are curves
which have no tangent, if such a curve is defined as an analytic continuum
of the second order.
Without doubt some artifice analogous to those we have discussed above
would have sufficed to remove the contradiction; but, as this is met with
only in very exceptional cases, it has received no further attention.
Instead of seeking to reconcile intuition with analysis, we have been
content to sacrifice one of the two, and as analysis must remain impeccable,
we have decided against intuition.
The Physical Continuum of Several Dimensions.—We have discussed
above the physical continuum as derived from the immediate data of our
senses, or, if you wish, from the rough results of Fechner's experiments; I
have shown that these results are summed up in the contradictory formulas
A = B, B = C, A < C.
Let us now see how this notion has been generalized and how from it has
come the concept of many-dimensional continua.
Consider any two aggregates of sensations. Either we can discriminate
them one from another, or we can not, just as in Fechner's experiments a
weight of 10 grams can be distinguished from a weight of 12 grams, but not
from a weight of 11 grams. This is all that is required to construct the
continuum of several dimensions.

Let us call one of these aggregates of sensations an element. That will be
something analogous to the point of the mathematicians; it will not be
altogether the same thing however. We can not say our element is without
extension, since we can not distinguish it from neighboring elements and it
is thus surrounded by a sort of haze. If the astronomical comparison may be
allowed, our 'elements' would be like nebulae, whereas the mathematical
points would be like stars.
That being granted, a system of elements will form a continuum if we can
pass from any one of them to any other, by a series of consecutive elements
such that each is indistinguishable from the preceding. This linear series is
to the line of the mathematician what an isolated element was to the point.
Before going farther, I must explain what is meant by a cut. Consider a
continuum C and remove from it certain of its elements which for an instant
we shall regard as no longer belonging to this continuum. The aggregate of
the elements so removed will be called a cut. It may happen that, thanks to
this cut, C may be subdivided into several distinct continua, the aggregate
of the remaining elements ceasing to form a unique continuum.
There will then be on C two elements, A and B, that must be regarded as
belonging to two distinct continua, and this will be recognized because it
will be impossible to find a linear series of consecutive elements of C, each
of these elements indistinguishable from the preceding, the first being A and
the last B, without one of the elements of this series being indistinguishable
from one of the elements of the cut.
On the contrary, it may happen that the cut made is insufficient to
subdivide the continuum C. To classify the physical continua, we will
examine precisely what are the cuts which must be made to subdivide them.
If a physical continuum C can be subdivided by a cut reducing to a finite
number of elements all distinguishable from one another (and consequently
forming neither a continuum, nor several continua), we shall say C is a one-
dimensional continuum.
If, on the contrary, C can be subdivided only by cuts which are
themselves continua, we shall say C has several dimensions. If cuts which
are continua of one dimension suffice, we shall say C has two dimensions;

if cuts of two dimensions suffice, we shall say C has three dimensions, and
so on.
Thus is defined the notion of the physical continuum of several
dimensions, thanks to this very simple fact that two aggregates of
sensations are distinguishable or indistinguishable.
The Mathematical Continuum of Several Dimensions.—Thence the
notion of the mathematical continuum of n dimensions has sprung quite
naturally by a process very like that we discussed at the beginning of this
chapter. A point of such a continuum, you know, appears to us as defined by
a system of n distinct magnitudes called its coordinates.
These magnitudes need not always be measurable; there is, for instance, a
branch of geometry independent of the measurement of these magnitudes,
in which it is only a question of knowing, for example, whether on a curve
ABC, the point B is between the points A and C, and not of knowing
whether the arc AB is equal to the arc BC or twice as great. This is what is
called Analysis Situs.
This is a whole body of doctrine which has attracted the attention of the
greatest geometers and where we see flow one from another a series of
remarkable theorems. What distinguishes these theorems from those of
ordinary geometry is that they are purely qualitative and that they would
remain true if the figures were copied by a draughtsman so awkward as to
grossly distort the proportions and replace straights by strokes more or less
curved.
Through the wish to introduce measure next into the continuum just
defined this continuum becomes space, and geometry is born. But the
discussion of this is reserved for Part Second.

PART II

SPACE

CHAPTER III

The Non-euclidean Geometries
Every conclusion supposes premises; these premises themselves either
are self-evident and need no demonstration, or can be established only by
relying upon other propositions, and since we can not go back thus to
infinity, every deductive science, and in particular geometry, must rest on a
certain number of undemonstrable axioms. All treatises on geometry begin,
therefore, by the enunciation of these axioms. But among these there is a
distinction to be made: Some, for example, 'Things which are equal to the
same thing are equal to one another,' are not propositions of geometry, but
propositions of analysis. I regard them as analytic judgments a priori, and
shall not concern myself with them.
But I must lay stress upon other axioms which are peculiar to geometry.
Most treatises enunciate three of these explicitly:
1º Through two points can pass only one straight;
2º The straight line is the shortest path from one point to another;
3º Through a given point there is not more than one parallel to a given
straight.
Although generally a proof of the second of these axioms is omitted, it
would be possible to deduce it from the other two and from those, much

more numerous, which are implicitly admitted without enunciating them, as
I shall explain further on.
It was long sought in vain to demonstrate likewise the third axiom,
known as Euclid's Postulate. What vast effort has been wasted in this
chimeric hope is truly unimaginable. Finally, in the first quarter of the
nineteenth century, and almost at the same time, a Hungarian and a Russian,
Bolyai and Lobachevski, established irrefutably that this demonstration is
impossible; they have almost rid us of inventors of geometries 'sans
postulatum'; since then the Académie des Sciences receives only about one
or two new demonstrations a year.
The question was not exhausted; it soon made a great stride by the
publication of Riemann's celebrated memoir entitled: Ueber die Hypothesen
welche der Geometrie zu Grunde liegen. This paper has inspired most of the
recent works of which I shall speak further on, and among which it is
proper to cite those of Beltrami and of Helmholtz.
The Bolyai-Lobachevski Geometry.—If it were possible to deduce
Euclid's postulate from the other axioms, it is evident that in denying the
postulate and admitting the other axioms, we should be led to contradictory
consequences; it would therefore be impossible to base on such premises a
coherent geometry.
Now this is precisely what Lobachevski did.
He assumes at the start that: Through a given point can be drawn two
parallels to a given straight.
And he retains besides all Euclid's other axioms. From these hypotheses
he deduces a series of theorems among which it is impossible to find any
contradiction, and he constructs a geometry whose faultless logic is inferior
in nothing to that of the Euclidean geometry.
The theorems are, of course, very different from those to which we are
accustomed, and they can not fail to be at first a little disconcerting.
Thus the sum of the angles of a triangle is always less than two right
angles, and the difference between this sum and two right angles is
proportional to the surface of the triangle.

It is impossible to construct a figure similar to a given figure but of
different dimensions.
If we divide a circumference into n equal parts, and draw tangents at the
points of division, these n tangents will form a polygon if the radius of the
circle is small enough; but if this radius is sufficiently great they will not
meet.
It is useless to multiply these examples; Lobachevski's propositions have
no relation to those of Euclid, but they are not less logically bound one to
another.
Riemann's Geometry.—Imagine a world uniquely peopled by beings of
no thickness (height); and suppose these 'infinitely flat' animals are all in
the same plane and can not get out. Admit besides that this world is
sufficiently far from others to be free from their influence. While we are
making hypotheses, it costs us no more to endow these beings with reason
and believe them capable of creating a geometry. In that case, they will
certainly attribute to space only two dimensions.
But suppose now that these imaginary animals, while remaining without
thickness, have the form of a spherical, and not of a plane, figure, and are
all on the same sphere without power to get off. What geometry will they
construct? First it is clear they will attribute to space only two dimensions;
what will play for them the rôle of the straight line will be the shortest path
from one point to another on the sphere, that is to say, an arc of a great
circle; in a word, their geometry will be the spherical geometry.
What they will call space will be this sphere on which they must stay, and
on which happen all the phenomena they can know. Their space will
therefore be unbounded since on a sphere one can always go forward
without ever being stopped, and yet it will be finite; one can never find the
end of it, but one can make a tour of it.
Well, Riemann's geometry is spherical geometry extended to three
dimensions. To construct it, the German mathematician had to throw
overboard, not only Euclid's postulate, but also the first axiom: Only one
straight can pass through two points.

On a sphere, through two given points we can draw in general only one
great circle (which, as we have just seen, would play the rôle of the straight
for our imaginary beings); but there is an exception: if the two given points
are diametrically opposite, an infinity of great circles can be drawn through
them.
In the same way, in Riemann's geometry (at least in one of its forms),
through two points will pass in general only a single straight; but there are
exceptional cases where through two points an infinity of straights can pass.
There is a sort of opposition between Riemann's geometry and that of
Lobachevski.
Thus the sum of the angles of a triangle is:
Equal to two right angles in Euclid's geometry;
Less than two right angles in that of Lobachevski;
Greater than two right angles in that of Riemann.
The number of straights through a given point that can be drawn coplanar
to a given straight, but nowhere meeting it, is equal:
To one in Euclid's geometry;
To zero in that of Riemann;
To infinity in that of Lobachevski.
Add that Riemann's space is finite, although unbounded, in the sense
given above to these two words.
The Surfaces of Constant Curvature.—One objection still remained
possible. The theorems of Lobachevski and of Riemann present no
contradiction; but however numerous the consequences these two
geometers have drawn from their hypotheses, they must have stopped
before exhausting them, since their number would be infinite; who can say
then that if they had pushed their deductions farther they would not have
eventually reached some contradiction?

This difficulty does not exist for Riemann's geometry, provided it is
limited to two dimensions; in fact, as we have seen, two-dimensional
Riemannian geometry does not differ from spherical geometry, which is
only a branch of ordinary geometry, and consequently is beyond all
discussion.
Beltrami, in correlating likewise Lobachevski's two-dimensional
geometry with a branch of ordinary geometry, has equally refuted the
objection so far as it is concerned.
Here is how he accomplished it. Consider any figure on a surface.
Imagine this figure traced on a flexible and inextensible canvas applied over
this surface in such a way that when the canvas is displaced and deformed,
the various lines of this figure can change their form without changing their
length. In general, this flexible and inextensible figure can not be displaced
without leaving the surface; but there are certain particular surfaces for
which such a movement would be possible; these are the surfaces of
constant curvature.
If we resume the comparison made above and imagine beings without
thickness living on one of these surfaces, they will regard as possible the
motion of a figure all of whose lines remain constant in length. On the
contrary, such a movement would appear absurd to animals without
thickness living on a surface of variable curvature.
These surfaces of constant curvature are of two sorts: Some are of
positive curvature, and can be deformed so as to be applied over a sphere.
The geometry of these surfaces reduces itself therefore to the spherical
geometry, which is that of Riemann.
The others are of negative curvature. Beltrami has shown that the
geometry of these surfaces is none other than that of Lobachevski. The two-
dimensional geometries of Riemann and Lobachevski are thus correlated to
the Euclidean geometry.
Interpretation of Non-Euclidean Geometries.—So vanishes the
objection so far as two-dimensional geometries are concerned.
It would be easy to extend Beltrami's reasoning to three-dimensional
geometries. The minds that space of four dimensions does not repel will see

no difficulty in it, but they are few. I prefer therefore to proceed otherwise.
Consider a certain plane, which I shall call the fundamental plane, and
construct a sort of dictionary, by making correspond each to each a double
series of terms written in two columns, just as correspond in the ordinary
dictionaries the words of two languages whose significance is the same:
Space: Portion of space situated above the fundamental plane.
Plane: Sphere cutting the fundamental plane orthogonally.
Straight: Circle cutting the fundamental plane orthogonally.
Sphere: Sphere.
Circle: Circle.
Angle: Angle.
Distance between two points: Logarithm of the cross ratio of these two
points and the intersections of the fundamental plane with a circle passing
through these two points and cutting it orthogonally. Etc., Etc.
Now take Lobachevski's theorems and translate them with the aid of this
dictionary as we translate a German text with the aid of a German-English
dictionary. We shall thus obtain theorems of the ordinary geometry. For
example, that theorem of Lobachevski: 'the sum of the angles of a triangle
is less than two right angles' is translated thus: "If a curvilinear triangle has
for sides circle-arcs which prolonged would cut orthogonally the
fundamental plane, the sum of the angles of this curvilinear triangle will be
less than two right angles." Thus, however far the consequences of
Lobachevski's hypotheses are pushed, they will never lead to a
contradiction. In fact, if two of Lobachevski's theorems were contradictory,
it would be the same with the translations of these two theorems, made by
the aid of our dictionary, but these translations are theorems of ordinary
geometry and no one doubts that the ordinary geometry is free from
contradiction. Whence comes this certainty and is it justified? That is a
question I can not treat here because it would require to be enlarged upon,
but which is very interesting and I think not insoluble.

Nothing remains then of the objection above formulated. This is not all.
Lobachevski's geometry, susceptible of a concrete interpretation, ceases to
be a vain logical exercise and is capable of applications; I have not the time
to speak here of these applications, nor of the aid that Klein and I have
gotten from them for the integration of linear differential equations.
This interpretation moreover is not unique, and several dictionaries
analogous to the preceding could be constructed, which would enable us by
a simple 'translation' to transform Lobachevski's theorems into theorems of
ordinary geometry.
The Implicit Axioms.—Are the axioms explicitly enunciated in our
treatises the sole foundations of geometry? We may be assured of the
contrary by noticing that after they are successively abandoned there are
still left over some propositions common to the theories of Euclid,
Lobachevski and Riemann. These propositions must rest on premises the
geometers admit without enunciation. It is interesting to try to disentangle
them from the classic demonstrations.
Stuart Mill has claimed that every definition contains an axiom, because
in defining one affirms implicitly the existence of the object defined. This is
going much too far; it is rare that in mathematics a definition is given
without its being followed by the demonstration of the existence of the
object defined, and when this is dispensed with it is generally because the
reader can easily supply it. It must not be forgotten that the word existence
has not the same sense when it refers to a mathematical entity and when it is
a question of a material object. A mathematical entity exists, provided its
definition implies no contradiction, either in itself, or with the propositions
already admitted.
But if Stuart Mill's observation can not be applied to all definitions, it is
none the less just for some of them. The plane is sometimes defined as
follows:
The plane is a surface such that the straight which joins any two of its
points is wholly on this surface.
This definition manifestly hides a new axiom; it is true we might change
it, and that would be preferable, but then we should have to enunciate the

axiom explicitly.
Other definitions would suggest reflections not less important.
Such, for example, is that of the equality of two figures; two figures are
equal when they can be superposed; to superpose them one must be
displaced until it coincides with the other; but how shall it be displaced? If
we should ask this, no doubt we should be told that it must be done without
altering the shape and as a rigid solid. The vicious circle would then be
evident.
In fact this definition defines nothing; it would have no meaning for a
being living in a world where there were only fluids. If it seems clear to us,
that is because we are used to the properties of natural solids which do not
differ much from those of the ideal solids, all of whose dimensions are
invariable.
Yet, imperfect as it may be, this definition implies an axiom.
The possibility of the motion of a rigid figure is not a self-evident truth,
or at least it is so only in the fashion of Euclid's postulate and not as an
analytic judgment a priori would be.
Moreover, in studying the definitions and the demonstrations of
geometry, we see that one is obliged to admit without proof not only the
possibility of this motion, but some of its properties besides.
This is at once seen from the definition of the straight line. Many
defective definitions have been given, but the true one is that which is
implied in all the demonstrations where the straight line enters:
"It may happen that the motion of a rigid figure is such that all the points
of a line belonging to this figure remain motionless while all the points
situated outside of this line move. Such a line will be called a straight line."
We have designedly, in this enunciation, separated the definition from the
axiom it implies.
Many demonstrations, such as those of the cases of the equality of
triangles, of the possibility of dropping a perpendicular from a point to a
straight, presume propositions which are not enunciated, for they require

the admission that it is possible to transport a figure in a certain way in
space.
The Fourth Geometry.—Among these implicit axioms, there is one
which seems to me to merit some attention, because when it is abandoned a
fourth geometry can be constructed as coherent as those of Euclid,
Lobachevski and Riemann.
To prove that a perpendicular may always be erected at a point A to a
straight AB, we consider a straight AC movable around the point A and
initially coincident with the fixed straight AB; and we make it turn about the
point A until it comes into the prolongation of AB.
Thus two propositions are presupposed: First, that such a rotation is
possible, and next that it may be continued until the two straights come into
the prolongation one of the other.
If the first point is admitted and the second rejected, we are led to a series
of theorems even stranger than those of Lobachevski and Riemann, but
equally exempt from contradiction.
I shall cite only one of these theorems and that not the most singular: A
real straight may be perpendicular to itself.
Lie's Theorem.—The number of axioms implicitly introduced in the
classic demonstrations is greater than necessary, and it would be interesting
to reduce it to a minimum. It may first be asked whether this reduction is
possible, whether the number of necessary axioms and that of imaginable
geometries are not infinite.
A theorem of Sophus Lie dominates this whole discussion. It may be thus
enunciated:
Suppose the following premises are admitted:
1º Space has n dimensions;
2º The motion of a rigid figure is possible;
3º It requires p conditions to determine the position of this figure in
space.

The number of geometries compatible with these premises will be limited.
I may even add that if n is given, a superior limit can be assigned to p.
If therefore the possibility of motion is admitted, there can be invented
only a finite (and even a rather small) number of three-dimensional
geometries.
Riemann's Geometries.—Yet this result seems contradicted by Riemann,
for this savant constructs an infinity of different geometries, and that to
which his name is ordinarily given is only a particular case.
All depends, he says, on how the length of a curve is defined. Now, there
is an infinity of ways of defining this length, and each of them may be the
starting point of a new geometry.
That is perfectly true, but most of these definitions are incompatible with
the motion of a rigid figure, which in the theorem of Lie is supposed
possible. These geometries of Riemann, in many ways so interesting, could
never therefore be other than purely analytic and would not lend themselves
to demonstrations analogous to those of Euclid.
On the Nature of Axioms.—Most mathematicians regard Lobachevski's
geometry only as a mere logical curiosity; some of them, however, have
gone farther. Since several geometries are possible, is it certain ours is the
true one? Experience no doubt teaches us that the sum of the angles of a
triangle is equal to two right angles; but this is because the triangles we deal
with are too little; the difference, according to Lobachevski, is proportional
to the surface of the triangle; will it not perhaps become sensible when we
shall operate on larger triangles or when our measurements shall become
more precise? The Euclidean geometry would thus be only a provisional
geometry.
To discuss this opinion, we should first ask ourselves what is the nature
of the geometric axioms.
Are they synthetic a priori judgments, as Kant said?
They would then impose themselves upon us with such force that we
could not conceive the contrary proposition, nor build upon it a theoretic

edifice. There would be no non-Euclidean geometry.
To be convinced of it take a veritable synthetic a priori judgment, the
following, for instance, of which we have seen the preponderant rôle in the
first chapter:
If a theorem is true for the number 1, and if it has been proved that it is
true of n + 1 provided it is true of n, it will be true of all the positive whole
numbers.
Then try to escape from that and, denying this proposition, try to found a
false arithmetic analogous to non-Euclidean geometry—it can not be done;
one would even be tempted at first blush to regard these judgments as
analytic.
Moreover, resuming our fiction of animals without thickness, we can
hardly admit that these beings, if their minds are like ours, would adopt the
Euclidean geometry which would be contradicted by all their experience.
Should we therefore conclude that the axioms of geometry are
experimental verities? But we do not experiment on ideal straights or
circles; it can only be done on material objects. On what then could be
based experiments which should serve as foundation for geometry? The
answer is easy.
We have seen above that we constantly reason as if the geometric figures
behaved like solids. What geometry would borrow from experience would
therefore be the properties of these bodies. The properties of light and its
rectilinear propagation have also given rise to some of the propositions of
geometry, and in particular those of projective geometry, so that from this
point of view one would be tempted to say that metric geometry is the study
of solids, and projective, that of light.
But a difficulty remains, and it is insurmountable. If geometry were an
experimental science, it would not be an exact science, it would be subject
to a continual revision. Nay, it would from this very day be convicted of
error, since we know that there is no rigorously rigid solid.
The axioms of geometry therefore are neither synthetic a priori judgments
nor experimental facts.

They are conventions; our choice among all possible conventions is
guided by experimental facts; but it remains free and is limited only by the
necessity of avoiding all contradiction. Thus it is that the postulates can
remain rigorously true even though the experimental laws which have
determined their adoption are only approximative.
In other words, the axioms of geometry (I do not speak of those of
arithmetic) are merely disguised definitions.
Then what are we to think of that question: Is the Euclidean geometry
true?
It has no meaning.
As well ask whether the metric system is true and the old measures false;
whether Cartesian coordinates are true and polar coordinates false. One
geometry can not be more true than another; it can only be more convenient.
Now, Euclidean geometry is, and will remain, the most convenient:
1º Because it is the simplest; and it is so not only in consequence of our
mental habits, or of I know not what direct intuition that we may have of
Euclidean space; it is the simplest in itself, just as a polynomial of the first
degree is simpler than one of the second; the formulas of spherical
trigonometry are more complicated than those of plane trigonometry, and
they would still appear so to an analyst ignorant of their geometric
signification.
2º Because it accords sufficiently well with the properties of natural
solids, those bodies which our hands and our eyes compare and with which
we make our instruments of measure.

CHAPTER IV

Space and Geometry
Let us begin by a little paradox.

Beings with minds like ours, and having the same senses as we, but
without previous education, would receive from a suitably chosen external
world impressions such that they would be led to construct a geometry
other than that of Euclid and to localize the phenomena of that external
world in a non-Euclidean space, or even in a space of four dimensions.
As for us, whose education has been accomplished by our actual world, if
we were suddenly transported into this new world, we should have no
difficulty in referring its phenomena to our Euclidean space. Conversely, if
these beings were transported into our environment, they would be led to
relate our phenomena to non-Euclidean space.
Nay more; with a little effort we likewise could do it. A person who
should devote his existence to it might perhaps attain to a realization of the
fourth dimension.
Geometric Space and Perceptual Space.—It is often said the images of
external objects are localized in space, even that they can not be formed
except on this condition. It is also said that this space, which serves thus as
a ready prepared frame for our sensations and our representations, is
identical with that of the geometers, of which it possesses all the properties.
To all the good minds who think thus, the preceding statement must have
appeared quite extraordinary. But let us see whether they are not subject to
an illusion that a more profound analysis would dissipate.
What, first of all, are the properties of space, properly so called? I mean
of that space which is the object of geometry and which I shall call
geometric space.
The following are some of the most essential:
1º It is continuous;
2º It is infinite;
3º It has three dimensions;
4º It is homogeneous, that is to say, all its points are identical one with
another;

5º It is isotropic, that is to say, all the straights which pass through the
same point are identical one with another.
Compare it now to the frame of our representations and our sensations,
which I may call perceptual space.
Visual Space.—Consider first a purely visual impression, due to an
image formed on the bottom of the retina.
A cursory analysis shows us this image as continuous, but as possessing
only two dimensions; this already distinguishes from geometric space what
we may call pure visual space.
Besides, this image is enclosed in a limited frame.
Finally, there is another difference not less important: this pure visual
space is not homogeneous. All the points of the retina, aside from the
images which may there be formed, do not play the same rôle. The yellow
spot can in no way be regarded as identical with a point on the border of the
retina. In fact, not only does the same object produce there much more vivid
impressions, but in every limited frame the point occupying the center of
the frame will never appear as equivalent to a point near one of the borders.
No doubt a more profound analysis would show us that this continuity of
visual space and its two dimensions are only an illusion; it would separate it
therefore still more from geometric space, but we shall not dwell on this
remark.
Sight, however, enables us to judge of distances and consequently to
perceive a third dimension. But every one knows that this perception of the
third dimension reduces itself to the sensation of the effort at
accommodation it is necessary to make, and to that of the convergence
which must be given to the two eyes, to perceive an object distinctly.
These are muscular sensations altogether different from the visual
sensations which have given us the notion of the first two dimensions. The
third dimension therefore will not appear to us as playing the same rôle as
the other two. What may be called complete visual space is therefore not an
isotropic space.

It has, it is true, precisely three dimensions, which means that the
elements of our visual sensations (those at least which combine to form the
notion of extension) will be completely defined when three of them are
known; to use the language of mathematics, they will be functions of three
independent variables.
But examine the matter a little more closely. The third dimension is
revealed to us in two different ways: by the effort of accommodation and by
the convergence of the eyes.
No doubt these two indications are always concordant, there is a constant
relation between them, or, in mathematical terms, the two variables which
measure these two muscular sensations do not appear to us as independent;
or again, to avoid an appeal to mathematical notions already rather refined,
we may go back to the language of the preceding chapter and enunciate the
same fact as follows: If two sensations of convergence, A and B, are
indistinguishable, the two sensations of accommodation, A´ and B´, which
respectively accompany them, will be equally indistinguishable.
But here we have, so to speak, an experimental fact; a priori nothing
prevents our supposing the contrary, and if the contrary takes place, if these
two muscular sensations vary independently of one another, we shall have
to take account of one more independent variable, and 'complete visual
space' will appear to us as a physical continuum of four dimensions.
We have here even, I will add, a fact of external experience. Nothing
prevents our supposing that a being with a mind like ours, having the same
sense organs that we have, may be placed in a world where light would only
reach him after having traversed reflecting media of complicated form. The
two indications which serve us in judging distances would cease to be
connected by a constant relation. A being who should achieve in such a
world the education of his senses would no doubt attribute four dimensions
to complete visual space.
Tactile Space and Motor Space.—'Tactile space' is still more
complicated than visual space and farther removed from geometric space. It
is superfluous to repeat for touch the discussion I have given for sight.

But apart from the data of sight and touch, there are other sensations
which contribute as much and more than they to the genesis of the notion of
space. These are known to every one; they accompany all our movements,
and are usually called muscular sensations.
The corresponding frame constitutes what may be called motor space.
Each muscle gives rise to a special sensation capable of augmenting or of
diminishing, so that the totality of our muscular sensations will depend
upon as many variables as we have muscles. From this point of view, motor
space would have as many dimensions as we have muscles.
I know it will be said that if the muscular sensations contribute to form
the notion of space, it is because we have the sense of the direction of each
movement and that it makes an integrant part of the sensation. If this were
so, if a muscular sensation could not arise except accompanied by this
geometric sense of direction, geometric space would indeed be a form
imposed upon our sensibility.
But I perceive nothing at all of this when I analyze my sensations.
What I do see is that the sensations which correspond to movements in
the same direction are connected in my mind by a mere association of
ideas. It is to this association that what we call 'the sense of direction' is
reducible. This feeling therefore can not be found in a single sensation.
This association is extremely complex, for the contraction of the same
muscle may correspond, according to the position of the limbs, to
movements of very different direction.
Besides, it is evidently acquired; it is, like all associations of ideas, the
result of a habit; this habit itself results from very numerous experiences;
without any doubt, if the education of our senses had been accomplished in
a different environment, where we should have been subjected to different
impressions, contrary habits would have arisen and our muscular sensations
would have been associated according to other laws.
Characteristics of Perceptual Space.—Thus perceptual space, under its
triple form, visual, tactile and motor, is essentially different from geometric
space.

It is neither homogeneous, nor isotropic; one can not even say that it has
three dimensions.
It is often said that we 'project' into geometric space the objects of our
external perception; that we 'localize' them.
Has this a meaning, and if so what?
Does it mean that we represent to ourselves external objects in geometric
space?
Our representations are only the reproduction of our sensations; they can
therefore be ranged only in the same frame as these, that is to say, in
perceptual space.
It is as impossible for us to represent to ourselves external bodies in
geometric space, as it is for a painter to paint on a plane canvas objects with
their three dimensions.
Perceptual space is only an image of geometric space, an image altered in
shape by a sort of perspective, and we can represent to ourselves objects
only by bringing them under the laws of this perspective.
Therefore we do not represent to ourselves external bodies in geometric
space, but we reason on these bodies as if they were situated in geometric
space.
When it is said then that we 'localize' such and such an object at such and
such a point of space, what does it mean?
It simply means that we represent to ourselves the movements it would be
necessary to make to reach that object; and one may not say that to
represent to oneself these movements, it is necessary to project the
movements themselves in space and that the notion of space must,
consequently, pre-exist.
When I say that we represent to ourselves these movements, I mean only
that we represent to ourselves the muscular sensations which accompany
them and which have no geometric character whatever, which consequently
do not at all imply the preexistence of the notion of space.

Change of State and Change of Position.—But, it will be said, if the
idea of geometric space is not imposed upon our mind, and if, on the other
hand, none of our sensations can furnish it, how could it have come into
existence?
This is what we have now to examine, and it will take some time, but I
can summarize in a few words the attempt at explanation that I am about to
develop.
None of our sensations, isolated, could have conducted us to the idea of
space; we are led to it only in studying the laws, according to which these
sensations succeed each other.
We see first that our impressions are subject to change; but among the
changes we ascertain we are soon led to make a distinction.
At one time we say that the objects which cause these impressions have
changed state, at another time that they have changed position, that they
have only been displaced.
Whether an object changes its state or merely its position, this is always
translated for us in the same manner: by a modification in an aggregate of
impressions.
How then could we have been led to distinguish between the two? It is
easy to account for. If there has only been a change of position, we can
restore the primitive aggregate of impressions by making movements which
replace us opposite the mobile object in the same relative situation. We thus
correct the modification that happened and we reestablish the initial state
by an inverse modification.
If it is a question of sight, for example, and if an object changes its place
before our eye, we can 'follow it with the eye' and maintain its image on the
same point of the retina by appropriate movements of the eyeball.
These movements we are conscious of because they are voluntary and
because they are accompanied by muscular sensations, but that does not
mean that we represent them to ourselves in geometric space.

So what characterizes change of position, what distinguishes it from
change of state, is that it can always be corrected in this way.
It may therefore happen that we pass from the totality of impressions A to
the totality B in two different ways:
1º Involuntarily and without experiencing muscular sensations; this
happens when it is the object which changes place;
2º Voluntarily and with muscular sensations; this happens when the
object is motionless, but we move so that the object has relative motion
with reference to us.
If this be so, the passage from the totality A to the totality B is only a
change of position.
It follows from this that sight and touch could not have given us the
notion of space without the aid of the 'muscular sense.'
Not only could this notion not be derived from a single sensation or even
from a series of sensations, but what is more, an immobile being could
never have acquired it, since, not being able to correct by his movements
the effects of the changes of position of exterior objects, he would have had
no reason whatever to distinguish them from changes of state. Just as little
could he have acquired it if his motions had not been voluntary or were
unaccompanied by any sensations.
Conditions of Compensation.—How is a like compensation possible, of
such sort that two changes, otherwise independent of each other,
reciprocally correct each other?
A mind already familiar with geometry would reason as follows:
Evidently, if there is to be compensation, the various parts of the external
object, on the one hand, and the various sense organs, on the other hand,
must be in the same relative position after the double change. And, for that
to be the case, the various parts of the external object must likewise have
retained in reference to each other the same relative position, and the same
must be true of the various parts of our body in regard to each other.

In other words, the external object, in the first change, must be displaced
as is a rigid solid, and so must it be with the whole of our body in the
second change which corrects the first.
Under these conditions, compensation may take place.
But we who as yet know nothing of geometry, since for us the notion of
space is not yet formed, we can not reason thus, we can not foresee a priori
whether compensation is possible. But experience teaches us that it
sometimes happens, and it is from this experimental fact that we start to
distinguish changes of state from changes of position.
Solid Bodies and Geometry.—Among surrounding objects there are
some which frequently undergo displacements susceptible of being thus
corrected by a correlative movement of our own body; these are the solid
bodies. The other objects, whose form is variable, only exceptionally
undergo like displacements (change of position without change of form).
When a body changes its place and its shape, we can no longer, by
appropriate movements, bring back our sense-organs into the same relative
situation with regard to this body; consequently we can no longer
reestablish the primitive totality of impressions.
It is only later, and as a consequence of new experiences, that we learn
how to decompose the bodies of variable form into smaller elements, such
that each is displaced almost in accordance with the same laws as solid
bodies. Thus we distinguish 'deformations' from other changes of state; in
these deformations, each element undergoes a mere change of position,
which can be corrected, but the modification undergone by the aggregate is
more profound and is no longer susceptible of correction by a correlative
movement.
Such a notion is already very complex and must have been relatively late
in appearing; moreover it could not have arisen if the observation of solid
bodies had not already taught us to distinguish changes of position.
Therefore, if there were no solid bodies in nature, there would be no
geometry.
Another remark also deserves a moment's attention. Suppose a solid body
to occupy successively the positions α and β; in its first position, it will

produce on us the totality of impressions A, and in its second position the
totality of impressions B. Let there be now a second solid body, having
qualities entirely different from the first, for example, a different color.
Suppose it to pass from the position α, where it gives us the totality of
impressions A´, to the position β, where it gives the totality of impressions
B´.
In general, the totality A will have nothing in common with the totality A
´, nor the totality B with the totality B´. The transition from the totality A to
the totality B and that from the totality A´ to the totality B´ are therefore two
changes which in themselves have in general nothing in common.
And yet we regard these two changes both as displacements and,
furthermore, we consider them as the same displacement. How can that be?
It is simply because they can both be corrected by the same correlative
movement of our body.
'Correlative movement' therefore constitutes the sole connection between
two phenomena which otherwise we never should have dreamt of likening.
On the other hand, our body, thanks to the number of its articulations and
muscles, may make a multitude of different movements; but all are not
capable of 'correcting' a modification of external objects; only those will be
capable of it in which our whole body, or at least all those of our sense-
organs which come into play, are displaced as a whole, that is, without their
relative positions varying, or in the fashion of a solid body.
To summarize:
1º We are led at first to distinguish two categories of phenomena:
Some, involuntary, unaccompanied by muscular sensations, are attributed
by us to external objects; these are external changes;
Others, opposite in character and attributed by us to the movements of
our own body, are internal changes;
2º We notice that certain changes of each of these categories may be
corrected by a correlative change of the other category;

3º We distinguish among external changes those which have thus a
correlative in the other category; these we call displacements; and just so
among the internal changes, we distinguish those which have a correlative
in the first category.
Thus are defined, thanks to this reciprocity, a particular class of
phenomena which we call displacements.
The laws of these phenomena constitute the object of geometry.
Law of Homogeneity.—The first of these laws is the law of homogeneity.
Suppose that, by an external change α, we pass from the totality of
impressions A to the totality B, then that this change α is corrected by a
correlative voluntary movement β, so that we are brought back to the
totality A.
Suppose now that another external change α´ makes us pass anew from
the totality A to the totality B.
Experience teaches us that this change α´ is, like α, susceptible of being
corrected by a correlative voluntary movement β´ and that this movement β´
corresponds to the same muscular sensations as the movement β which
corrected α.
This fact is usually enunciated by saying that space is homogeneous and
isotropic.
It may also be said that a movement which has once been produced may
be repeated a second and a third time, and so on, without its properties
varying.
In the first chapter, where we discussed the nature of mathematical
reasoning, we saw the importance which must be attributed to the
possibility of repeating indefinitely the same operation.
It is from this repetition that mathematical reasoning gets its power; it is,
therefore, thanks to the law of homogeneity, that it has a hold on the
geometric facts.

For completeness, to the law of homogeneity should be added a
multitude of other analogous laws, into the details of which I do not wish to
enter, but which mathematicians sum up in a word by saying that
displacements form 'a group.'
The Non-Euclidean World.—If geometric space were a frame imposed
on each of our representations, considered individually, it would be
impossible to represent to ourselves an image stripped of this frame, and we
could change nothing of our geometry.
But this is not the case; geometry is only the résumé of the laws
according to which these images succeed each other. Nothing then prevents
us from imagining a series of representations, similar in all points to our
ordinary representations, but succeeding one another according to laws
different from those to which we are accustomed.
We can conceive then that beings who received their education in an
environment where these laws were thus upset might have a geometry very
different from ours.
Suppose, for example, a world enclosed in a great sphere and subject to
the following laws:
The temperature is not uniform; it is greatest at the center, and diminishes
in proportion to the distance from the center, to sink to absolute zero when
the sphere is reached in which this world is enclosed.
To specify still more precisely the law in accordance with which this
temperature varies: Let R be the radius of the limiting sphere; let r be the
distance of the point considered from the center of this sphere. The absolute
temperature shall be proportional to R2 − r2.
I shall further suppose that, in this world, all bodies have the same
coefficient of dilatation, so that the length of any rule is proportional to its
absolute temperature.
Finally, I shall suppose that a body transported from one point to another
of different temperature is put immediately into thermal equilibrium with its
new environment.

Nothing in these hypotheses is contradictory or unimaginable.
A movable object will then become smaller and smaller in proportion as
it approaches the limit-sphere.
Note first that, though this world is limited from the point of view of our
ordinary geometry, it will appear infinite to its inhabitants.
In fact, when these try to approach the limit-sphere, they cool off and
become smaller and smaller. Therefore the steps they take are also smaller
and smaller, so that they can never reach the limiting sphere.
If, for us, geometry is only the study of the laws according to which rigid
solids move, for these imaginary beings it will be the study of the laws of
motion of solids distorted by the differences of temperature just spoken of.
No doubt, in our world, natural solids likewise undergo variations of
form and volume due to warming or cooling. But we neglect these
variations in laying the foundations of geometry, because, besides their
being very slight, they are irregular and consequently seem to us accidental.
In our hypothetical world, this would no longer be the case, and these
variations would follow regular and very simple laws.
Moreover, the various solid pieces of which the bodies of its inhabitants
would be composed would undergo the same variations of form and
volume.
I will make still another hypothesis; I will suppose light traverses media
diversely refractive and such that the index of refraction is inversely
proportional to R2 − r2. It is easy to see that, under these conditions, the rays
of light would not be rectilinear, but circular.
To justify what precedes, it remains for me to show that certain changes
in the position of external objects can be corrected by correlative
movements of the sentient beings inhabiting this imaginary world, and that
in such a way as to restore the primitive aggregate of impressions
experienced by these sentient beings.

Suppose in fact that an object is displaced, undergoing deformation, not
as a rigid solid, but as a solid subjected to unequal dilatations in exact
conformity to the law of temperature above supposed. Permit me for brevity
to call such a movement a non-Euclidean displacement.
If a sentient being happens to be in the neighborhood, his impressions
will be modified by the displacement of the object, but he can reestablish
them by moving in a suitable manner. It suffices if finally the aggregate of
the object and the sentient being, considered as forming a single body, has
undergone one of those particular displacements I have just called non-
Euclidean. This is possible if it be supposed that the limbs of these beings
dilate according to the same law as the other bodies of the world they
inhabit.
Although from the point of view of our ordinary geometry there is a
deformation of the bodies in this displacement and their various parts are no
longer in the same relative position, nevertheless we shall see that the
impressions of the sentient being have once more become the same.
In fact, though the mutual distances of the various parts may have varied,
yet the parts originally in contact are again in contact. Therefore the tactile
impressions have not changed.
On the other hand, taking into account the hypothesis made above in
regard to the refraction and the curvature of the rays of light, the visual
impressions will also have remained the same.
These imaginary beings will therefore like ourselves be led to classify the
phenomena they witness and to distinguish among them the 'changes of
position' susceptible of correction by a correlative voluntary movement.
If they construct a geometry, it will not be, as ours is, the study of the
movements of our rigid solids; it will be the study of the changes of
position which they will thus have distinguished and which are none other
than the 'non-Euclidean displacements'; it will be non-Euclidean geometry.
Thus beings like ourselves, educated in such a world, would not have the
same geometry as ours.

The World of Four Dimensions.—We can represent to ourselves a four-
dimensional world just as well as a non-Euclidean.
The sense of sight, even with a single eye, together with the muscular
sensations relative to the movements of the eyeball, would suffice to teach
us space of three dimensions.
The images of external objects are painted on the retina, which is a two-
dimensional canvas; they are perspectives.
But, as eye and objects are movable, we see in succession various
perspectives of the same body, taken from different points of view.
At the same time, we find that the transition from one perspective to
another is often accompanied by muscular sensations.
If the transition from the perspective A to the perspective B, and that
from the perspective A´ to the perspective B´ are accompanied by the same
muscular sensations, we liken them one to the other as operations of the
same nature.
Studying then the laws according to which these operations combine, we
recognize that they form a group, which has the same structure as that of the
movements of rigid solids.
Now, we have seen that it is from the properties of this group we have
derived the notion of geometric space and that of three dimensions.
We understand thus how the idea of a space of three dimensions could
take birth from the pageant of these perspectives, though each of them is of
only two dimensions, since they follow one another according to certain
laws.
Well, just as the perspective of a three-dimensional figure can be made
on a plane, we can make that of a four-dimensional figure on a picture of
three (or of two) dimensions. To a geometer this is only child's play.
We can even take of the same figure several perspectives from several
different points of view.

We can easily represent to ourselves these perspectives, since they are of
only three dimensions.
Imagine that the various perspectives of the same object succeed one
another, and that the transition from one to the other is accompanied by
muscular sensations.
We shall of course consider two of these transitions as two operations of
the same nature when they are associated with the same muscular
sensations.
Nothing then prevents us from imagining that these operations combine
according to any law we choose, for example, so as to form a group with
the same structure as that of the movements of a rigid solid of four
dimensions.
Here there is nothing unpicturable, and yet these sensations are precisely
those which would be felt by a being possessed of a two-dimensional retina
who could move in space of four dimensions. In this sense we may say the
fourth dimension is imaginable.
Conclusions.—We see that experience plays an indispensable rôle in the
genesis of geometry; but it would be an error thence to conclude that
geometry is, even in part, an experimental science.
If it were experimental, it would be only approximative and provisional.
And what rough approximation!
Geometry would be only the study of the movements of solids; but in
reality it is not occupied with natural solids, it has for object certain ideal
solids, absolutely rigid, which are only a simplified and very remote image
of natural solids.
The notion of these ideal solids is drawn from all parts of our mind, and
experience is only an occasion which induces us to bring it forth from them.
The object of geometry is the study of a particular 'group'; but the general
group concept pre-exists, at least potentially, in our minds. It is imposed on
us, not as form of our sense, but as form of our understanding.

Only, from among all the possible groups, that must be chosen which will
be, so to speak, the standard to which we shall refer natural phenomena.
Experience guides us in this choice without forcing it upon us; it tells us
not which is the truest geometry, but which is the most convenient.
Notice that I have been able to describe the fantastic worlds above
imagined without ceasing to employ the language of ordinary geometry.
And, in fact, we should not have to change it if transported thither.
Beings educated there would doubtless find it more convenient to create
a geometry different from ours, and better adapted to their impressions. As
for us, in face of the same impressions, it is certain we should find it more
convenient not to change our habits.

CHAPTER V

Experience and Geometry
1. Already in the preceding pages I have several times tried to show that
the principles of geometry are not experimental facts and that in particular
Euclid's postulate can not be proven experimentally.
However decisive appear to me the reasons already given, I believe I
should emphasize this point because here a false idea is profoundly rooted
in many minds.
2. If we construct a material circle, measure its radius and circumference,
and see if the ratio of these two lengths is equal to π, what shall we have
done? We shall have made an experiment on the properties of the matter
with which we constructed this round thing, and of that of which the
measure used was made.
3. Geometry and Astronomy.—The question has also been put in another
way. If Lobachevski's geometry is true, the parallax of a very distant star
will be finite; if Riemann's is true, it will be negative. These are results
which seem within the reach of experiment, and there have been hopes that
astronomical observations might enable us to decide between the three
geometries.
But in astronomy 'straight line' means simply 'path of a ray of light.'
If therefore negative parallaxes were found, or if it were demonstrated
that all parallaxes are superior to a certain limit, two courses would be open
to us; we might either renounce Euclidean geometry, or else modify the
laws of optics and suppose that light does not travel rigorously in a straight
line.
It is needless to add that all the world would regard the latter solution as
the more advantageous.
The Euclidean geometry has, therefore, nothing to fear from fresh
experiments.

4. Is the position tenable, that certain phenomena, possible in Euclidean
space, would be impossible in non-Euclidean space, so that experience, in
establishing these phenomena, would directly contradict the non-Euclidean
hypothesis? For my part I think no such question can be put. To my mind it
is precisely equivalent to the following, whose absurdity is patent to all
eyes: are there lengths expressible in meters and centimeters, but which can
not be measured in fathoms, feet and inches, so that experience, in
ascertaining the existence of these lengths, would directly contradict the
hypothesis that there are fathoms divided into six feet?
Examine the question more closely. I suppose that the straight line
possesses in Euclidean space any two properties which I shall call A and B;
that in non-Euclidean space it still possesses the property A, but no longer
has the property B; finally I suppose that in both Euclidean and non-
Euclidean space the straight line is the only line having the property A.
If this were so, experience would be capable of deciding between the
hypothesis of Euclid and that of Lobachevski. It would be ascertained that a
definite concrete object, accessible to experiment, for example, a pencil of
rays of light, possesses the property A; we should conclude that it is
rectilinear, and then investigate whether or not it has the property B.
But this is not so; no property exists which, like this property A, can be
an absolute criterion enabling us to recognize the straight line and to
distinguish it from every other line.
Shall we say, for instance: "the following is such a property: the straight
line is a line such that a figure of which this line forms a part can be moved
without the mutual distances of its points varying and so that all points of
this line remain fixed"?
This, in fact, is a property which, in Euclidean or non-Euclidean space,
belongs to the straight and belongs only to it. But how shall we ascertain
experimentally whether it belongs to this or that concrete object? It will be
necessary to measure distances, and how shall one know that any concrete
magnitude which I have measured with my material instrument really
represents the abstract distance?
We have only pushed back the difficulty.

In reality the property just enunciated is not a property of the straight line
alone, it is a property of the straight line and distance. For it to serve as
absolute criterion, we should have to be able to establish not only that it
does not also belong to a line other than the straight and to distance, but in
addition that it does not belong to a line other than the straight and to a
magnitude other than distance. Now this is not true.
It is therefore impossible to imagine a concrete experiment which can be
interpreted in the Euclidean system and not in the Lobachevskian system,
so that I may conclude:
No experience will ever be in contradiction to Euclid's postulate; nor, on
the other hand, will any experience ever contradict the postulate of
Lobachevski.
5. But it is not enough that the Euclidean (or non-Euclidean) geometry
can never be directly contradicted by experience. Might it not happen that it
can accord with experience only by violating the principle of sufficient
reason or that of the relativity of space?
I will explain myself: consider any material system; we shall have to
regard, on the one hand, 'the state' of the various bodies of this system (for
instance, their temperature, their electric potential, etc.), and, on the other
hand, their position in space; and among the data which enable us to define
this position we shall, moreover, distinguish the mutual distances of these
bodies, which define their relative positions, from the conditions which
define the absolute position of the system and its absolute orientation in
space.
The laws of the phenomena which will happen in this system will depend
on the state of these bodies and their mutual distances; but, because of the
relativity and passivity of space, they will not depend on the absolute
position and orientation of the system.
In other words, the state of the bodies and their mutual distances at any
instant will depend solely on the state of these same bodies and on their
mutual distances at the initial instant, but will not at all depend on the
absolute initial position of the system or on its absolute initial orientation.
This is what for brevity I shall call the law of relativity.

Hitherto I have spoken as a Euclidean geometer. As I have said, an
experience, whatever it be, admits of an interpretation on the Euclidean
hypothesis; but it admits of one equally on the non-Euclidean hypothesis.
Well, we have made a series of experiments; we have interpreted them on
the Euclidean hypothesis, and we have recognized that these experiments
thus interpreted do not violate this 'law of relativity.'
We now interpret them on the non-Euclidean hypothesis: this is always
possible; only the non-Euclidean distances of our different bodies in this
new interpretation will not generally be the same as the Euclidean distances
in the primitive interpretation.
Will our experiments, interpreted in this new manner, still be in accord
with our 'law of relativity'? And if there were not this accord, should we not
have also the right to say experience had proven the falsity of the non-
Euclidean geometry?
It is easy to see that this is an idle fear; in fact, to apply the law of
relativity in all rigor, it must be applied to the entire universe. For if only a
part of this universe were considered, and if the absolute position of this
part happened to vary, the distances to the other bodies of the universe
would likewise vary, their influence on the part of the universe considered
would consequently augment or diminish, which might modify the laws of
the phenomena happening there.
But if our system is the entire universe, experience is powerless to give
information about its absolute position and orientation in space. All that our
instruments, however perfected they may be, can tell us will be the state of
the various parts of the universe and their mutual distances.
So our law of relativity may be thus enunciated:
The readings we shall be able to make on our instruments at any instant
will depend only on the readings we could have made on these same
instruments at the initial instant.
Now such an enunciation is independent of every interpretation of
experimental facts. If the law is true in the Euclidean interpretation, it will
also be true in the non-Euclidean interpretation.

Allow me here a short digression. I have spoken above of the data which
define the position of the various bodies of the system; I should likewise
have spoken of those which define their velocities; I should then have had
to distinguish the velocities with which the mutual distances of the different
bodies vary; and, on the other hand, the velocities of translation and rotation
of the system, that is to say, the velocities with which its absolute position
and orientation vary.
To fully satisfy the mind, the law of relativity should be expressible thus:
The state of bodies and their mutual distances at any instant, as well as
the velocities with which these distances vary at this same instant, will
depend only on the state of those bodies and their mutual distances at the
initial instant, and the velocities with which these distances vary at this
initial instant, but they will not depend either upon the absolute initial
position of the system, or upon its absolute orientation, or upon the
velocities with which this absolute position and orientation varied at the
initial instant.
Unhappily the law thus enunciated is not in accord with experiments, at
least as they are ordinarily interpreted.
Suppose a man be transported to a planet whose heavens were always
covered with a thick curtain of clouds, so that he could never see the other
stars; on that planet he would live as if it were isolated in space. Yet this
man could become aware that it turned, either by measuring its oblateness
(done ordinarily by the aid of astronomic observations, but capable of being
done by purely geodetic means), or by repeating the experiment of
Foucault's pendulum. The absolute rotation of this planet could therefore be
made evident.
That is a fact which shocks the philosopher, but which the physicist is
compelled to accept.
We know that from this fact Newton inferred the existence of absolute
space; I myself am quite unable to adopt this view. I shall explain why in
Part III. For the moment it is not my intention to enter upon this difficulty.
Therefore I must resign myself, in the enunciation of the law of relativity,
to including velocities of every kind among the data which define the state

of the bodies.
However that may be, this difficulty is the same for Euclid's geometry as
for Lobachevski's; I therefore need not trouble myself with it, and have only
mentioned it incidentally.
What is important is the conclusion: experiment can not decide between
Euclid and Lobachevski.
To sum up, whichever way we look at it, it is impossible to discover in
geometric empiricism a rational meaning.
6. Experiments only teach us the relations of bodies to one another; none
of them bears or can bear on the relations of bodies with space, or on the
mutual relations of different parts of space.
"Yes," you reply, "a single experiment is insufficient, because it gives me
only a single equation with several unknowns; but when I shall have made
enough experiments I shall have equations enough to calculate all my
unknowns."
To know the height of the mainmast does not suffice for calculating the
age of the captain. When you have measured every bit of wood in the ship
you will have many equations, but you will know his age no better. All your
measurements bearing only on your bits of wood can reveal to you nothing
except concerning these bits of wood. Just so your experiments, however
numerous they may be, bearing only on the relations of bodies to one
another, will reveal to us nothing about the mutual relations of the various
parts of space.
7. Will you say that if the experiments bear on the bodies, they bear at
least upon the geometric properties of the bodies? But, first, what do you
understand by geometric properties of the bodies? I assume that it is a
question of the relations of the bodies with space; these properties are
therefore inaccessible to experiments which bear only on the relations of the
bodies to one another. This alone would suffice to show that there can be no
question of these properties.
Still let us begin by coming to an understanding about the sense of the
phrase: geometric properties of bodies. When I say a body is composed of

several parts, I assume that I do not enunciate therein a geometric property,
and this would remain true even if I agreed to give the improper name of
points to the smallest parts I consider.
When I say that such a part of such a body is in contact with such a part
of such another body, I enunciate a proposition which concerns the mutual
relations of these two bodies and not their relations with space.
I suppose you will grant me these are not geometric properties; at least I
am sure you will grant me these properties are independent of all
knowledge of metric geometry.
This presupposed, I imagine that we have a solid body formed of eight
slender iron rods, OA, OB, OC, OD, OE, OF, OG, OH, united at one of
their extremities O. Let us besides have a second solid body, for example a
bit of wood, to be marked with three little flecks of ink which I shall call α,
β, γ. I further suppose it ascertained that αβγ may be brought into contact
with AGO (I mean α with A, and at the same time β with G and γ with O),
then that we may bring successively into contact αβγ with BGO, CGO,
DGO, EGO, FGO, then with AHO, BHO, CHO, DHO, EHO, FHO, then αγ
successively with AB, BC, CD, DE, EF, FA.
These are determinations we may make without having in advance any
notion about form or about the metric properties of space. They in no wise
bear on the 'geometric properties of bodies.' And these determinations will
not be possible if the bodies experimented upon move in accordance with a
group having the same structure as the Lobachevskian group (I mean
according to the same laws as solid bodies in Lobachevski's geometry).
They suffice therefore to prove that these bodies move in accordance with
the Euclidean group, or at least that they do not move according to the
Lobachevskian group.
That they are compatible with the Euclidean group is easy to see. For
they could be made if the body αβγ was a rigid solid of our ordinary
geometry presenting the form of a right-angled triangle, and if the points
ABCDEFGH were the summits of a polyhedron formed of two regular
hexagonal pyramids of our ordinary geometry, having for common base
ABCDEF and for apices the one G and the other H.

Suppose now that in place of the preceding determination it is observed
that as above αβγ can be successively applied to AGO, BGO, CGO, DGO,
EGO, AHO, BHO, CHO, DHO, EHO, FHO, then that αβ (and no longer αγ)
can be successively applied to AB, BC, CD, DE, EF and FA.
These are determinations which could be made if non-Euclidean
geometry were true, if the bodies αβγ and OABCDEFGH were rigid solids,
and if the first were a right-angled triangle and the second a double regular
hexagonal pyramid of suitable dimensions.
Therefore these new determinations are not possible if the bodies move
according to the Euclidean group; but they become so if it be supposed that
the bodies move according to the Lobachevskian group. They would
suffice, therefore (if one made them), to prove that the bodies in question do
not move according to the Euclidean group.
Thus, without making any hypothesis about form, about the nature of
space, about the relations of bodies to space, and without attributing to
bodies any geometric property, I have made observations which have
enabled me to show in one case that the bodies experimented upon move
according to a group whose structure is Euclidean, in the other case that
they move according to a group whose structure is Lobachevskian.
And one may not say that the first aggregate of determinations would
constitute an experiment proving that space is Euclidean, and the second an
experiment proving that space is non-Euclidean.
In fact one could imagine (I say imagine) bodies moving so as to render
possible the second series of determinations. And the proof is that the first
mechanician met could construct such bodies if he cared to take the pains
and make the outlay. You will not conclude from that, however, that space is
non-Euclidean.
Nay, since the ordinary solid bodies would continue to exist when the
mechanician had constructed the strange bodies of which I have just
spoken, it would be necessary to conclude that space is at the same time
Euclidean and non-Euclidean.
Suppose, for example, that we have a great sphere of radius R and that
the temperature decreases from the center to the surface of this sphere

according to the law of which I have spoken in describing the non-
Euclidean world.
We might have bodies whose expansion would be negligible and which
would act like ordinary rigid solids; and, on the other hand, bodies very
dilatable and which would act like non-Euclidean solids. We might have
two double pyramids OABCDEFGH and O´A´B´C´D´E´F´G´H´ and two
triangles αβγ and α´β´γ´. The first double pyramid might be rectilinear and
the second curvilinear; the triangle αβγ might be made of inexpansible
matter and the other of a very dilatable matter.
It would then be possible to make the first observations with the double
pyramid OAH and the triangle αβγ, and the second with the double pyramid
O´A´H´ and the triangle α´β´γ´. And then experiment would seem to prove
first that the Euclidean geometry is true and then that it is false.
Experiments therefore have a bearing, not on space, but on bodies.
Supplement
8. To complete the matter, I ought to speak of a very delicate question,
which would require long development; I shall confine myself to
summarizing here what I have expounded in the Revue de Métaphysique et
de Morale and in The Monist. When we say space has three dimensions,
what do we mean?
We have seen the importance of those 'internal changes' revealed to us by
our muscular sensations. They may serve to characterize the various
attitudes of our body. Take arbitrarily as origin one of these attitudes A.
When we pass from this initial attitude to any other attitude B, we feel a
series of muscular sensations, and this series S will define B. Observe,
however, that we shall often regard two series S and S´ as defining the same
attitude B (since the initial and final attitudes A and B remaining the same,
the intermediary attitudes and the corresponding sensations may differ).
How then shall we recognize the equivalence of these two series? Because
they may serve to compensate the same external change, or more generally
because, when it is a question of compensating an external change, one of
the series can be replaced by the other. Among these series, we have
distinguished those which of themselves alone can compensate an external

change, and which we have called 'displacements.' As we can not
discriminate between two displacements which are too close together, the
totality of these displacements presents the characteristics of a physical
continuum; experience teaches us that they are those of a physical
continuum of six dimensions; but we do not yet know how many
dimensions space itself has, we must first solve another question.
What is a point of space? Everybody thinks he knows, but that is an
illusion. What we see when we try to represent to ourselves a point of space
is a black speck on white paper, a speck of chalk on a blackboard, always an
object. The question should therefore be understood as follows:
What do I mean when I say the object B is at the same point that the
object A occupied just now? Or further, what criterion will enable me to
apprehend this?
I mean that, although I have not budged (which my muscular sense tells
me), my first finger which just now touched the object A touches at present
the object B. I could have used other criteria; for instance another finger or
the sense of sight. But the first criterion is sufficient; I know that if it
answers yes, all the other criteria will give the same response. I know it by
experience, I can not know it a priori. For the same reason I say that touch
can not be exercised at a distance; this is another way of enunciating the
same experimental fact. And if, on the contrary, I say that sight acts at a
distance, it means that the criterion furnished by sight may respond yes
while the others reply no.
And in fact, the object, although moved away, may form its image at the
same point of the retina. Sight responds yes, the object has remained at the
same point and touch answers no, because my finger which just now
touched the object, at present touches it no longer. If experience had shown
us that one finger may respond no when the other says yes, we should
likewise say that touch acts at a distance.
In short, for each attitude of my body, my first finger determines a point,
and this it is, and this alone, which defines a point of space.
To each attitude corresponds thus a point; but it often happens that the
same point corresponds to several different attitudes (in this case we say our

finger has not budged, but the rest of the body has moved). We distinguish,
therefore, among the changes of attitude those where the finger does not
budge. How are we led thereto? It is because often we notice that in these
changes the object which is in contact with the finger remains in contact
with it.
Range, therefore, in the same class all the attitudes obtainable from each
other by one of the changes we have thus distinguished. To all the attitudes
of the class will correspond the same point of space. Therefore to each class
will correspond a point and to each point a class. But one may say that what
experience arrives at is not the point, it is this class of changes or, better, the
corresponding class of muscular sensations.
And when we say space has three dimensions, we simply mean that the
totality of these classes appears to us with the characteristics of a physical
continuum of three dimensions.
One might be tempted to conclude that it is experience which has taught
us how many dimensions space has. But in reality here also our experiences
have bearing, not on space, but on our body and its relations with the
neighboring objects. Moreover they are excessively crude.
In our mind pre-existed the latent idea of a certain number of groups—
those whose theory Lie has developed. Which group shall we choose, to
make of it a sort of standard with which to compare natural phenomena?
And, this group chosen, which of its sub-groups shall we take to
characterize a point of space? Experience has guided us by showing us
which choice best adapts itself to the properties of our body. But its rôle is
limited to that.

Ancestral Experience
It has often been said that if individual experience could not create
geometry the same is not true of ancestral experience. But what does that
mean? Is it meant that we could not experimentally demonstrate Euclid's
postulate, but that our ancestors have been able to do it? Not in the least. It
is meant that by natural selection our mind has adapted itself to the
conditions of the external world, that it has adopted the geometry most
advantageous to the species: or in other words the most convenient. This is

entirely in conformity with our conclusions; geometry is not true, it is
advantageous.

PART III

FORCE

CHAPTER VI

The Classic Mechanics
The English teach mechanics as an experimental science; on the
continent it is always expounded as more or less a deductive and a priori
science. The English are right, that goes without saying; but how could the
other method have been persisted in so long? Why have the continental
savants who have sought to get out of the ruts of their predecessors been
usually unable to free themselves completely?
On the other hand, if the principles of mechanics are only of
experimental origin, are they not therefore only approximate and
provisional? Might not new experiments some day lead us to modify or
even to abandon them?
Such are the questions which naturally obtrude themselves, and the
difficulty of solution comes principally from the fact that the treatises on
mechanics do not clearly distinguish between what is experiment, what is
mathematical reasoning, what is convention, what is hypothesis.
That is not all:
1º There is no absolute space and we can conceive only of relative
motions; yet usually the mechanical facts are enunciated as if there were an
absolute space to which to refer them.

2º There is no absolute time; to say two durations are equal is an
assertion which has by itself no meaning and which can acquire one only by
convention.
3º Not only have we no direct intuition of the equality of two durations,
but we have not even direct intuition of the simultaneity of two events
occurring in different places: this I have explained in an article entitled La
mesure du temps.[3]
4º Finally, our Euclidean geometry is itself only a sort of convention of
language; mechanical facts might be enunciated with reference to a non-
Euclidean space which would be a guide less convenient than, but just as
legitimate as, our ordinary space; the enunciation would thus become much
more complicated, but it would remain possible.
Thus absolute space, absolute time, geometry itself, are not conditions
which impose themselves on mechanics; all these things are no more
antecedent to mechanics than the French language is logically antecedent to
the verities one expresses in French.
We might try to enunciate the fundamental laws of mechanics in a
language independent of all these conventions; we should thus without
doubt get a better idea of what these laws are in themselves; this is what M.
Andrade has attempted to do, at least in part, in his Leçons de mécanique
physique.
The enunciation of these laws would become of course much more
complicated, because all these conventions have been devised expressly to
abridge and simplify this enunciation.
As for me, save in what concerns absolute space, I shall ignore all these
difficulties; not that I fail to appreciate them, far from that; but we have
sufficiently examined them in the first two parts of the book.
I shall therefore admit, provisionally, absolute time and Euclidean
geometry.
The Principle of Inertia.—A body acted on by no force can only move
uniformly in a straight line.

Is this a truth imposed a priori upon the mind? If it were so, how should
the Greeks have failed to recognize it? How could they have believed that
motion stops when the cause which gave birth to it ceases? Or again that
every body if nothing prevents, will move in a circle, the noblest of
motions?
If it is said that the velocity of a body can not change if there is no reason
for it to change, could it not be maintained just as well that the position of
this body can not change, or that the curvature of its trajectory can not
change, if no external cause intervenes to modify them?
Is the principle of inertia, which is not an a priori truth, therefore an
experimental fact? But has any one ever experimented on bodies withdrawn
from the action of every force? and, if so, how was it known that these
bodies were subjected to no force? The example ordinarily cited is that of a
ball rolling a very long time on a marble table; but why do we say it is
subjected to no force? Is this because it is too remote from all other bodies
to experience any appreciable action from them? Yet it is not farther from
the earth than if it were thrown freely into the air; and every one knows that
in this case it would experience the influence of gravity due to the attraction
of the earth.
Teachers of mechanics usually pass rapidly over the example of the ball;
but they add that the principle of inertia is verified indirectly by its
consequences. They express themselves badly; they evidently mean it is
possible to verify various consequences of a more general principle, of
which that of inertia is only a particular case.
I shall propose for this general principle the following enunciation:
The acceleration of a body depends only upon the position of this body
and of the neighboring bodies and upon their velocities.
Mathematicians would say the movements of all the material molecules
of the universe depend on differential equations of the second order.
To make it clear that this is really the natural generalization of the law of
inertia, I shall beg you to permit me a bit of fiction. The law of inertia, as I
have said above, is not imposed upon us a priori; other laws would be quite
as compatible with the principle of sufficient reason. If a body is subjected

to no force, in lieu of supposing its velocity not to change, it might be
supposed that it is its position or else its acceleration which is not to change.
Well, imagine for an instant that one of these two hypothetical laws is a
law of nature and replaces our law of inertia. What would be its natural
generalization? A moment's thought will show us.
In the first case, we must suppose that the velocity of a body depends
only upon its position and upon that of the neighboring bodies; in the
second case that the change of acceleration of a body depends only upon the
position of this body and of the neighboring bodies, upon their velocities
and upon their accelerations.
Or to speak the language of mathematics, the differential equations of
motion would be of the first order in the first case, and of the third order in
the second case.
Let us slightly modify our fiction. Suppose a world analogous to our
solar system, but where, by a strange chance, the orbits of all the planets are
without eccentricity and without inclination. Suppose further that the
masses of these planets are too slight for their mutual perturbations to be
sensible. Astronomers inhabiting one of these planets could not fail to
conclude that the orbit of a star can only be circular and parallel to a certain
plane; the position of a star at a given instant would then suffice to
determine its velocity and its whole path. The law of inertia which they
would adopt would be the first of the two hypothetical laws I have
mentioned.
Imagine now that this system is some day traversed with great velocity
by a body of vast mass, coming from distant constellations. All the orbits
would be profoundly disturbed. Still our astronomers would not be too
greatly astonished; they would very well divine that this new star was alone
to blame for all the mischief. "But," they would say, "when it is gone, order
will of itself be reestablished; no doubt the distances of the planets from the
sun will not revert to what they were before the cataclysm, but when the
perturbing star is gone, the orbits will again become circular."
It would only be when the disturbing body was gone and when
nevertheless the orbits, in lieu of again becoming circular, became elliptic,

that these astronomers would become conscious of their error and the
necessity of remaking all their mechanics.
I have dwelt somewhat upon these hypotheses because it seems to me
one can clearly comprehend what our generalized law of inertia really is
only in contrasting it with a contrary hypothesis.
Well, now, has this generalized law of inertia been verified by
experiment, or can it be? When Newton wrote the Principia he quite
regarded this truth as experimentally acquired and demonstrated. It was so
in his eyes, not only through the anthropomorphism of which we shall
speak further on, but through the work of Galileo. It was so even from
Kepler's laws themselves; in accordance with these laws, in fact, the path of
a planet is completely determined by its initial position and initial velocity;
this is just what our generalized law of inertia requires.
For this principle to be only in appearance true, for one to have cause to
dread having some day to replace it by one of the analogous principles I
have just now contrasted with it, would be necessary our having been
misled by some amazing chance, like that which, in the fiction above
developed, led into error our imaginary astronomers.
Such a hypothesis is too unlikely to delay over. No one will believe that
such coincidences can happen; no doubt the probability of two
eccentricities being both precisely null, to within errors of observation, is
not less than the probability of one being precisely equal to 0.1, for
instance, and the other to 0.2, to within errors of observation. The
probability of a simple event is not less than that of a complicated event;
and yet, if the first happens, we shall not consent to attribute it to chance;
we should not believe that nature had acted expressly to deceive us. The
hypothesis of an error of this sort being discarded, it may therefore be
admitted that in so far as astronomy is concerned, our law has been verified
by experiment.
But astronomy is not the whole of physics.
May we not fear lest some day a new experiment should come to falsify
the law in some domain of physics? An experimental law is always subject

to revision; one should always expect to see it replaced by a more precise
law.
Yet no one seriously thinks that the law we are speaking of will ever be
abandoned or amended. Why? Precisely because it can never be subjected
to a decisive test.
First of all, in order that this trial should be complete, it would be
necessary that after a certain time all the bodies in the universe should
revert to their initial positions with their initial velocities. It might then be
seen whether, starting from this moment, they would resume their original
paths.
But this test is impossible, it can be only partially applied, and, however
well it is made, there will always be some bodies which will not revert to
their initial positions; thus every derogation of the law will easily find its
explanation.
This is not all; in astronomy we see the bodies whose motions we study
and we usually assume that they are not subjected to the action of other
invisible bodies. Under these conditions our law must indeed be either
verified or not verified.
But it is not the same in physics; if the physical phenomena are due to
motions, it is to the motions of molecules which we do not see. If then the
acceleration of one of the bodies we see appears to us to depend on
something else besides the positions or velocities of other visible bodies or
of invisible molecules whose existence we have been previously led to
admit, nothing prevents our supposing that this something else is the
position or the velocity of other molecules whose presence we have not
before suspected. The law will find itself safeguarded.
Permit me to employ mathematical language a moment to express the
same thought under another form. Suppose we observe n molecules and
ascertain that their 3n coordinates satisfy a system of 3n differential
equations of the fourth order (and not of the second order as the law of
inertia would require). We know that by introducing 3n auxiliary variables,
a system of 3n equations of the fourth order can be reduced to a system of
6n equations of the second order. If then we suppose these 3n auxiliary

variables represent the coordinates of n invisible molecules, the result is
again in conformity with the law of inertia.
To sum up, this law, verified experimentally in some particular cases,
may unhesitatingly be extended to the most general cases, since we know
that in these general cases experiment no longer is able either to confirm or
to contradict it.
The Law of Acceleration.—The acceleration of a body is equal to the
force acting on it divided by its mass. Can this law be verified by
experiment? For that it would be necessary to measure the three magnitudes
which figure in the enunciation: acceleration, force and mass.
I assume that acceleration can be measured, for I pass over the difficulty
arising from the measurement of time. But how measure force, or mass? We
do not even know what they are.
What is mass? According to Newton, it is the product of the volume by
the density. According to Thomson and Tait, it would be better to say that
density is the quotient of the mass by the volume. What is force? It is,
replies Lagrange, that which moves or tends to move a body. It is, Kirchhoff
will say, the product of the mass by the acceleration. But then, why not say
the mass is the quotient of the force by the acceleration?
These difficulties are inextricable.
When we say force is the cause of motion, we talk metaphysics, and this
definition, if one were content with it, would be absolutely sterile. For a
definition to be of any use, it must teach us to measure force; moreover that
suffices; it is not at all necessary that it teach us what force is in itself, nor
whether it is the cause or the effect of motion.
We must therefore first define the equality of two forces. When shall we
say two forces are equal? It is, we are told, when, applied to the same mass,
they impress upon it the same acceleration, or when, opposed directly one
to the other, they produce equilibrium. This definition is only a sham. A
force applied to a body can not be uncoupled to hook it up to another body,
as one uncouples a locomotive to attach it to another train. It is therefore
impossible to know what acceleration such a force, applied to such a body,
would impress upon such another body, if it were applied to it. It is

impossible to know how two forces which are not directly opposed would
act, if they were directly opposed.
It is this definition we try to materialize, so to speak, when we measure a
force with a dynamometer, or in balancing it with a weight. Two forces F
and F´, which for simplicity I will suppose vertical and directed upward, are
applied respectively to two bodies C and C´; I suspend the same heavy body
P first to the body C, then to the body C´; if equilibrium is produced in both
cases, I shall conclude that the two forces F and F´ are equal to one another,
since they are each equal to the weight of the body P.
But am I sure the body P has retained the same weight when I have
transported it from the first body to the second? Far from it; I am sure of the
contrary; I know the intensity of gravity varies from one point to another,
and that it is stronger, for instance, at the pole than at the equator. No doubt
the difference is very slight and, in practise, I shall take no account of it; but
a properly constructed definition should have mathematical rigor; this rigor
is lacking. What I say of weight would evidently apply to the force of the
resiliency of a dynamometer, which the temperature and a multitude of
circumstances may cause to vary.
This is not all; we can not say the weight of the body P may be applied to
the body C and directly balance the force F. What is applied to the body C
is the action A of the body P on the body C; the body P is submitted on its
part, on the one hand, to its weight; on the other hand, to the reaction R of
the body C on P. Finally, the force F is equal to the force A, since it
balances it; the force A is equal to R, in virtue of the principle of the
equality of action and reaction; lastly, the force R is equal to the weight of
P, since it balances it. It is from these three equalities we deduce as
consequence the equality of F and the weight of P.
We are therefore obliged in the definition of the equality of the two
forces to bring in the principle of the equality of action and reaction; on this
account, this principle must no longer be regarded as an experimental law,
but as a definition.
For recognizing the equality of two forces here, we are then in possession
of two rules: equality of two forces which balance; equality of action and
reaction. But, as we have seen above, these two rules are insufficient; we

are obliged to have recourse to a third rule and to assume that certain forces,
as, for instance, the weight of a body, are constant in magnitude and
direction. But this third rule, as I have said, is an experimental law; it is
only approximately true; it is a bad definition.
We are therefore reduced to Kirchhoff's definition; force is equal to the
mass multiplied by the acceleration. This 'law of Newton' in its turn ceases
to be regarded as an experimental law, it is now only a definition. But this
definition is still insufficient, for we do not know what mass is. It enables us
doubtless to calculate the relation of two forces applied to the same body at
different instants; it teaches us nothing about the relation of two forces
applied to two different bodies.
To complete it, it is necessary to go back anew to Newton's third law
(equality of action and reaction), regarded again, not as an experimental
law, but as a definition. Two bodies A and B act one upon the other; the
acceleration of A multiplied by the mass of A is equal to the action of B
upon A; in the same way, the product of the acceleration of B by its mass is
equal to the reaction of A upon B. As, by definition, action is equal to
reaction, the masses of A and B are in the inverse ratio of their
accelerations. Here we have the ratio of these two masses defined, and it is
for experiment to verify that this ratio is constant.
That would be all very well if the two bodies A and B alone were present
and removed from the action of the rest of the world. This is not at all the
case; the acceleration of A is not due merely to the action of B, but to that of
a multitude of other bodies C, D,... To apply the preceding rule, it is
therefore necessary to separate the acceleration of A into many components,
and discern which of these components is due to the action of B.
This separation would still be possible, if we should assume that the
action of C upon A is simply adjoined to that of B upon A, without the
presence of the body C modifying the action of B upon A; or the presence of
B modifying the action of C upon A; if we should assume, consequently,
that any two bodies attract each other, that their mutual action is along their
join and depends only upon their distance apart; if, in a word, we assume
the hypothesis of central forces.

You know that to determine the masses of the celestial bodies we use a
wholly different principle. The law of gravitation teaches us that the
attraction of two bodies is proportional to their masses; if r is their distance
apart, m and m´ their masses, k a constant, their attraction will be kmm´/r2.
What we are measuring then is not mass, the ratio of force to
acceleration, but the attracting mass; it is not the inertia of the body, but its
attracting force.
This is an indirect procedure, whose employment is not theoretically
indispensable. It might very well have been that attraction was inversely
proportional to the square of the distance without being proportional to the
product of the masses, that it was equal to f/r2, but without our having f =
kmm´.
If it were so, we could nevertheless, by observation of the relative
motions of the heavenly bodies, measure the masses of these bodies.
But have we the right to admit the hypothesis of central forces? Is this
hypothesis rigorously exact? Is it certain it will never be contradicted by
experiment? Who would dare affirm that? And if we must abandon this
hypothesis, the whole edifice so laboriously erected will crumble.
We have no longer the right to speak of the component of the
acceleration of A due to the action of B. We have no means of
distinguishing it from that due to the action of C or of another body. The
rule for the measurement of masses becomes inapplicable.
What remains then of the principle of the equality of action and reaction?
If the hypothesis of central forces is rejected, this principle should evidently
be enunciated thus: the geometric resultant of all the forces applied to the
various bodies of a system isolated from all external action will be null. Or,
in other words, the motion of the center of gravity of this system will be
rectilinear and uniform.
There it seems we have a means of defining mass; the position of the
center of gravity evidently depends on the values attributed to the masses; it
will be necessary to dispose of these values in such a way that the motion of
the center of gravity may be rectilinear and uniform; this will always be

possible if Newton's third law is true, and possible in general only in a
single way.
But there exists no system isolated from all external action; all the parts
of the universe are subject more or less to the action of all the other parts.
The law of the motion of the center of gravity is rigorously true only if
applied to the entire universe.
But then, to get from it the values of the masses, it would be necessary to
observe the motion of the center of gravity of the universe. The absurdity of
this consequence is manifest; we know only relative motions; the motion of
the center of gravity of the universe will remain for us eternally unknown.
Therefore nothing remains and our efforts have been fruitless; we are
driven to the following definition, which is only an avowal of
powerlessness: masses are coefficients it is convenient to introduce into
calculations.
We could reconstruct all mechanics by attributing different values to all
the masses. This new mechanics would not be in contradiction either with
experience or with the general principles of dynamics (principle of inertia,
proportionality of forces to masses and to accelerations, equality of action
and reaction, rectilinear and uniform motion of the center of gravity,
principle of areas).
Only the equations of this new mechanics would be less simple. Let us
understand clearly: it would only be the first terms which would be less
simple, that is those experience has already made us acquainted with;
perhaps one could alter the masses by small quantities without the complete
equations gaining or losing in simplicity.
Hertz has raised the question whether the principles of mechanics are
rigorously true. "In the opinion of many physicists," he says, "it is
inconceivable that the remotest experience should ever change anything in
the immovable principles of mechanics; and yet, what comes from
experience may always be rectified by experience." After what we have just
said, these fears will appear groundless.
The principles of dynamics at first appeared to us as experimental truths;
but we have been obliged to use them as definitions. It is by definition that

force is equal to the product of mass by acceleration; here, then, is a
principle which is henceforth beyond the reach of any further experiment. It
is in the same way by definition that action is equal to reaction.
But then, it will be said, these unverifiable principles are absolutely
devoid of any significance; experiment can not contradict them; but they
can teach us nothing useful; then what is the use of studying dynamics?
This over-hasty condemnation would be unjust. There is not in nature any
system perfectly isolated, perfectly removed from all external action; but
there are systems almost isolated.
If such a system be observed, one may study not only the relative motion
of its various parts one in reference to another, but also the motion of its
center of gravity in reference to the other parts of the universe. We ascertain
then that the motion of this center of gravity is almost rectilinear and
uniform, in conformity with Newton's third law.
That is an experimental truth, but it can not be invalidated by experience;
in fact, what would a more precise experiment teach us? It would teach us
that the law was only almost true; but that we knew already.
We can now understand how experience has been able to serve as basis
for the principles of mechanics and yet will never be able to contradict
them.
Anthropomorphic Mechanics.—"Kirchhoff," it will be said, "has only
acted in obedience to the general tendency of mathematicians toward
nominalism; from this his ability as a physicist has not saved him. He
wanted a definition of force, and he took for it the first proposition that
presented itself; but we need no definition of force: the idea of force is
primitive, irreducible, indefinable; we all know what it is, we have a direct
intuition of it. This direct intuition comes from the notion of effort, which is
familiar to us from infancy."
But first, even though this direct intuition made known to us the real
nature of force in itself, it would be insufficient as a foundation for
mechanics; it would besides be wholly useless. What is of importance is not
to know what force is, but to know how to measure it.

Whatever does not teach us to measure it is as useless to mechanics as is,
for instance, the subjective notion of warmth and cold to the physicist who
is studying heat. This subjective notion can not be translated into numbers,
therefore it is of no use; a scientist whose skin was an absolutely bad
conductor of heat and who, consequently, would never have felt either
sensations of cold or sensations of warmth, could read a thermometer just as
well as any one else, and that would suffice him for constructing the whole
theory of heat.
Now this immediate notion of effort is of no use to us for measuring
force; it is clear, for instance, that I should feel more fatigue in lifting a
weight of fifty kilos than a man accustomed to carry burdens.
But more than that: this notion of effort does not teach us the real nature
of force; it reduces itself finally to a remembrance of muscular sensations,
and it will hardly be maintained that the sun feels a muscular sensation
when it draws the earth.
All that can there be sought is a symbol, less precise and less convenient
than the arrows the geometers use, but just as remote from the reality.
Anthropomorphism has played a considerable historic rôle in the genesis
of mechanics; perhaps it will still at times furnish a symbol which will
appear convenient to some minds; but it can not serve as foundation for
anything of a truly scientific or philosophic character.
'The School of the Thread.'—M. Andrade, in his Leçons de mécanique
physique, has rejuvenated anthropomorphic mechanics. To the school of
mechanics to which Kirchhoff belongs, he opposes that which he bizarrely
calls the school of the thread.
This school tries to reduce everything to "the consideration of certain
material systems of negligible mass, envisaged in the state of tension and
capable of transmitting considerable efforts to distant bodies, systems of
which the ideal type is the thread."
A thread which transmits any force is slightly elongated under the action
of this force; the direction of the thread tells us the direction of the force,
whose magnitude is measured by the elongation of the thread.

One may then conceive an experiment such as this. A body A is attached
to a thread; at the other extremity of the thread any force acts which varies
until the thread takes an elongation α; the acceleration of the body A is
noted; A is detached and the body B attached to the same thread; the same
force or another force acts anew, and is made to vary until the thread takes
again the elongation α; the acceleration of the body B is noted. The
experiment is then renewed with both A and B, but so that the thread takes
the elongation ßβ. The four observed accelerations should be proportional.
We have thus an experimental verification of the law of acceleration above
enunciated.
Or still better, a body is submitted to the simultaneous action of several
identical threads in equal tension, and by experiment it is sought what must
be the orientations of all these threads that the body may remain in
equilibrium. We have then an experimental verification of the law of the
composition of forces.
But, after all, what have we done? We have defined the force to which
the thread is subjected by the deformation undergone by this thread, which
is reasonable enough; we have further assumed that if a body is attached to
this thread, the effort transmitted to it by the thread is equal to the action
this body exercises on this thread; after all, we have therefore used the
principle of the equality of action and reaction, in considering it, not as an
experimental truth, but as the very definition of force.
This definition is just as conventional as Kirchhoff's, but far less general.
All forces are not transmitted by threads (besides, to be able to compare
them, they would all have to be transmitted by identical threads). Even if it
should be conceded that the earth is attached to the sun by some invisible
thread, at least it would be admitted that we have no means of measuring its
elongation.
Nine times out of ten, consequently, our definition would be at fault; no
sort of sense could be attributed to it, and it would be necessary to fall back
on Kirchhoff's.
Why then take this détour? You admit a certain definition of force which
has a meaning only in certain particular cases. In these cases you verify by

experiment that it leads to the law of acceleration. On the strength of this
experiment, you then take the law of acceleration as a definition of force in
all the other cases.
Would it not be simpler to consider the law of acceleration as a definition
in all cases, and to regard the experiments in question, not as verifications
of this law, but as verifications of the principle of reaction, or as
demonstrating that the deformations of an elastic body depend only on the
forces to which this body is subjected?
And this is without taking into account that the conditions under which
your definition could be accepted are never fulfilled except imperfectly, that
a thread is never without mass, that it is never removed from every force
except the reaction of the bodies attached to its extremities.
Andrade's ideas are nevertheless very interesting; if they do not satisfy
our logical craving, they make us understand better the historic genesis of
the fundamental ideas of mechanics. The reflections they suggest show us
how the human mind has raised itself from a naïve anthropomorphism to
the present conceptions of science.
We see at the start a very particular and in sum rather crude experiment;
at the finish, a law perfectly general, perfectly precise, the certainty of
which we regard as absolute. This certainty we ourselves have bestowed
upon it voluntarily, so to speak, by looking upon it as a convention.
Are the law of acceleration, the rule of the composition of forces then
only arbitrary conventions? Conventions, yes; arbitrary, no; they would be
if we lost sight of the experiments which led the creators of the science to
adopt them, and which, imperfect as they may be, suffice to justify them. It
is well that from time to time our attention is carried back to the
experimental origin of these conventions.

CHAPTER VII

Relative Motion and Absolute Motion

The Principle of Relative Motion.—The attempt has sometimes been
made to attach the law of acceleration to a more general principle. The
motion of any system must obey the same laws, whether it be referred to
fixed axes, or to movable axes carried along in a rectilinear and uniform
motion. This is the principle of relative motion, which forces itself upon us
for two reasons: first, the commonest experience confirms it, and second,
the contrary hypothesis is singularly repugnant to the mind.
Assume it then, and consider a body subjected to a force; the relative
motion of this body, in reference to an observer moving with a uniform
velocity equal to the initial velocity of the body, must be identical to what
its absolute motion would be if it started from rest. We conclude hence that
its acceleration can not depend upon its absolute velocity; the attempt has
even been made to derive from this a demonstration of the law of
acceleration.
There long were traces of this demonstration in the regulations for the
degree B. ès Sc. It is evident that this attempt is idle. The obstacle which
prevented our demonstrating the law of acceleration is that we had no
definition of force; this obstacle subsists in its entirety, since the principle
invoked has not furnished us the definition we lacked.
The principle of relative motion is none the less highly interesting and
deserves study for its own sake. Let us first try to enunciate it in a precise
manner.
We have said above that the accelerations of the different bodies forming
part of an isolated system depend only on their relative velocities and
positions, and not on their absolute velocities and positions, provided the
movable axes to which the relative motion is referred move uniformly in a
straight line. Or, if we prefer, their accelerations depend only on the
differences of their velocities and the differences of their coordinates, and
not on the absolute values of these velocities and coordinates.
If this principle is true for relative accelerations, or rather for differences
of acceleration, in combining it with the law of reaction we shall thence
deduce that it is still true of absolute accelerations.

It then remains to be seen how we may demonstrate that the differences
of the accelerations depend only on the differences of the velocities and of
the coordinates, or, to speak in mathematical language, that these
differences of coordinates satisfy differential equations of the second order.
Can this demonstration be deduced from experiments or from a priori
considerations?
Recalling what we have said above, the reader can answer for himself.
Thus enunciated, in fact, the principle of relative motion singularly
resembles what I called above the generalized principle of inertia; it is not
altogether the same thing, since it is a question of the differences of
coordinates and not of the coordinates themselves. The new principle
teaches us therefore something more than the old, but the same discussion is
applicable and would lead to the same conclusions; it is unnecessary to
return to it.
Newton's Argument.—Here we encounter a very important and even
somewhat disconcerting question. I have said the principle of relative
motion was for us not solely a result of experiment and that a priori every
contrary hypothesis would be repugnant to the mind.
But then, why is the principle true only if the motion of the movable axes
is rectilinear and uniform? It seems that it ought to impose itself upon us
with the same force, if this motion is varied, or at any rate if it reduces to a
uniform rotation. Now, in these two cases, the principle is not true. I will
not dwell long on the case where the motion of the axes is rectilinear
without being uniform; the paradox does not bear a moment's examination.
If I am on board, and if the train, striking any obstacle, stops suddenly, I
shall be thrown against the seat in front of me, although I have not been
directly subjected to any force. There is nothing mysterious in that; if I have
undergone the action of no external force, the train itself has experienced an
external impact. There can be nothing paradoxical in the relative motion of
two bodies being disturbed when the motion of one or the other is modified
by an external cause.
I will pause longer on the case of relative motions referred to axes which
rotate uniformly. If the heavens were always covered with clouds, if we had

no means of observing the stars, we nevertheless might conclude that the
earth turns round; we could learn this from its flattening or again by the
Foucault pendulum experiment.
And yet, in this case, would it have any meaning, to say the earth turns
round? If there is no absolute space, can one turn without turning in
reference to something else? and, on the other hand, how could we admit
Newton's conclusion and believe in absolute space?
But it does not suffice to ascertain that all possible solutions are equally
repugnant to us; we must analyze, in each case, the reasons for our
repugnance, so as to make our choice intelligently. The long discussion
which follows will therefore be excused.
Let us resume our fiction: thick clouds hide the stars from men, who can
not observe them and are ignorant even of their existence; how shall these
men know the earth turns round?
Even more than our ancestors, no doubt, they will regard the ground
which bears them as fixed and immovable; they will await much longer the
advent of a Copernicus. But in the end the Copernicus would come—how?
The students of mechanics in this world would not at first be confronted
with an absolute contradiction. In the theory of relative motion, besides real
forces, two fictitious forces are met which are called ordinary and
compound centrifugal force. Our imaginary scientists could therefore
explain everything by regarding these two forces as real, and they would
not see therein any contradiction of the generalized principle of inertia, for
these forces would depend, the one on the relative positions of the various
parts of the system, as real attractions do, the other on their relative
velocities, as real frictions do.
Many difficulties, however, would soon awaken their attention; if they
succeeded in realizing an isolated system, the center of gravity of this
system would not have an almost rectilinear path. They would invoke, to
explain this fact, the centrifugal forces which they would regard as real, and
which they would attribute no doubt to the mutual actions of the bodies.
Only they would not see these forces become null at great distances, that is

to say in proportion as the isolation was better realized; far from it;
centrifugal force increases indefinitely with the distance.
This difficulty would seem to them already sufficiently great; and yet it
would not stop them long; they would soon imagine some very subtile
medium, analogous to our ether, in which all bodies would be immersed
and which would exert a repellent action upon them.
But this is not all. Space is symmetric, and yet the laws of motion would
not show any symmetry; they would have to distinguish between right and
left. It would be seen for instance that cyclones turn always in the same
sense, whereas by reason of symmetry these winds should turn indifferently
in one sense and in the other. If our scientists by their labor had succeeded
in rendering their universe perfectly symmetric, this symmetry would not
remain, even though there was no apparent reason why it should be
disturbed in one sense rather than in the other.
They would get themselves out of the difficulty doubtless, they would
invent something which would be no more extraordinary than the glass
spheres of Ptolemy, and so it would go on, complications accumulating,
until the long-expected Copernicus sweeps them all away at a single stroke,
saying: It is much simpler to assume the earth turns round.
And just as our Copernicus said to us: It is more convenient to suppose
the earth turns round, since thus the laws of astronomy are expressible in a
much simpler language; this one would say: It is more convenient to
suppose the earth turns round, since thus the laws of mechanics are
expressible in a much simpler language.
This does not preclude maintaining that absolute space, that is to say the
mark to which it would be necessary to refer the earth to know whether it
really moves, has no objective existence. Hence, this affirmation: 'the earth
turns round' has no meaning, since it can be verified by no experiment;
since such an experiment, not only could not be either realized or dreamed
by the boldest Jules Verne, but can not be conceived of without
contradiction; or rather these two propositions: 'the earth turns round,' and,
'it is more convenient to suppose the earth turns round' have the same
meaning; there is nothing more in the one than in the other.

Perhaps one will not be content even with that, and will find it already
shocking that among all the hypotheses, or rather all the conventions we can
make on this subject, there is one more convenient than the others.
But if it has been admitted without difficulty when it was a question of
the laws of astronomy, why should it be shocking in that which concerns
mechanics?
We have seen that the coordinates of bodies are determined by
differential equations of the second order, and that so are the differences of
these coordinates. This is what we have called the generalized principle of
inertia and the principle of relative motion. If the distances of these bodies
were determined likewise by equations of the second order, it seems that the
mind ought to be entirely satisfied. In what measure does the mind get this
satisfaction and why is it not content with it?
To account for this, we had better take a simple example. I suppose a
system analogous to our solar system, but where one can not perceive fixed
stars foreign to this system, so that astronomers can observe only the mutual
distances of the planets and the sun, and not the absolute longitudes of the
planets. If we deduce directly from Newton's law the differential equations
which define the variation of these distances, these equations will not be of
the second order. I mean that if, besides Newton's law, one knew the initial
values of these distances and of their derivatives with respect to the time,
that would not suffice to determine the values of these same distances at a
subsequent instant. There would still be lacking one datum, and this datum
might be for instance what astronomers call the area-constant.
But here two different points of view may be taken; we may distinguish
two sorts of constants. To the eyes of the physicist the world reduces to a
series of phenomena, depending, on the one hand, solely upon the initial
phenomena; on the other hand, upon the laws which bind the consequents to
the antecedents. If then observation teaches us that a certain quantity is a
constant, we shall have the choice between two conceptions.
Either we shall assume that there is a law requiring this quantity not to
vary, but that by chance, at the beginning of the ages, it had, rather than
another, this value it has been forced to keep ever since. This quantity might
then be called an accidental constant.

Or else we shall assume, on the contrary, that there is a law of nature
which imposes upon this quantity such a value and not such another.
We shall then have what we may call an essential constant.
For example, in virtue of Newton's laws, the duration of the revolution of
the earth must be constant. But if it is 366 sidereal days and something over,
and not 300 or 400, this is in consequence of I know not what initial chance.
This is an accidental constant. If, on the contrary, the exponent of the
distance which figures in the expression of the attractive force is equal to −2
and not to −3, this is not by chance, but because Newton's law requires it.
This is an essential constant.
I know not whether this way of giving chance its part is legitimate in
itself, and whether this distinction is not somewhat artificial; it is certain at
least that, so long as nature shall have secrets, this distinction will be in
application extremely arbitrary and always precarious.
As to the area-constant, we are accustomed to regard it as accidental. Is it
certain our imaginary astronomers would do the same? If they could have
compared two different solar systems, they would have the idea that this
constant may have several different values; but my very supposition in the
beginning was that their system should appear as isolated, and that they
should observe no star foreign to it. Under these conditions, they would see
only one single constant which would have a single value absolutely
invariable; they would be led without any doubt to regard it as an essential
constant.
A word in passing to forestall an objection: the inhabitants of this
imaginary world could neither observe nor define the area-constant as we
do, since the absolute longitudes escape them; that would not preclude their
being quickly led to notice a certain constant which would introduce itself
naturally into their equations and which would be nothing but what we call
the area-constant.
But then see what would happen. If the area-constant is regarded as
essential, as depending upon a law of nature, to calculate the distances of
the planets at any instant it will suffice to know the initial values of these
distances and those of their first derivatives. From this new point of view,

the distances will be determined by differential equations of the second
order.
Yet would the mind of these astronomers be completely satisfied? I do
not believe so; first, they would soon perceive that in differentiating their
equations and thus raising their order, these equations became much
simpler. And above all they would be struck by the difficulty which comes
from symmetry. It would be necessary to assume different laws, according
as the aggregate of the planets presented the figure of a certain polyhedron
or of the symmetric polyhedron, and one would escape from this
consequence only by regarding the area-constant as accidental.
I have taken a very special example, since I have supposed astronomers
who did not at all consider terrestrial mechanics, and whose view was
limited to the solar system. Our universe is more extended than theirs, as we
have fixed stars, but still it too is limited, and so we might reason on the
totality of our universe as the astronomers on their solar system.
Thus we see that finally we should be led to conclude that the equations
which define distances are of an order superior to the second. Why should
we be shocked at that, why do we find it perfectly natural for the series of
phenomena to depend upon the initial values of the first derivatives of these
distances, while we hesitate to admit that they may depend on the initial
values of the second derivatives? This can only be because of the habits of
mind created in us by the constant study of the generalized principle of
inertia and its consequences.
The values of the distances at any instant depend upon their initial values,
upon those of their first derivatives and also upon something else. What is
this something else?
If we will not admit that this may be simply one of the second
derivatives, we have only the choice of hypotheses. Either it may be
supposed, as is ordinarily done, that this something else is the absolute
orientation of the universe in space, or the rapidity with which this
orientation varies; and this supposition may be correct; it is certainly the
most convenient solution for geometry; it is not the most satisfactory for the
philosopher, because this orientation does not exist.

Or it may be supposed that this something else is the position or the
velocity of some invisible body; this has been done by certain persons who
have even called it the body alpha, although we are doomed never to know
anything of this body but its name. This is an artifice entirely analogous to
that of which I spoke at the end of the paragraph devoted to my reflections
on the principle of inertia.
But, after all, the difficulty is artificial. Provided the future indications of
our instruments can depend only on the indications they have given us or
would have given us formerly, this is all that is necessary. Now as to this we
may rest easy.

CHAPTER VIII

Energy and Thermodynamics
Energetics.—The difficulties inherent in the classic mechanics have led
certain minds to prefer a new system they call energetics.
Energetics took its rise as an outcome of the discovery of the principle of
the conservation of energy. Helmholtz gave it its final form.
It begins by defining two quantities which play the fundamental rôle in
this theory. They are kinetic energy, or vis viva, and potential energy.
All the changes which bodies in nature can undergo are regulated by two
experimental laws:
1º The sum of kinetic energy and potential energy is constant. This is the
principle of the conservation of energy.
2º If a system of bodies is at A at the time t0 and at B at the time t1, it
always goes from the first situation to the second in such a way that the
mean value of the difference between the two sorts of energy, in the interval
of time which separates the two epochs t0 and t1, may be as small as
possible.

This is Hamilton's principle, which is one of the forms of the principle of
least action.
The energetic theory has the following advantages over the classic
theory:
1º It is less incomplete; that is to say, Hamilton's principle and that of the
conservation of energy teach us more than the fundamental principles of the
classic theory, and exclude certain motions not realized in nature and which
would be compatible with the classic theory:
2º It saves us the hypothesis of atoms, which it was almost impossible to
avoid with the classic theory.
But it raises in its turn new difficulties:
The definitions of the two sorts of energy would raise difficulties almost
as great as those of force and mass in the first system. Yet they may be
gotten over more easily, at least in the simplest cases.
Suppose an isolated system formed of a certain number of material
points; suppose these points subjected to forces depending only on their
relative position and their mutual distances, and independent of their
velocities. In virtue of the principle of the conservation of energy, a function
of forces must exist.
In this simple case the enunciation of the principle of the conservation of
energy is of extreme simplicity. A certain quantity, accessible to experiment,
must remain constant. This quantity is the sum of two terms; the first
depends only on the position of the material points and is independent of
their velocities; the second is proportional to the square of these velocities.
This resolution can take place only in a single way.
The first of these terms, which I shall call U, will be the potential energy;
the second, which I shall call T, will be the kinetic energy.
It is true that if T + U is a constant, so is any function of T + U,
Φ (T + U).

But this function Φ (T + U) will not be the sum of two terms the one
independent of the velocities, the other proportional to the square of these
velocities. Among the functions which remain constant there is only one
which enjoys this property, that is T + U (or a linear function of T + U,
which comes to the same thing, since this linear function may always be
reduced to T + U by change of unit and of origin). This then is what we
shall call energy; the first term we shall call potential energy and the second
kinetic energy. The definition of the two sorts of energy can therefore be
carried through without any ambiguity.
It is the same with the definition of the masses. Kinetic energy, or vis
viva, is expressed very simply by the aid of the masses and the relative
velocities of all the material points with reference to one of them. These
relative velocities are accessible to observation, and, when we know the
expression of the kinetic energy as function of these relative velocities, the
coefficients of this expression will give us the masses.
Thus, in this simple case, the fundamental ideas may be defined without
difficulty. But the difficulties reappear in the more complicated cases and,
for instance, if the forces, in lieu of depending only on the distances,
depend also on the velocities. For example, Weber supposes the mutual
action of two electric molecules to depend not only on their distance, but on
their velocity and their acceleration. If material points should attract each
other according to an analogous law, U would depend on the velocity, and
might contain a term proportional to the square of the velocity.
Among the terms proportional to the squares of the velocities, how
distinguish those which come from T or from U? Consequently, how
distinguish the two parts of energy?
But still more; how define energy itself? We no longer have any reason to
take as definition T + U rather than any other function of T + U, when the
property which characterized T + U has disappeared, that, namely, of being
the sum of two terms of a particular form.
But this is not all; it is necessary to take account, not only of mechanical
energy properly so called, but of the other forms of energy, heat, chemical
energy, electric energy, etc. The principle of the conservation of energy
should be written:

T + U + Q = const.
where T would represent the sensible kinetic energy, U the potential energy
of position, depending only on the position of the bodies, Q the internal
molecular energy, under the thermal, chemic or electric form.
All would go well if these three terms were absolutely distinct, if T were
proportional to the square of the velocities, U independent of these
velocities and of the state of the bodies, Q independent of the velocities and
of the positions of the bodies and dependent only on their internal state.
The expression for the energy could be resolved only in one single way
into three terms of this form.
But this is not the case; consider electrified bodies; the electrostatic
energy due to their mutual action will evidently depend upon their charge,
that is to say, on their state; but it will equally depend upon their position. If
these bodies are in motion, they will act one upon another
electrodynamically and the electrodynamic energy will depend not only
upon their state and their position, but upon their velocities.
We therefore no longer have any means of making the separation of the
terms which should make part of T, of U and of Q, and of separating the
three parts of energy.
If (T + U + Q) is constant so is any function Φ (T + U + Q).
If T + U + Q were of the particular form I have above considered, no
ambiguity would result; among the functions Φ (T + U + Q) which remain
constant, there would only be one of this particular form, and that I should
convene to call energy.
But as I have said, this is not rigorously the case; among the functions
which remain constant, there is none which can be put rigorously under this
particular form; hence, how choose among them the one which should be
called energy? We no longer have anything to guide us in our choice.
There only remains for us one enunciation of the principle of the
conservation of energy: There is something which remains constant. Under
this form it is in its turn out of the reach of experiment and reduces to a sort

of tautology. It is clear that if the world is governed by laws, there will be
quantities which will remain constant. Like Newton's laws, and, for an
analogous reason, the principle of the conservation of energy, founded on
experiment, could no longer be invalidated by it.
This discussion shows that in passing from the classic to the energetic
system progress has been made; but at the same time it shows this progress
is insufficient.
Another objection seems to me still more grave: the principle of least
action is applicable to reversible phenomena; but it is not at all satisfactory
in so far as irreversible phenomena are concerned; the attempt by
Helmholtz to extend it to this kind of phenomena did not succeed and could
not succeed; in this regard everything remains to be done. The very
statement of the principle of least action has something about it repugnant
to the mind. To go from one point to another, a material molecule, acted
upon by no force, but required to move on a surface, will take the geodesic
line, that is to say, the shortest path.
This molecule seems to know the point whither it is to go, to foresee the
time it would take to reach it by such and such a route, and then to choose
the most suitable path. The statement presents the molecule to us, so to
speak, as a living and free being. Clearly it would be better to replace it by
an enunciation less objectionable, and where, as the philosophers would
say, final causes would not seem to be substituted for efficient causes.

Thermodynamics.[4]—The rôle of the two fundamental principles of
thermodynamics in all branches of natural philosophy becomes daily more
important. Abandoning the ambitious theories of forty years ago, which
were encumbered by molecular hypotheses, we are trying to-day to erect
upon thermodynamics alone the entire edifice of mathematical physics. Will
the two principles of Mayer and of Clausius assure to it foundations solid
enough for it to last some time? No one doubts it; but whence comes this
confidence?
An eminent physicist said to me one day à propos of the law of errors:
"All the world believes it firmly, because the mathematicians imagine that it
is a fact of observation, and the observers that it is a theorem of

mathematics." It was long so for the principle of the conservation of energy.
It is no longer so to-day; no one is ignorant that this is an experimental fact.
But then what gives us the right to attribute to the principle itself more
generality and more precision than to the experiments which have served to
demonstrate it? This is to ask whether it is legitimate, as is done every day,
to generalize empirical data, and I shall not have the presumption to discuss
this question, after so many philosophers have vainly striven to solve it.
One thing is certain; if this power were denied us, science could not exist
or, at least, reduced to a sort of inventory, to the ascertaining of isolated
facts, it would have no value for us, since it could give no satisfaction to our
craving for order and harmony and since it would be at the same time
incapable of foreseeing. As the circumstances which have preceded any fact
will probably never be simultaneously reproduced, a first generalization is
already necessary to foresee whether this fact will be reproduced again after
the least of these circumstances shall be changed.
But every proposition may be generalized in an infinity of ways. Among
all the generalizations possible, we must choose, and we can only choose
the simplest. We are therefore led to act as if a simple law were, other things
being equal, more probable than a complicated law.
Half a century ago this was frankly confessed, and it was proclaimed that
nature loves simplicity; she has since too often given us the lie. To-day we
no longer confess this tendency, and we retain only so much of it as is
indispensable if science is not to become impossible.
In formulating a general, simple and precise law on the basis of
experiments relatively few and presenting certain divergences, we have
therefore only obeyed a necessity from which the human mind can not free
itself.
But there is something more, and this is why I dwell upon the point.
No one doubts that Mayer's principle is destined to survive all the
particular laws from which it was obtained, just as Newton's law has
survived Kepler's laws, from which it sprang, and which are only
approximative if account be taken of perturbations.

Why does this principle occupy thus a sort of privileged place among all
the physical laws? There are many little reasons for it.
First of all it is believed that we could not reject it or even doubt its
absolute rigor without admitting the possibility of perpetual motion; of
course we are on our guard at such a prospect, and we think ourselves less
rash in affirming Mayer's principle than in denying it.
That is perhaps not wholly accurate; the impossibility of perpetual
motion implies the conservation of energy only for reversible phenomena.
The imposing simplicity of Mayer's principle likewise contributes to
strengthen our faith. In a law deduced immediately from experiment, like
Mariotte's, this simplicity would rather seem to us a reason for distrust; but
here this is no longer the case; we see elements, at first sight disparate,
arrange themselves in an unexpected order and form a harmonious whole;
and we refuse to believe that an unforeseen harmony may be a simple effect
of chance. It seems that our conquest is the dearer to us the more effort it
has cost us, or that we are the surer of having wrested her true secret from
nature the more jealously she has hidden it from us.
But those are only little reasons; to establish Mayer's law as an absolute
principle, a more profound discussion is necessary. But if this be attempted,
it is seen that this absolute principle is not even easy to state.
In each particular case it is clearly seen what energy is and at least a
provisional definition of it can be given; but it is impossible to find a
general definition for it.
If we try to enunciate the principle in all its generality and apply it to the
universe, we see it vanish, so to speak, and nothing is left but this: There is
something which remains constant.
But has even this any meaning? In the determinist hypothesis, the state of
the universe is determined by an extremely great number n of parameters
which I shall call x1, x2, ... xn. As soon as the values of these n parameters at
any instant are known, their derivatives with respect to the time are likewise
known and consequently the values of these same parameters at a preceding

or subsequent instant can be calculated. In other words, these n parameters
satisfy n differential equations of the first order.
These equations admit of n − 1 integrals and consequently there are n − 1
functions of x1, x2,... xn, which remain constant. If then we say there is
something which remains constant, we only utter a tautology. We should
even be puzzled to say which among all our integrals should retain the
name of energy.
Besides, Mayer's principle is not understood in this sense when it is
applied to a limited system. It is then assumed that p of our parameters vary
independently, so that we only have n − p relations, generally linear,
between our n parameters and their derivatives.
To simplify the enunciation, suppose that the sum of the work of the
external forces is null, as well as that of the quantities of heat given off to
the outside. Then the signification of our principle will be:
There is a combination of these n − p relations whose first member is an
exact differential; and then this differential vanishing in virtue of our n − p
relations, its integral is a constant and this integral is called energy.
But how can it be possible that there are several parameters whose
variations are independent? That can only happen under the influence of
external forces (although we have supposed, for simplicity, that the
algebraic sum of the effects of these forces is null). In fact, if the system
were completely isolated from all external action, the values of our n
parameters at a given instant would suffice to determine the state of the
system at any subsequent instant, provided always we retain the determinist
hypothesis; we come back therefore to the same difficulty as above.
If the future state of the system is not entirely determined by its present
state, this is because it depends besides upon the state of bodies external to
the system. But then is it probable that there exist between the parameters
xi, which define the state of the system, equations independent of this state
of the external bodies? and if in certain cases we believe we can find such,
is this not solely in consequence of our ignorance and because the influence
of these bodies is too slight for our experimenting to detect it?

If the system is not regarded as completely isolated, it is probable that the
rigorously exact expression of its internal energy will depend on the state of
the external bodies. Again, I have above supposed the sum of the external
work was null, and if we try to free ourselves from this rather artificial
restriction, the enunciation becomes still more difficult.
To formulate Mayer's principle in an absolute sense, it is therefore
necessary to extend it to the whole universe, and then we find ourselves
face to face with the very difficulty we sought to avoid.
In conclusion, using ordinary language, the law of the conservation of
energy can have only one signification, which is that there is a property
common to all the possibilities; but on the determinist hypothesis there is
only a single possibility, and then the law has no longer any meaning.
On the indeterminist hypothesis, on the contrary, it would have a
meaning, even if it were taken in an absolute sense; it would appear as a
limitation imposed upon freedom.
But this word reminds me that I am digressing and am on the point of
leaving the domain of mathematics and physics. I check myself therefore
and will stress of all this discussion only one impression, that Mayer's law
is a form flexible enough for us to put into it almost whatever we wish. By
that I do not mean it corresponds to no objective reality, nor that it reduces
itself to a mere tautology, since, in each particular case, and provided one
does not try to push to the absolute, it has a perfectly clear meaning.
This flexibility is a reason for believing in its permanence, and as, on the
other hand, it will disappear only to lose itself in a higher harmony, we may
work with confidence, supporting ourselves upon it, certain beforehand that
our labor will not be lost.
Almost everything I have just said applies to the principle of Clausius.
What distinguishes it is that it is expressed by an inequality. Perhaps it will
be said it is the same with all physical laws, since their precision is always
limited by errors of observation. But they at least claim to be first
approximations, and it is hoped to replace them little by little by laws more
and more precise. If, on the other hand, the principle of Clausius reduces to

an inequality, this is not caused by the imperfection of our means of
observation, but by the very nature of the question.

General Conclusions on Part Third
The principles of mechanics, then, present themselves to us under two
different aspects. On the one hand, they are truths founded on experiment
and approximately verified so far as concerns almost isolated systems. On
the other hand, they are postulates applicable to the totality of the universe
and regarded as rigorously true.
If these postulates possess a generality and a certainty which are lacking
to the experimental verities whence they are drawn, this is because they
reduce in the last analysis to a mere convention which we have the right to
make, because we are certain beforehand that no experiment can ever
contradict it.
This convention, however, is not absolutely arbitrary; it does not spring
from our caprice; we adopt it because certain experiments have shown us
that it would be convenient.
Thus is explained how experiment could make the principles of
mechanics, and yet why it can not overturn them.
Compare with geometry: The fundamental propositions of geometry, as
for instance Euclid's postulate, are nothing more than conventions, and it is
just as unreasonable to inquire whether they are true or false as to ask
whether the metric system is true or false.
Only, these conventions are convenient, and it is certain experiments
which have taught us that.
At first blush, the analogy is complete; the rôle of experiment seems the
same. One will therefore be tempted to say: Either mechanics must be
regarded as an experimental science, and then the same must hold for
geometry; or else, on the contrary, geometry is a deductive science, and
then one may say as much of mechanics.
Such a conclusion would be illegitimate. The experiments which have led
us to adopt as more convenient the fundamental conventions of geometry

bear on objects which have nothing in common with those geometry
studies; they bear on the properties of solid bodies, on the rectilinear
propagation of light. They are experiments of mechanics, experiments of
optics; they can not in any way be regarded as experiments of geometry.
And even the principal reason why our geometry seems convenient to us is
that the different parts of our body, our eye, our limbs, have the properties
of solid bodies. On this account, our fundamental experiments are
preeminently physiological experiments, which bear, not on space which is
the object the geometer must study, but on his body, that is to say, on the
instrument he must use for this study.
On the contrary, the fundamental conventions of mechanics, and the
experiments which prove to us that they are convenient, bear on exactly the
same objects or on analogous objects. The conventional and general
principles are the natural and direct generalization of the experimental and
particular principles.
Let it not be said that thus I trace artificial frontiers between the sciences;
that if I separate by a barrier geometry properly so called from the study of
solid bodies, I could just as well erect one between experimental mechanics
and the conventional mechanics of the general principles. In fact, who does
not see that in separating these two sciences I mutilate them both, and that
what will remain of conventional mechanics when it shall be isolated will
be only a very small thing and can in no way be compared to that superb
body of doctrine called geometry?
One sees now why the teaching of mechanics should remain
experimental.
Only thus can it make us comprehend the genesis of the science, and that
is indispensable for the complete understanding of the science itself.
Besides, if we study mechanics, it is to apply it; and we can apply it only
if it remains objective. Now, as we have seen, what the principles gain in
generality and certainty they lose in objectivity. It is, therefore, above all
with the objective side of the principles that we must be familiarized early,
and that can be done only by going from the particular to the general,
instead of the inverse.

The principles are conventions and disguised definitions. Yet they are
drawn from experimental laws; these laws have, so to speak, been exalted
into principles to which our mind attributes an absolute value.
Some philosophers have generalized too far; they believed the principles
were the whole science and consequently that the whole science was
conventional.
This paradoxical doctrine, called nominalism, will not bear examination.
How can a law become a principle? It expressed a relation between two
real terms A and B. But it was not rigorously true, it was only approximate.
We introduce arbitrarily an intermediary term C more or less fictitious, and
C is by definition that which has with A exactly the relation expressed by
the law.
Then our law is separated into an absolute and rigorous principle which
expresses the relation of A to C and an experimental law, approximate and
subject to revision, which expresses the relation of C to B. It is clear that,
however far this partition is pushed, some laws will always be left
remaining.
We go to enter now the domain of laws properly so called.

PART IV

NATURE

CHAPTER IX

Hypotheses in Physics
The Rôle of Experiment and Generalization.—Experiment is the sole
source of truth. It alone can teach us anything new; it alone can give us
certainty. These are two points that can not be questioned.
But then, if experiment is everything, what place will remain for
mathematical physics? What has experimental physics to do with such an
aid, one which seems useless and perhaps even dangerous?
And yet mathematical physics exists, and has done unquestionable
service. We have here a fact that must be explained.
The explanation is that merely to observe is not enough. We must use our
observations, and to do that we must generalize. This is what men always
have done; only as the memory of past errors has made them more and
more careful, they have observed more and more, and generalized less and
less.
Every age has ridiculed the one before it, and accused it of having
generalized too quickly and too naïvely. Descartes pitied the Ionians;
Descartes, in his turn, makes us smile. No doubt our children will some day
laugh at us.
But can we not then pass over immediately to the goal? Is not this the
means of escaping the ridicule that we foresee? Can we not be content with

just the bare experiment?
No, that is impossible; it would be to mistake utterly the true nature of
science. The scientist must set in order. Science is built up with facts, as a
house is with stones. But a collection of facts is no more a science than a
heap of stones is a house.
And above all the scientist must foresee. Carlyle has somewhere said
something like this: "Nothing but facts are of importance. John Lackland
passed by here. Here is something that is admirable. Here is a reality for
which I would give all the theories in the world." Carlyle was a fellow
countryman of Bacon; but Bacon would not have said that. That is the
language of the historian. The physicist would say rather: "John Lackland
passed by here; that makes no difference to me, for he never will pass this
way again."
We all know that there are good experiments and poor ones. The latter
will accumulate in vain; though one may have made a hundred or a
thousand, a single piece of work by a true master, by a Pasteur, for example,
will suffice to tumble them into oblivion. Bacon would have well
understood this; it is he who invented the phrase Experimentum crucis. But
Carlyle would not have understood it. A fact is a fact. A pupil has read a
certain number on his thermometer; he has taken no precaution; no matter,
he has read it, and if it is only the fact that counts, here is a reality of the
same rank as the peregrinations of King John Lackland. Why is the fact that
this pupil has made this reading of no interest, while the fact that a skilled
physicist had made another reading might be on the contrary very
important? It is because from the first reading we could not infer anything.
What then is a good experiment? It is that which informs us of something
besides an isolated fact; it is that which enables us to foresee, that is, that
which enables us to generalize.
For without generalization foreknowledge is impossible. The
circumstances under which one has worked will never reproduce
themselves all at once. The observed action then will never recur; the only
thing that can be affirmed is that under analogous circumstances an
analogous action will be produced. In order to foresee, then, it is necessary
to invoke at least analogy, that is to say, already then to generalize.

No matter how timid one may be, still it is necessary to interpolate.
Experiment gives us only a certain number of isolated points. We must unite
these by a continuous line. This is a veritable generalization. But we do
more; the curve that we shall trace will pass between the observed points
and near these points; it will not pass through these points themselves. Thus
one does not restrict himself to generalizing the experiments, but corrects
them; and the physicist who should try to abstain from these corrections and
really be content with the bare experiment, would be forced to enunciate
some very strange laws.
The bare facts, then, would not be enough for us; and that is why we
must have science ordered, or rather organized.
It is often said experiments must be made without a preconceived idea.
That is impossible. Not only would it make all experiment barren, but that
would be attempted which could not be done. Every one carries in his mind
his own conception of the world, of which he can not so easily rid himself.
We must, for instance, use language; and our language is made up only of
preconceived ideas and can not be otherwise. Only these are unconscious
preconceived ideas, a thousand times more dangerous than the others.
Shall we say that if we introduce others, of which we are fully conscious,
we shall only aggravate the evil? I think not. I believe rather that they will
serve as counterbalances to each other—I was going to say as antidotes;
they will in general accord ill with one another—they will come into
conflict with one another, and thereby force us to regard things under
different aspects. This is enough to emancipate us. He is no longer a slave
who can choose his master.
Thus, thanks to generalization, each fact observed enables us to foresee a
great many others; only we must not forget that the first alone is certain,
that all others are merely probable. No matter how solidly founded a
prediction may appear to us, we are never absolutely sure that experiment
will not contradict it, if we undertake to verify it. The probability, however,
is often so great that practically we may be content with it. It is far better to
foresee even without certainty than not to foresee at all.
One must, then, never disdain to make a verification when opportunity
offers. But all experiment is long and difficult; the workers are few; and the

number of facts that we need to foresee is immense. Compared with this
mass the number of direct verifications that we can make will never be
anything but a negligible quantity.
Of this few that we can directly attain, we must make the best use; it is
very necessary to get from every experiment the greatest possible number
of predictions, and with the highest possible degree of probability. The
problem is, so to speak, to increase the yield of the scientific machine.
Let us compare science to a library that ought to grow continually. The
librarian has at his disposal for his purchases only insufficient funds. He
ought to make an effort not to waste them.
It is experimental physics that is entrusted with the purchases. It alone,
then, can enrich the library.
As for mathematical physics, its task will be to make out the catalogue. If
the catalogue is well made, the library will not be any richer, but the reader
will be helped to use its riches.
And even by showing the librarian the gaps in his collections, it will
enable him to make a judicious use of his funds; which is all the more
important because these funds are entirely inadequate.
Such, then, is the rôle of mathematical physics. It must direct
generalization in such a manner as to increase what I just now called the
yield of science. By what means it can arrive at this, and how it can do it
without danger, is what remains for us to investigate.
The Unity of Nature.—Let us notice, first of all, that every
generalization implies in some measure the belief in the unity and
simplicity of nature. As to the unity there can be no difficulty. If the
different parts of the universe were not like the members of one body, they
would not act on one another, they would know nothing of one another; and
we in particular would know only one of these parts. We do not ask, then, if
nature is one, but how it is one.
As for the second point, that is not such an easy matter. It is not certain
that nature is simple. Can we without danger act as if it were?

There was a time when the simplicity of Mariotte's law was an argument
invoked in favor of its accuracy; when Fresnel himself, after having said in
a conversation with Laplace that nature was not concerned about analytical
difficulties, felt himself obliged to make explanations, in order not to strike
too hard at prevailing opinion.
To-day ideas have greatly changed; and yet, those who do not believe
that natural laws have to be simple, are still often obliged to act as if they
did. They could not entirely avoid this necessity without making impossible
all generalization, and consequently all science.
It is clear that any fact can be generalized in an infinity of ways, and it is
a question of choice. The choice can be guided only by considerations of
simplicity. Let us take the most commonplace case, that of interpolation.
We pass a continuous line, as regular as possible, between the points given
by observation. Why do we avoid points making angles and too abrupt
turns? Why do we not make our curve describe the most capricious zig-
zags? It is because we know beforehand, or believe we know, that the law to
be expressed can not be so complicated as all that.
We may calculate the mass of Jupiter from either the movements of its
satellites, or the perturbations of the major planets, or those of the minor
planets. If we take the averages of the determinations obtained by these
three methods, we find three numbers very close together, but different. We
might interpret this result by supposing that the coefficient of gravitation is
not the same in the three cases. The observations would certainly be much
better represented. Why do we reject this interpretation? Not because it is
absurd, but because it is needlessly complicated. We shall only accept it
when we are forced to, and that is not yet.
To sum up, ordinarily every law is held to be simple till the contrary is
proved.
This custom is imposed upon physicists by the causes that I have just
explained. But how shall we justify it in the presence of discoveries that
show us every day new details that are richer and more complex? How shall
we even reconcile it with the belief in the unity of nature? For if everything
depends on everything, relationships where so many diverse factors enter
can no longer be simple.

If we study the history of science, we see happen two inverse
phenomena, so to speak. Sometimes simplicity hides under complex
appearances; sometimes it is the simplicity which is apparent, and which
disguises extremely complicated realities.
What is more complicated than the confused movements of the planets?
What simpler than Newton's law? Here nature, making sport, as Fresnel
said, of analytical difficulties, employs only simple means, and by
combining them produces I know not what inextricable tangle. Here it is the
hidden simplicity which must be discovered.
Examples of the opposite abound. In the kinetic theory of gases, one
deals with molecules moving with great velocities, whose paths, altered by
incessant collisions, have the most capricious forms and traverse space in
every direction. The observable result is Mariotte's simple law. Every
individual fact was complicated. The law of great numbers has
reestablished simplicity in the average. Here the simplicity is merely
apparent, and only the coarseness of our senses prevents our perceiving the
complexity.
Many phenomena obey a law of proportionality. But why? Because in
these phenomena there is something very small. The simple law observed,
then, is only a result of the general analytical rule that the infinitely small
increment of a function is proportional to the increment of the variable. As
in reality our increments are not infinitely small, but very small, the law of
proportionality is only approximate, and the simplicity is only apparent.
What I have just said applies to the rule of the superposition of small
motions, the use of which is so fruitful, and which is the basis of optics.
And Newton's law itself? Its simplicity, so long undetected, is perhaps
only apparent. Who knows whether it is not due to some complicated
mechanism, to the impact of some subtile matter animated by irregular
movements, and whether it has not become simple only through the action
of averages and of great numbers? In any case, it is difficult not to suppose
that the true law contains complementary terms, which would become
sensible at small distances. If in astronomy they are negligible as modifying
Newton's law, and if the law thus regains its simplicity, it would be only
because of the immensity of celestial distances.

No doubt, if our means of investigation should become more and more
penetrating, we should discover the simple under the complex, then the
complex under the simple, then again the simple under the complex, and so
on, without our being able to foresee what will be the last term.
We must stop somewhere, and that science may be possible we must stop
when we have found simplicity. This is the only ground on which we can
rear the edifice of our generalizations. But this simplicity being only
apparent, will the ground be firm enough? This is what must be
investigated.
For that purpose, let us see what part is played in our generalizations by
the belief in simplicity. We have verified a simple law in a good many
particular cases; we refuse to admit that this agreement, so often repeated, is
simply the result of chance, and conclude that the law must be true in the
general case.
Kepler notices that a planet's positions, as observed by Tycho, are all on
one ellipse. Never for a moment does he have the thought that by a strange
play of chance Tycho never observed the heavens except at a moment when
the real orbit of the planet happened to cut this ellipse.
What does it matter then whether the simplicity be real, or whether it
covers a complex reality? Whether it is due to the influence of great
numbers, which levels down individual differences, or to the greatness or
smallness of certain quantities, which allows us to neglect certain terms, in
no case is it due to chance. This simplicity, real or apparent, always has a
cause. We can always follow, then, the same course of reasoning, and if a
simple law has been observed in several particular cases, we can
legitimately suppose that it will still be true in analogous cases. To refuse to
do this would be to attribute to chance an inadmissible rôle.
There is, however, a difference. If the simplicity were real and essential,
it would resist the increasing precision of our means of measure. If then we
believe nature to be essentially simple, we must, from a simplicity that is
approximate, infer a simplicity that is rigorous. This is what was done
formerly; and this is what we no longer have a right to do.

The simplicity of Kepler's laws, for example, is only apparent. That does
not prevent their being applicable, very nearly, to all systems analogous to
the solar system; but it does prevent their being rigorously exact.
The Rôle of Hypothesis.—All generalization is a hypothesis.
Hypothesis, then, has a necessary rôle that no one has ever contested. Only,
it ought always, as soon as possible and as often as possible, to be subjected
to verification. And, of course, if it does not stand this test, it ought to be
abandoned without reserve. This is what we generally do, but sometimes
with rather an ill humor.
Well, even this ill humor is not justified. The physicist who has just
renounced one of his hypotheses ought, on the contrary, to be full of joy; for
he has found an unexpected opportunity for discovery. His hypothesis, I
imagine, had not been adopted without consideration; it took account of all
the known factors that it seemed could enter into the phenomenon. If the
test does not support it, it is because there is something unexpected and
extraordinary; and because there is going to be something found that is
unknown and new.
Has the discarded hypothesis, then, been barren? Far from that, it may be
said it has rendered more service than a true hypothesis. Not only has it
been the occasion of the decisive experiment, but, without having made the
hypothesis, the experiment would have been made by chance, so that
nothing would have been derived from it. One would have seen nothing
extraordinary; only one fact the more would have been catalogued without
deducing from it the least consequence.
Now on what condition is the use of hypothesis without danger?
The firm determination to submit to experiment is not enough; there are
still dangerous hypotheses; first, and above all, those which are tacit and
unconscious. Since we make them without knowing it, we are powerless to
abandon them. Here again, then, is a service that mathematical physics can
render us. By the precision that is characteristic of it, it compels us to
formulate all the hypotheses that we should make without it, but
unconsciously.

Let us notice besides that it is important not to multiply hypotheses
beyond measure, and to make them only one after the other. If we construct
a theory based on a number of hypotheses, and if experiment condemns it,
which of our premises is it necessary to change? It will be impossible to
know. And inversely, if the experiment succeeds, shall we believe that we
have demonstrated all the hypotheses at once? Shall we believe that with
one single equation we have determined several unknowns?
We must equally take care to distinguish between the different kinds of
hypotheses. There are first those which are perfectly natural and from which
one can scarcely escape. It is difficult not to suppose that the influence of
bodies very remote is quite negligible, that small movements follow a linear
law, that the effect is a continuous function of its cause. I will say as much
of the conditions imposed by symmetry. All these hypotheses form, as it
were, the common basis of all the theories of mathematical physics. They
are the last that ought to be abandoned.
There is a second class of hypotheses, that I shall term neutral. In most
questions the analyst assumes at the beginning of his calculations either that
matter is continuous or, on the contrary, that it is formed of atoms. He might
have made the opposite assumption without changing his results. He would
only have had more trouble to obtain them; that is all. If, then, experiment
confirms his conclusions, will he think that he has demonstrated, for
instance, the real existence of atoms?
In optical theories two vectors are introduced, of which one is regarded
as a velocity, the other as a vortex. Here again is a neutral hypothesis, since
the same conclusions would have been reached by taking precisely the
opposite. The success of the experiment, then, can not prove that the first
vector is indeed a velocity; it can only prove one thing, that it is a vector.
This is the only hypothesis that has really been introduced in the premises.
In order to give it that concrete appearance which the weakness of our
minds requires, it has been necessary to consider it either as a velocity or as
a vortex, in the same way that it has been necessary to represent it by a
letter, either x or y. The result, however, whatever it may be, will not prove
that it was right or wrong to regard it as a velocity any more than it will
prove that it was right or wrong to call it x and not y.

These neutral hypotheses are never dangerous, if only their character is
not misunderstood. They may be useful, either as devices for computation,
or to aid our understanding by concrete images, to fix our ideas as the
saying is. There is, then, no occasion to exclude them.
The hypotheses of the third class are the real generalizations. They are
the ones that experiment must confirm or invalidate. Whether verified or
condemned, they will always be fruitful. But for the reasons that I have set
forth, they will only be fruitful if they are not too numerous.
Origin of Mathematical Physics.—Let us penetrate further, and study
more closely the conditions that have permitted the development of
mathematical physics. We observe at once that the efforts of scientists have
always aimed to resolve the complex phenomenon directly given by
experiment into a very large number of elementary phenomena.
This is done in three different ways: first, in time. Instead of embracing
in its entirety the progressive development of a phenomenon, the aim is
simply to connect each instant with the instant immediately preceding it. It
is admitted that the actual state of the world depends only on the immediate
past, without being directly influenced, so to speak, by the memory of a
distant past. Thanks to this postulate, instead of studying directly the whole
succession of phenomena, it is possible to confine ourselves to writing its
'differential equation.' For Kepler's laws we substitute Newton's law.
Next we try to analyze the phenomenon in space. What experiment gives
us is a confused mass of facts presented on a stage of considerable extent.
We must try to discover the elementary phenomenon, which will be, on the
contrary, localized in a very small region of space.
Some examples will perhaps make my thought better understood. If we
wished to study in all its complexity the distribution of temperature in a
cooling solid, we should never succeed. Everything becomes simple if we
reflect that one point of the solid can not give up its heat directly to a distant
point; it will give up its heat only to the points in the immediate
neighborhood, and it is by degrees that the flow of heat can reach other
parts of the solid. The elementary phenomenon is the exchange of heat
between two contiguous points. It is strictly localized, and is relatively

simple, if we admit, as is natural, that it is not influenced by the temperature
of molecules whose distance is sensible.
I bend a rod. It is going to take a very complicated form, the direct study
of which would be impossible. But I shall be able, however, to attack it, if I
observe that its flexure is a result only of the deformation of the very small
elements of the rod, and that the deformation of each of these elements
depends only on the forces that are directly applied to it, and not at all on
those which may act on the other elements.
In all these examples, which I might easily multiply, we admit that there
is no action at a distance, or at least at a great distance. This is a hypothesis.
It is not always true, as the law of gravitation shows us. It must, then, be
submitted to verification. If it is confirmed, even approximately, it is
precious, for it will enable us to make mathematical physics, at least by
successive approximations.
If it does not stand the test, we must look for something else analogous;
for there are still other means of arriving at the elementary phenomenon. If
several bodies act simultaneously, it may happen that their actions are
independent and are simply added to one another, either as vectors or as
scalars. The elementary phenomenon is then the action of an isolated body.
Or again, we have to deal with small movements, or more generally with
small variations, which obey the well-known law of superposition. The
observed movement will then be decomposed into simple movements, for
example, sound into its harmonics, white light into its monochromatic
components.
When we have discovered in what direction it is advisable to look for the
elementary phenomenon, by what means can we reach it?
First of all, it will often happen that in order to detect it, or rather to
detect the part of it useful to us, it will not be necessary to penetrate the
mechanism; the law of great numbers will suffice.
Let us take again the instance of the propagation of heat. Every molecule
emits rays toward every neighboring molecule. According to what law, we
do not need to know. If we should make any supposition in regard to this, it
would be a neutral hypothesis and consequently useless and incapable of

verification. And, in fact, by the action of averages and thanks to the
symmetry of the medium, all the differences are leveled down, and
whatever hypothesis may be made, the result is always the same.
The same circumstance is presented in the theory of electricity and in that
of capillarity. The neighboring molecules attract and repel one another. We
do not need to know according to what law; it is enough for us that this
attraction is sensible only at small distances, and that the molecules are very
numerous, that the medium is symmetrical, and we shall only have to let the
law of great numbers act.
Here again the simplicity of the elementary phenomenon was hidden
under the complexity of the resultant observable phenomenon; but, in its
turn, this simplicity was only apparent, and concealed a very complex
mechanism.
The best means of arriving at the elementary phenomenon would
evidently be experiment. We ought by experimental contrivance to
dissociate the complex sheaf that nature offers to our researches, and to
study with care the elements as much isolated as possible. For example,
natural white light would be decomposed into monochromatic lights by the
aid of the prism, and into polarized light by the aid of the polarizer.
Unfortunately that is neither always possible nor always sufficient, and
sometimes the mind must outstrip experiment. I shall cite only one
example, which has always struck me forcibly.
If I decompose white light, I shall be able to isolate a small part of the
spectrum, but however small it may be, it will retain a certain breadth.
Likewise the natural lights, called monochromatic, give us a very narrow
line, but not, however, infinitely narrow. It might be supposed that by
studying experimentally the properties of these natural lights, by working
with finer and finer lines of the spectrum, and by passing at last to the limit,
so to speak, we should succeed in learning the properties of a light strictly
monochromatic.
That would not be accurate. Suppose that two rays emanate from the
same source, that we polarize them first in two perpendicular planes, then
bring them back to the same plane of polarization, and try to make them

interfere. If the light were strictly monochromatic, they would interfere.
With our lights, which are nearly monochromatic, there will be no
interference, and that no matter how narrow the line. In order to be
otherwise it would have to be several million times as narrow as the finest
known lines.
Here, then, the passage to the limit would have deceived us. The mind
must outstrip the experiment, and if it has done so with success, it is
because it has allowed itself to be guided by the instinct of simplicity.
The knowledge of the elementary fact enables us to put the problem in an
equation. Nothing remains but to deduce from this by combination the
complex fact that can be observed and verified. This is what is called
integration, and is the business of the mathematician.
It may be asked why, in physical sciences, generalization so readily takes
the mathematical form. The reason is now easy to see. It is not only because
we have numerical laws to express; it is because the observable
phenomenon is due to the superposition of a great number of elementary
phenomena all alike. Thus quite naturally are introduced differential
equations.
It is not enough that each elementary phenomenon obeys simple laws; all
those to be combined must obey the same law. Then only can the
intervention of mathematics be of use; mathematics teaches us in fact to
combine like with like. Its aim is to learn the result of a combination
without needing to go over the combination piece by piece. If we have to
repeat several times the same operation, it enables us to avoid this repetition
by telling us in advance the result of it by a sort of induction. I have
explained this above, in the chapter on mathematical reasoning.
But for this, all the operations must be alike. In the opposite case, it
would evidently be necessary to resign ourselves to doing them in reality
one after another, and mathematics would become useless.
It is then thanks to the approximate homogeneity of the matter studied by
physicists that mathematical physics could be born.
In the natural sciences, we no longer find these conditions: homogeneity,
relative independence of remote parts, simplicity of the elementary fact; and

this is why naturalists are obliged to resort to other methods of
generalization.

CHAPTER X

The Theories of Modern Physics
Meaning of Physical Theories.—The laity are struck to see how
ephemeral scientific theories are. After some years of prosperity, they see
them successively abandoned; they see ruins accumulate upon ruins; they
foresee that the theories fashionable to-day will shortly succumb in their
turn and hence they conclude that these are absolutely idle. This is what
they call the bankruptcy of science.
Their skepticism is superficial; they give no account to themselves of the
aim and the rôle of scientific theories; otherwise they would comprehend
that the ruins may still be good for something.
No theory seemed more solid than that of Fresnel which attributed light
to motions of the ether. Yet now Maxwell's is preferred. Does this mean the
work of Fresnel was in vain? No, because the aim of Fresnel was not to find
out whether there is really an ether, whether it is or is not formed of atoms,
whether these atoms really move in this or that sense; his object was to
foresee optical phenomena.
Now, Fresnel's theory always permits of this, to-day as well as before
Maxwell. The differential equations are always true; they can always be
integrated by the same procedures and the results of this integration always
retain their value.
And let no one say that thus we reduce physical theories to the rôle of
mere practical recipes; these equations express relations, and if the
equations remain true it is because these relations preserve their reality.
They teach us, now as then, that there is such and such a relation between
some thing and some other thing; only this something formerly we called
motion; we now call it electric current. But these appellations were only

images substituted for the real objects which nature will eternally hide from
us. The true relations between these real objects are the only reality we can
attain to, and the only condition is that the same relations exist between
these objects as between the images by which we are forced to replace
them. If these relations are known to us, what matter if we deem it
convenient to replace one image by another.
That some periodic phenomenon (an electric oscillation, for instance) is
really due to the vibration of some atom which, acting like a pendulum,
really moves in this or that sense, is neither certain nor interesting. But that
between electric oscillation, the motion of the pendulum and all periodic
phenomena there exists a close relationship which corresponds to a
profound reality; that this relationship, this similitude, or rather this
parallelism extends into details; that it is a consequence of more general
principles, that of energy and that of least action; this is what we can affirm;
this is the truth which will always remain the same under all the costumes
in which we may deem it useful to deck it out.
Numerous theories of dispersion have been proposed; the first was
imperfect and contained only a small part of truth. Afterwards came that of
Helmholtz; then it was modified in various ways, and its author himself
imagined another founded on the principles of Maxwell. But, what is
remarkable, all the scientists who came after Helmholtz reached the same
equations, starting from points of departure in appearance very widely
separated. I will venture to say these theories are all true at the same time,
not only because they make us foresee the same phenomena, but because
they put in evidence a true relation, that of absorption and anomalous
dispersion. What is true in the premises of these theories is what is common
to all the authors; this is the affirmation of this or that relation between
certain things which some call by one name, others by another.
The kinetic theory of gases has given rise to many objections, which we
could hardly answer if we pretended to see in it the absolute truth. But all
these objections will not preclude its having been useful, and particularly so
in revealing to us a relation true and but for it profoundly hidden, that of the
gaseous pressure and the osmotic pressure. In this sense, then, it may be
said to be true.

When a physicist finds a contradiction between two theories equally dear
to him, he sometimes says: "We will not bother about that, but hold firmly
the two ends of the chain, though the intermediate links are hidden from
us." This argument of an embarrassed theologian would be ridiculous if it
were necessary to attribute to physical theories the sense the laity give
them. In case of contradiction, one of them at least must then be regarded as
false. It is no longer the same if in them be sought only what should be
sought. May be they both express true relations and the contradiction is
only in the images wherewith we have clothed the reality.
To those who find we restrict too much the domain accessible to the
scientist, I answer: These questions which we interdict to you and which
you regret, are not only insoluble, they are illusory and devoid of meaning.
Some philosopher pretends that all physics may be explained by the
mutual impacts of atoms. If he merely means there are between physical
phenomena the same relations as between the mutual impacts of a great
number of balls, well and good, that is verifiable, that is perhaps true. But
he means something more; and we think we understand it because we think
we know what impact is in itself; why? Simply because we have often seen
games of billiards. Shall we think God, contemplating his work, feels the
same sensations as we in watching a billiard match? If we do not wish to
give this bizarre sense to his assertion, if neither do we wish the restricted
sense I have just explained, which is good sense, then it has none.
Hypotheses of this sort have therefore only a metaphorical sense. The
scientist should no more interdict them than the poet does metaphors; but he
ought to know what they are worth. They may be useful to give a certain
satisfaction to the mind, and they will not be injurious provided they are
only indifferent hypotheses.
These considerations explain to us why certain theories, supposed to be
abandoned and finally condemned by experiment, suddenly arise from their
ashes and recommence a new life. It is because they expressed true
relations; and because they had not ceased to do so when, for one reason or
another, we felt it necessary to enunciate the same relations in another
language. So they retained a sort of latent life.

Scarcely fifteen years ago was there anything more ridiculous, more
naïvely antiquated, than Coulomb's fluids? And yet here they are
reappearing under the name of electrons. Wherein do these permanently
electrified molecules differ from Coulomb's electric molecules? It is true
that in the electrons the electricity is supported by a little, a very little
matter; in other words, they have a mass (and yet this is now contested); but
Coulomb did not deny mass to his fluids, or, if he did, it was only with
reluctance. It would be rash to affirm that the belief in electrons will not
again suffer eclipse; it was none the less curious to note this unexpected
resurrection.
But the most striking example is Carnot's principle. Carnot set it up
starting from false hypotheses; when it was seen that heat is not
indestructible, but may be transformed into work, his ideas were completely
abandoned; afterwards Clausius returned to them and made them finally
triumph. Carnot's theory, under its primitive form, expressed, aside from
true relations, other inexact relations, débris of antiquated ideas; but the
presence of these latter did not change the reality of the others. Clausius had
only to discard them as one lops off dead branches.
The result was the second fundamental law of thermodynamics. There
were always the same relations; though these relations no longer subsisted,
at least in appearance, between the same objects. This was enough for the
principle to retain its value. And even the reasonings of Carnot have not
perished because of that; they were applied to a material tainted with error;
but their form (that is to say, the essential) remained correct.
What I have just said illuminates at the same time the rôle of general
principles such as the principle of least action, or that of the conservation of
energy.
These principles have a very high value; they were obtained in seeking
what there was in common in the enunciation of numerous physical laws;
they represent therefore, as it were, the quintessence of innumerable
observations.
However, from their very generality a consequence results to which I
have called attention in Chapter VIII, namely, that they can no longer be
verified. As we can not give a general definition of energy, the principle of

the conservation of energy signifies simply that there is something which
remains constant. Well, whatever be the new notions that future
experiments shall give us about the world, we are sure in advance that there
will be something there which will remain constant and which may be
called energy.
Is this to say that the principle has no meaning and vanishes in a
tautology? Not at all; it signifies that the different things to which we give
the name of energy are connected by a true kinship; it affirms a real relation
between them. But then if this principle has a meaning, it may be false; it
may be that we have not the right to extend indefinitely its applications, and
yet it is certain beforehand to be verified in the strict acceptation of the
term; how then shall we know when it shall have attained all the extension
which can legitimately be given it? Just simply when it shall cease to be
useful to us, that is, to make us correctly foresee new phenomena. We shall
be sure in such a case that the relation affirmed is no longer real; for
otherwise it would be fruitful; experiment, without directly contradicting a
new extension of the principle, will yet have condemned it.
Physics and Mechanism.—Most theorists have a constant predilection for
explanations borrowed from mechanics or dynamics. Some would be
satisfied if they could explain all phenomena by motions of molecules
attracting each other according to certain laws. Others are more exacting;
they would suppress attractions at a distance; their molecules should follow
rectilinear paths from which they could be made to deviate only by impacts.
Others again, like Hertz, suppress forces also, but suppose their molecules
subjected to geometric attachments analogous, for instance, to those of our
linkages; they try thus to reduce dynamics to a sort of kinematics.
In a word, all would bend nature into a certain form outside of which
their mind could not feel satisfied. Will nature be sufficiently flexible for
that?
We shall examine this question in Chapter XII, à propos of Maxwell's
theory. Whenever the principles of energy and of least action are satisfied,
we shall see not only that there is always one possible mechanical
explanation, but that there is always an infinity of them. Thanks to a well-
known theorem of König's on linkages, it could be shown that we can, in an

infinity of ways, explain everything by attachments after the manner of
Hertz, or also by central forces. Without doubt it could be demonstrated just
as easily that everything can always be explained by simple impacts.
For that, of course, we need not be content with ordinary matter, with that
which falls under our senses and whose motions we observe directly. Either
we shall suppose that this common matter is formed of atoms whose
internal motions elude us, the displacement of the totality alone remaining
accessible to our senses. Or else we shall imagine some one of those subtile
fluids which under the name of ether or under other names, have at all times
played so great a rôle in physical theories.
Often one goes further and regards the ether as the sole primitive matter
or even as the only true matter. The more moderate consider common
matter as condensed ether, which is nothing startling; but others reduce still
further its importance and see in it nothing more than the geometric locus of
the ether's singularities. For instance, what we call matter is for Lord Kelvin
only the locus of points where the ether is animated by vortex motions; for
Riemann, it was the locus of points where ether is constantly destroyed; for
other more recent authors, Wiechert or Larmor, it is the locus of points
where the ether undergoes a sort of torsion of a very particular nature. If the
attempt is made to occupy one of these points of view, I ask myself by what
right shall we extend to the ether, under pretext that this is the true matter,
mechanical properties observed in ordinary matter, which is only false
matter.
The ancient fluids, caloric, electricity, etc., were abandoned when it was
perceived that heat is not indestructible. But they were abandoned for
another reason also. In materializing them, their individuality was, so to
speak, emphasized, a sort of abyss was opened between them. This had to
be filled up on the coming of a more vivid feeling of the unity of nature,
and the perception of the intimate relations which bind together all its parts.
Not only did the old physicists, in multiplying fluids, create entities
unnecessarily, but they broke real ties.
It is not sufficient for a theory to affirm no false relations, it must not
hide true relations.

And does our ether really exist? We know the origin of our belief in the
ether. If light reaches us from a distant star, during several years it was no
longer on the star and not yet on the earth; it must then be somewhere and
sustained, so to speak, by some material support.
The same idea may be expressed under a more mathematical and more
abstract form. What we ascertain are the changes undergone by material
molecules; we see, for instance, that our photographic plate feels the
consequences of phenomena of which the incandescent mass of the star was
the theater several years before. Now, in ordinary mechanics the state of the
system studied depends only on its state at an instant immediately anterior;
therefore the system satisfies differential equations. On the contrary, if we
should not believe in the ether, the state of the material universe would
depend not only on the state immediately preceding, but on states much
older; the system would satisfy equations of finite differences. It is to
escape this derogation of the general laws of mechanics that we have
invented the ether.
That would still only oblige us to fill up, with the ether, the interplanetary
void, but not to make it penetrate the bosom of the material media
themselves. Fizeau's experiment goes further. By the interference of rays
which have traversed air or water in motion, it seems to show us two
different media interpenetrating and yet changing place one with regard to
the other.
We seem to touch the ether with the finger.
Yet experiments may be conceived which would make us touch it still
more nearly. Suppose Newton's principle, of the equality of action and
reaction, no longer true if applied to matter alone, and that we have
established it. The geometric sum of all the forces applied to all the material
molecules would no longer be null. It would be necessary then, if we did
not wish to change all mechanics, to introduce the ether, in order that this
action which matter appeared to experience should be counterbalanced by
the reaction of matter on something.
Or again, suppose we discover that optical and electrical phenomena are
influenced by the motion of the earth. We should be led to conclude that
these phenomena might reveal to us not only the relative motions of

material bodies, but what would seem to be their absolute motions. Again,
an ether would be necessary, that these so-called absolute motions should
not be their displacements with regard to a void space, but their
displacements with regard to something concrete.
Shall we ever arrive at that? I have not this hope, I shall soon say why,
and yet it is not so absurd, since others have had it.
For instance, if the theory of Lorentz, of which I shall speak in detail
further on in Chapter XIII., were true, Newton's principle would not apply
to matter alone, and the difference would not be very far from being
accessible to experiment.
On the other hand, many researches have been made on the influence of
the earth's motion. The results have always been negative. But these
experiments were undertaken because the outcome was not sure in advance,
and, indeed, according to the ruling theories, the compensation would be
only approximate, and one might expect to see precise methods give
positive results.
I believe that such a hope is illusory; it was none the less interesting to
show that a success of this sort would open to us, in some sort, a new world.
And now I must be permitted a digression; I must explain, in fact, why I
do not believe, despite Lorentz, that more precise observations can ever put
in evidence anything else than the relative displacements of material bodies.
Experiments have been made which should have disclosed the terms of the
first order; the results have been negative; could that be by chance? No one
has assumed that; a general explanation has been sought, and Lorentz has
found it; he has shown that the terms of the first order must destroy each
other, but not those of the second. Then more precise experiments were
made; they also were negative; neither could this be the effect of chance; an
explanation was necessary; it was found; they always are found; of
hypotheses there is never lack.
But this is not enough; who does not feel that this is still to leave to
chance too great a rôle? Would not that also be a chance, this singular
coincidence which brought it about that a certain circumstance should come
just in the nick of time to destroy the terms of the first order, and that

another circumstance, wholly different, but just as opportune, should take
upon itself to destroy those of the second order? No, it is necessary to find
an explanation the same for the one as for the other, and then everything
leads us to think that this explanation will hold good equally well for the
terms of higher order, and that the mutual destruction of these terms will be
rigorous and absolute.
Present State of the Science.—In the history of the development of
physics we distinguish two inverse tendencies.
On the one hand, new bonds are continually being discovered between
objects which had seemed destined to remain forever unconnected;
scattered facts cease to be strangers to one another; they tend to arrange
themselves in an imposing synthesis. Science advances toward unity and
simplicity.
On the other hand, observation reveals to us every day new phenomena;
they must long await their place and sometimes, to make one for them, a
corner of the edifice must be demolished. In the known phenomena
themselves, where our crude senses showed us uniformity, we perceive
details from day to day more varied; what we believed simple becomes
complex, and science appears to advance toward variety and complexity.
Of these two inverse tendencies, which seem to triumph turn about,
which will win? If it be the first, science is possible; but nothing proves this
a priori, and it may well be feared that after having made vain efforts to
bend nature in spite of herself to our ideal of unity, submerged by the ever-
rising flood of our new riches, we must renounce classifying them, abandon
our ideal, and reduce science to the registration of innumerable recipes.
To this question we can not reply. All we can do is to observe the science
of to-day and compare it with that of yesterday. From this examination we
may doubtless draw some encouragement.
Half a century ago, hope ran high. The discovery of the conservation of
energy and of its transformations had revealed to us the unity of force. Thus
it showed that the phenomena of heat could be explained by molecular
motions. What was the nature of these motions was not exactly known, but
no one doubted that it soon would be. For light, the task seemed completely

accomplished. In what concerns electricity, things were less advanced.
Electricity had just annexed magnetism. This was a considerable step
toward unity, and a decisive step.
But how should electricity in its turn enter into the general unity, how
should it be reduced to the universal mechanism?
Of that no one had any idea. Yet the possibility of this reduction was
doubted by none, there was faith. Finally, in what concerns the molecular
properties of material bodies, the reduction seemed still easier, but all the
detail remained hazy. In a word, the hopes were vast and animated, but
vague. To-day, what do we see? First of all, a prime progress, immense
progress. The relations of electricity and light are now known; the three
realms, of light, of electricity and of magnetism, previously separated, form
now but one; and this annexation seems final.
This conquest, however, has cost us some sacrifices. The optical
phenomena subordinate themselves as particular cases under the electrical
phenomena; so long as they remained isolated, it was easy to explain them
by motions that were supposed to be known in all their details, that was a
matter of course; but now an explanation, to be acceptable, must be easily
capable of extension to the entire electric domain. Now that is a matter not
without difficulties.
The most satisfactory theory we have is that of Lorentz, which, as we
shall see in the last chapter, explains electric currents by the motions of
little electrified particles; it is unquestionably the one which best explains
the known facts, the one which illuminates the greatest number of true
relations, the one of which most traces will be found in the final
construction. Nevertheless, it still has a serious defect, which I have
indicated above; it is contrary to Newton's law of the equality of action and
reaction; or rather, this principle, in the eyes of Lorentz, would not be
applicable to matter alone; for it to be true, it would be necessary to take
account of the action of the ether on matter and of the reaction of matter on
the ether.
Now, from what we know at present, it seems probable that things do not
happen in this way.

However that may be, thanks to Lorentz, Fizeau's results on the optics of
moving bodies, the laws of normal and anomalous dispersion and of
absorption find themselves linked to one another and to the other properties
of the ether by bonds which beyond any doubt will never more be broken.
See the facility with which the new Zeeman effect has found its place
already and has even aided in classifying Faraday's magnetic rotation which
had defied Maxwell's efforts; this facility abundantly proves that the theory
of Lorentz is not an artificial assemblage destined to fall asunder. It will
probably have to be modified, but not destroyed.
But Lorentz had no aim beyond that of embracing in one totality all the
optics and electrodynamics of moving bodies; he never pretended to give a
mechanical explanation of them. Larmor goes further; retaining the theory
of Lorentz in essentials, he grafts upon it, so to speak, MacCullagh's ideas
on the direction of the motions of the ether.
According to him, the velocity of the ether would have the same direction
and the same magnitude as the magnetic force. However ingenious this
attempt may be, the defect of the theory of Lorentz remains and is even
aggravated. With Lorentz, we do not know what are the motions of the
ether; thanks to this ignorance, we may suppose them such that,
compensating those of matter, they reestablish the equality of action and
reaction. With Larmor, we know the motions of the ether, and we can
ascertain that the compensation does not take place.
If Larmor has failed, as it seems to me he has, does that mean that a
mechanical explanation is impossible? Far from it: I have said above that
when a phenomenon obeys the two principles of energy and of least action,
it admits of an infinity of mechanical explanations; so it is, therefore, with
the optical and electrical phenomena.
But this is not enough: for a mechanical explanation to be good, it must
be simple; for choosing it among all which are possible, there should be
other reasons besides the necessity of making a choice. Well, we have not as
yet a theory satisfying this condition and consequently good for something.
Must we lament this? That would be to forget what is the goal sought; this
is not mechanism; the true, the sole aim is unity.

We must therefore set bounds to our ambition; let us not try to formulate
a mechanical explanation; let us be content with showing that we could
always find one if we wished to. In this regard we have been successful; the
principle of the conservation of energy has received only confirmations; a
second principle has come to join it, that of least action, put under the form
which is suitable for physics. It also has always been verified, at least in so
far as concerns reversible phenomena which thus obey the equations of
Lagrange, that is to say, the most general laws of mechanics.
Irreversible phenomena are much more rebellious. Yet these also are
being coordinated, and tend to come into unity; the light which has
illuminated them has come to us from Carnot's principle. Long did
thermodynamics confine itself to the study of the dilatation of bodies and
their changes of state. For some time past it has been growing bolder and
has considerably extended its domain. We owe to it the theory of the
galvanic battery and that of the thermoelectric phenomena; there is not in
all physics a corner that it has not explored, and it has attacked chemistry
itself.
Everywhere the same laws reign; everywhere, under the diversity of
appearances, is found again Carnot's principle; everywhere also is found
that concept so prodigiously abstract of entropy, which is as universal as
that of energy and seems like it to cover a reality. Radiant heat seemed
destined to escape it; but recently we have seen that submit to the same
laws.
In this way fresh analogies are revealed to us, which may often be
followed into detail; ohmic resistance resembles the viscosity of liquids;
hysteresis would resemble rather the friction of solids. In all cases, friction
would appear to be the type which the most various irreversible phenomena
copy, and this kinship is real and profound.
Of these phenomena a mechanical explanation, properly so called, has
also been sought. They hardly lent themselves to it. To find it, it was
necessary to suppose that the irreversibility is only apparent, that the
elementary phenomena are reversible and obey the known laws of
dynamics. But the elements are extremely numerous and blend more and
more, so that to our crude sight all appears to tend toward uniformity, that

is, everything seems to go forward in the same sense without hope of return.
The apparent irreversibility is thus only an effect of the law of great
numbers. But, only a being with infinitely subtile senses, like Maxwell's
imaginary demon, could disentangle this inextricable skein and turn back
the course of the universe.
This conception, which attaches itself to the kinetic theory of gases, has
cost great efforts and has not, on the whole, been fruitful; but it may
become so. This is not the place to examine whether it does not lead to
contradictions and whether it is in conformity with the true nature of things.
We signalize, however, M. Gouy's original ideas on the Brownian
movement. According to this scientist, this singular motion should escape
Carnot's principle. The particles which it puts in swing would be smaller
than the links of that so compacted skein; they would therefore be fitted to
disentangle them and hence to make the world go backward. We should
almost see Maxwell's demon at work.
To summarize, the previously known phenomena are better and better
classified, but new phenomena come to claim their place; most of these,
like the Zeeman effect, have at once found it.
But we have the cathode rays, the X-rays, those of uranium and of
radium. Herein is a whole world which no one suspected. How many
unexpected guests must be stowed away?
No one can yet foresee the place they will occupy. But I do not believe
they will destroy the general unity; I think they will rather complete it. On
the one hand, in fact, the new radiations seem connected with the
phenomena of luminescence; not only do they excite fluorescence, but they
sometimes take birth in the same conditions as it.
Nor are they without kinship with the causes which produce the electric
spark under the action of the ultra-violet light.
Finally, and above all, it is believed that in all these phenomena are found
true ions, animated, it is true, by velocities incomparably greater than in the
electrolytes.
That is all very vague, but it will all become more precise.

Phosphorescence, the action of light on the spark, these were regions
rather isolated and consequently somewhat neglected by investigators. One
may now hope that a new path will be constructed which will facilitate their
communications with the rest of science.
Not only do we discover new phenomena, but in those we thought we
knew, unforeseen aspects reveal themselves. In the free ether, the laws
retain their majestic simplicity; but matter, properly so called, seems more
and more complex; all that is said of it is never more than approximate, and
at each instant our formulas require new terms.
Nevertheless the frames are not broken; the relations that we have
recognized between objects we thought simple still subsist between these
same objects when we know their complexity, and it is that alone which is
of importance. Our equations become, it is true, more and more
complicated, in order to embrace more closely the complexity of nature; but
nothing is changed in the relations which permit the deducing of these
equations one from another. In a word, the form of these equations has
persisted.
Take, for example, the laws of reflection: Fresnel had established them
by a simple and seductive theory which experiment seemed to confirm.
Since then more precise researches have proved that this verification was
only approximate; they have shown everywhere traces of elliptic
polarization. But, thanks to the help that the first approximation gave us, we
found forthwith the cause of these anomalies, which is the presence of a
transition layer; and Fresnel's theory has subsisted in its essentials.
But there is a reflection we can not help making: All these relations
would have remained unperceived if one had at first suspected the
complexity of the objects they connect. It has long been said: If Tycho had
had instruments ten times more precise neither Kepler, nor Newton, nor
astronomy would ever have been. It is a misfortune for a science to be born
too late, when the means of observation have become too perfect. This is to-
day the case with physical chemistry; its founders are embarrassed in their
general grasp by third and fourth decimals; happily they are men of a robust
faith.

The better one knows the properties of matter the more one sees
continuity reign. Since the labors of Andrews and of van der Waals, we get
an idea of how the passage is made from the liquid to the gaseous state and
that this passage is not abrupt. Similarly, there is no gap between the liquid
and solid states, and in the proceedings of a recent congress is to be seen,
alongside of a work on the rigidity of liquids, a memoir on the flow of
solids.
By this tendency no doubt simplicity loses; some phenomenon was
formerly represented by several straight lines, now these straights must be
joined by curves more or less complicated. In compensation unity gains
notably. Those cut-off categories quieted the mind, but they did not satisfy
it.
Finally the methods of physics have invaded a new domain, that of
chemistry; physical chemistry is born. It is still very young, but we already
see that it will enable us to connect such phenomena as electrolysis,
osmosis and the motions of ions.
From this rapid exposition, what shall we conclude?
Everything considered, we have approached unity; we have not been as
quick as was hoped fifty years ago, we have not always taken the predicted
way; but, finally, we have gained ever so much ground.

CHAPTER XI

The Calculus of Probabilities
Doubtless it will be astonishing to find here thoughts about the calculus
of probabilities. What has it to do with the method of the physical sciences?
And yet the questions I shall raise without solving present themselves
naturally to the philosopher who is thinking about physics. So far is this the
case that in the two preceding chapters I have often been led to use the
words 'probability' and 'chance.'

'Predicted facts,' as I have said above, 'can only be probable.' "However
solidly founded a prediction may seem to us to be, we are never absolutely
sure that experiment will not prove it false. But the probability is often so
great that practically we may be satisfied with it." And a little further on I
have added: "See what a rôle the belief in simplicity plays in our
generalizations. We have verified a simple law in a great number of
particular cases; we refuse to admit that this coincidence, so often repeated,
can be a mere effect of chance...."
Thus in a multitude of circumstances the physicist is in the same position
as the gambler who reckons up his chances. As often as he reasons by
induction, he requires more or less consciously the calculus of probabilities,
and this is why I am obliged to introduce a parenthesis, and interrupt our
study of method in the physical sciences in order to examine a little more
closely the value of this calculus, and what confidence it merits.
The very name calculus of probabilities is a paradox. Probability opposed
to certainty is what we do not know, and how can we calculate what we do
not know? Yet many eminent savants have occupied themselves with this
calculus, and it can not be denied that science has drawn therefrom no small
advantage.
How can we explain this apparent contradiction?
Has probability been defined? Can it even be defined? And if it can not,
how dare we reason about it? The definition, it will be said, is very simple:
the probability of an event is the ratio of the number of cases favorable to
this event to the total number of possible cases.
A simple example will show how incomplete this definition is. I throw
two dice. What is the probability that one of the two at least turns up a six?
Each die can turn up in six different ways; the number of possible cases is 6
× 6 = 36; the number of favorable cases is 11; the probability is 11/36.
That is the correct solution. But could I not just as well say: The points
which turn up on the two dice can form 6 × 7/2 = 21 different
combinations? Among these combinations 6 are favorable; the probability is
6/21.

Now why is the first method of enumerating the possible cases more
legitimate than the second? In any case it is not our definition that tells us.
We are therefore obliged to complete this definition by saying: '... to the
total number of possible cases provided these cases are equally probable.'
So, therefore, we are reduced to defining the probable by the probable.
How can we know that two possible cases are equally probable? Will it
be by a convention? If we place at the beginning of each problem an
explicit convention, well and good. We shall then have nothing to do but
apply the rules of arithmetic and of algebra, and we shall complete our
calculation without our result leaving room for doubt. But if we wish to
make the slightest application of this result, we must prove our convention
was legitimate, and we shall find ourselves in the presence of the very
difficulty we thought to escape.
Will it be said that good sense suffices to show us what convention
should be adopted? Alas! M. Bertrand has amused himself by discussing the
following simple problem: "What is the probability that a chord of a circle
may be greater than the side of the inscribed equilateral triangle?" The
illustrious geometer successively adopted two conventions which good
sense seemed equally to dictate and with one he found 1/2, with the other
1/3.
The conclusion which seems to follow from all this is that the calculus of
probabilities is a useless science, and that the obscure instinct which we
may call good sense, and to which we are wont to appeal to legitimatize our
conventions, must be distrusted.
But neither can we subscribe to this conclusion; we can not do without
this obscure instinct. Without it science would be impossible, without it we
could neither discover a law nor apply it. Have we the right, for instance, to
enunciate Newton's law? Without doubt, numerous observations are in
accord with it; but is not this a simple effect of chance? Besides how do we
know whether this law, true for so many centuries, will still be true next
year? To this objection, you will find nothing to reply, except: 'That is very
improbable.'

But grant the law. Thanks to it, I believe myself able to calculate the
position of Jupiter a year from now. Have I the right to believe this? Who
can tell if a gigantic mass of enormous velocity will not between now and
that time pass near the solar system, and produce unforeseen perturbations?
Here again the only answer is: 'It is very improbable.'
From this point of view, all the sciences would be only unconscious
applications of the calculus of probabilities. To condemn this calculus
would be to condemn the whole of science.
I shall dwell lightly on the scientific problems in which the intervention
of the calculus of probabilities is more evident. In the forefront of these is
the problem of interpolation, in which, knowing a certain number of values
of a function, we seek to divine the intermediate values.
I shall likewise mention: the celebrated theory of errors of observation, to
which I shall return later; the kinetic theory of gases, a well-known
hypothesis, wherein each gaseous molecule is supposed to describe an
extremely complicated trajectory, but in which, through the effect of great
numbers, the mean phenomena, alone observable, obey the simple laws of
Mariotte and Gay-Lussac.
All these theories are based on the laws of great numbers, and the
calculus of probabilities would evidently involve them in its ruin. It is true
that they have only a particular interest and that, save as far as interpolation
is concerned, these are sacrifices to which we might readily be resigned.
But, as I have said above, it would not be only these partial sacrifices that
would be in question; it would be the legitimacy of the whole of science
that would be challenged.
I quite see that it might be said: "We are ignorant, and yet we must act.
For action, we have not time to devote ourselves to an inquiry sufficient to
dispel our ignorance. Besides, such an inquiry would demand an infinite
time. We must therefore decide without knowing; we are obliged to do so,
hit or miss, and we must follow rules without quite believing them. What I
know is not that such and such a thing is true, but that the best course for
me is to act as if it were true." The calculus of probabilities, and

consequently science itself, would thenceforth have merely a practical
value.
Unfortunately the difficulty does not thus disappear. A gambler wants to
try a coup; he asks my advice. If I give it to him, I shall use the calculus of
probabilities, but I shall not guarantee success. This is what I shall call
subjective probability. In this case, we might be content with the
explanation of which I have just given a sketch. But suppose that an
observer is present at the game, that he notes all its coups, and that the game
goes on a long time. When he makes a summary of his book, he will find
that events have taken place in conformity with the laws of the calculus of
probabilities. This is what I shall call objective probability, and it is this
phenomenon which has to be explained.
There are numerous insurance companies which apply the rules of the
calculus of probabilities, and they distribute to their shareholders dividends
whose objective reality can not be contested. To invoke our ignorance and
the necessity to act does not suffice to explain them.
Thus absolute skepticism is not admissible. We may distrust, but we can
not condemn en bloc. Discussion is necessary.
I. Classification of the Problems of Probability.—In order to classify
the problems which present themselves à propos of probabilities, we may
look at them from many different points of view, and, first, from the point
of view of generality. I have said above that probability is the ratio of the
number of favorable cases to the number of possible cases. What for want
of a better term I call the generality will increase with the number of
possible cases. This number may be finite, as, for instance, if we take a
throw of the dice in which the number of possible cases is 36. That is the
first degree of generality.
But if we ask, for example, what is the probability that a point within a
circle is within the inscribed square, there are as many possible cases as
there are points in the circle, that is to say, an infinity. This is the second
degree of generality. Generality can be pushed further still. We may ask the
probability that a function will satisfy a given condition. There are then as
many possible cases as one can imagine different functions. This is the third

degree of generality, to which we rise, for instance, when we seek to find
the most probable law in conformity with a finite number of observations.
We may place ourselves at a point of view wholly different. If we were
not ignorant, there would be no probability, there would be room for
nothing but certainty. But our ignorance can not be absolute, for then there
would no longer be any probability at all, since a little light is necessary to
attain even this uncertain science. Thus the problems of probability may be
classed according to the greater or less depth of this ignorance.
In mathematics even we may set ourselves problems of probability. What
is the probability that the fifth decimal of a logarithm taken at random from
a table is a '9'? There is no hesitation in answering that this probability is
1/10; here we possess all the data of the problem. We can calculate our
logarithm without recourse to the table, but we do not wish to give
ourselves the trouble. This is the first degree of ignorance.
In the physical sciences our ignorance becomes greater. The state of a
system at a given instant depends on two things: Its initial state, and the law
according to which that state varies. If we know both this law and this
initial state, we shall have then only a mathematical problem to solve, and
we fall back upon the first degree of ignorance.
But it often happens that we know the law, and do not know the initial
state. It may be asked, for instance, what is the present distribution of the
minor planets? We know that from all time they have obeyed the laws of
Kepler, but we do not know what was their initial distribution.
In the kinetic theory of gases, we assume that the gaseous molecules
follow rectilinear trajectories, and obey the laws of impact of elastic bodies.
But, as we know nothing of their initial velocities, we know nothing of their
present velocities.
The calculus of probabilities only enables us to predict the mean
phenomena which will result from the combination of these velocities. This
is the second degree of ignorance.
Finally it is possible that not only the initial conditions but the laws
themselves are unknown. We then reach the third degree of ignorance and

in general we can no longer affirm anything at all as to the probability of a
phenomenon.
It often happens that instead of trying to guess an event, by means of a
more or less imperfect knowledge of the law, the events may be known and
we want to find the law; or that instead of deducing effects from causes, we
wish to deduce the causes from the effects. These are the problems called
probability of causes, the most interesting from the point of view of their
scientific applications.
I play écarté with a gentleman I know to be perfectly honest. He is about
to deal. What is the probability of his turning up the king? It is 1/8. This is a
problem of the probability of effects.
I play with a gentleman whom I do not know. He has dealt ten times, and
he has turned up the king six times. What is the probability that he is a
sharper? This is a problem in the probability of causes.
It may be said that this is the essential problem of the experimental
method. I have observed n values of x and the corresponding values of y. I
have found that the ratio of the latter to the former is practically constant.
There is the event, what is the cause?
Is it probable that there is a general law according to which y would be
proportional to x, and that the small divergencies are due to errors of
observation? This is a type of question that one is ever asking, and which
we unconsciously solve whenever we are engaged in scientific work.
I am now going to pass in review these different categories of problems,
discussing in succession what I have called above subjective and objective
probability.
II. Probability in Mathematics.—The impossibility of squaring the circle
has been proved since 1882; but even before that date all geometers
considered that impossibility as so 'probable,' that the Academy of Sciences
rejected without examination the alas! too numerous memoirs on this
subject, that some unhappy madmen sent in every year.
Was the Academy wrong? Evidently not, and it knew well that in acting
thus it did not run the least risk of stifling a discovery of moment. The

Academy could not have proved that it was right; but it knew quite well that
its instinct was not mistaken. If you had asked the Academicians, they
would have answered: "We have compared the probability that an unknown
savant should have found out what has been vainly sought for so long, with
the probability that there is one madman the more on the earth; the second
appears to us the greater." These are very good reasons, but there is nothing
mathematical about them; they are purely psychological.
And if you had pressed them further they would have added: "Why do
you suppose a particular value of a transcendental function to be an
algebraic number; and if π were a root of an algebraic equation, why do you
suppose this root to be a period of the function sin 2x, and not the same
about the other roots of this same equation?" To sum up, they would have
invoked the principle of sufficient reason in its vaguest form.
But what could they deduce from it? At most a rule of conduct for the
employment of their time, more usefully spent at their ordinary work than
in reading a lucubration that inspired in them a legitimate distrust. But what
I call above objective probability has nothing in common with this first
problem.
It is otherwise with the second problem.
Consider the first 10,000 logarithms that we find in a table. Among these
10,000 logarithms I take one at random. What is the probability that its third
decimal is an even number? You will not hesitate to answer 1/2; and in fact
if you pick out in a table the third decimals of these 10,000 numbers, you
will find nearly as many even digits as odd.
Or if you prefer, let us write 10,000 numbers corresponding to our 10,000
logarithms, each of these numbers being +1 if the third decimal of the
corresponding logarithm is even, and −1 if odd. Then take the mean of these
10,000 numbers.
I do not hesitate to say that the mean of these 10,000 numbers is probably
0, and if I were actually to calculate it I should verify that it is extremely
small.
But even this verification is needless. I might have rigorously proved that
this mean is less than 0.003. To prove this result, I should have had to make

a rather long calculation for which there is no room here, and for which I
confine myself to citing an article I published in the Revue générale des
Sciences, April 15, 1899. The only point to which I wish to call attention is
the following: in this calculation, I should have needed only to rest my case
on two facts, to wit, that the first and second derivatives of the logarithm
remain, in the interval considered, between certain limits.
Hence this important consequence that the property is true not only of the
logarithm, but of any continuous function whatever, since the derivatives of
every continuous function are limited.
If I was certain beforehand of the result, it is first, because I had often
observed analogous facts for other continuous functions; and next, because
I made in my mind, in a more or less unconscious and imperfect manner,
the reasoning which led me to the preceding inequalities, just as a skilled
calculator before finishing his multiplication takes into account what it
should come to approximately.
And besides, since what I call my intuition was only an incomplete
summary of a piece of true reasoning, it is clear why observation has
confirmed my predictions, and why the objective probability has been in
agreement with the subjective probability.
As a third example I shall choose the following problem: A number u is
taken at random, and n is a given very large integer. What is the probable
value of sin nu? This problem has no meaning by itself. To give it one a
convention is needed. We shall agree that the probability for the number u
to lie between a and a+ is equal to ϕ(a)da; that it is therefore proportional to
the infinitely small interval da, and equal to this multiplied by a function
ϕ(a) depending only on a. As for this function, I choose it arbitrarily, but I
must assume it to be continuous. The value of sin nu remaining the same
when u increases by 2π, I may without loss of generality assume that u lies
between 0 and 2π, and I shall thus be led to suppose that ϕ(a) is a periodic
function whose period is 2π.
The probable value sought is readily expressed by a simple integral, and
it is easy to show that this integral is less than

2πMk ⁄ nk,

Mk being the maximum value of the kth derivative of ϕ(u). We see then
that if the kth derivative is finite, our probable value will tend toward 0
when n increases indefinitely, and that more rapidly than 1/nk−1.
The probable value of sin nu when n is very large is therefore naught. To
define this value I required a convention; but the result remains the same
whatever that convention may be. I have imposed upon myself only slight
restrictions in assuming that the function ϕ(a) is continuous and periodic,
and these hypotheses are so natural that we may ask ourselves how they can
be escaped.
Examination of the three preceding examples, so different in all respects,
has already given us a glimpse, on the one hand, of the rôle of what
philosophers call the principle of sufficient reason, and, on the other hand,
of the importance of the fact that certain properties are common to all
continuous functions. The study of probability in the physical sciences will
lead us to the same result.
III. Probability in the Physical Sciences.—We come now to the
problems connected with what I have called the second degree of
ignorance, those, namely, in which we know the law, but do not know the
initial state of the system. I could multiply examples, but will take only one.
What is the probable present distribution of the minor planets on the
zodiac?
We know they obey the laws of Kepler. We may even, without at all
changing the nature of the problem, suppose that their orbits are all circular,
and situated in the same plane, and that we know this plane. On the other
hand, we are in absolute ignorance as to what was their initial distribution.
However, we do not hesitate to affirm that their distribution is now nearly
uniform. Why?
Let b be the longitude of a minor planet in the initial epoch, that is to say,
the epoch zero. Let a be its mean motion. Its longitude at the present epoch,
that is to say at the epoch t, will be at + b. To say that the present
distribution is uniform is to say that the mean value of the sines and cosines
of multiples of at + b is zero. Why do we assert this?

Let us represent each minor planet by a point in a plane, to wit, by a point
whose coordinates are precisely a and b. All these representative points will
be contained in a certain region of the plane, but as they are very numerous
this region will appear dotted with points. We know nothing else about the
distribution of these points.
What do we do when we wish to apply the calculus of probabilities to
such a question? What is the probability that one or more representative
points may be found in a certain portion of the plane? In our ignorance, we
are reduced to making an arbitrary hypothesis. To explain the nature of this
hypothesis, allow me to use, in lieu of a mathematical formula, a crude but
concrete image. Let us suppose that over the surface of our plane has been
spread an imaginary substance, whose density is variable, but varies
continuously. We shall then agree to say that the probable number of
representative points to be found on a portion of the plane is proportional to
the quantity of fictitious matter found there. If we have then two regions of
the plane of the same extent, the probabilities that a representative point of
one of our minor planets is found in one or the other of these regions will be
to one another as the mean densities of the fictitious matter in the one and
the other region.
Here then are two distributions, one real, in which the representative
points are very numerous, very close together, but discrete like the
molecules of matter in the atomic hypothesis; the other remote from reality,
in which our representative points are replaced by continuous fictitious
matter. We know that the latter can not be real, but our ignorance forces us
to adopt it.
If again we had some idea of the real distribution of the representative
points, we could arrange it so that in a region of some extent the density of
this imaginary continuous matter would be nearly proportional to the
number of the representative points, or, if you wish, to the number of atoms
which are contained in that region. Even that is impossible, and our
ignorance is so great that we are forced to choose arbitrarily the function
which defines the density of our imaginary matter. Only we shall be forced
to a hypothesis from which we can hardly get away, we shall suppose that
this function is continuous. That is sufficient, as we shall see, to enable us
to reach a conclusion.

What is at the instant t the probable distribution of the minor planets? Or
rather what is the probable value of the sine of the longitude at the instant t,
that is to say of sin (at + b)? We made at the outset an arbitrary convention,
but if we adopt it, this probable value is entirely defined. Divide the plane
into elements of surface. Consider the value of sin (at + b) at the center of
each of these elements; multiply this value by the surface of the element,
and by the corresponding density of the imaginary matter. Take then the
sum for all the elements of the plane. This sum, by definition, will be the
probable mean value we seek, which will thus be expressed by a double
integral. It may be thought at first that this mean value depends on the
choice of the function which defines the density of the imaginary matter,
and that, as this function ϕ is arbitrary, we can, according to the arbitrary
choice which we make, obtain any mean value. This is not so.
A simple calculation shows that our double integral decreases very
rapidly when t increases. Thus I could not quite tell what hypothesis to
make as to the probability of this or that initial distribution; but whatever
the hypothesis made, the result will be the same, and this gets me out of my
difficulty.
Whatever be the function ϕ, the mean value tends toward zero as t
increases, and as the minor planets have certainly accomplished a very great
number of revolutions, I may assert that this mean value is very small.
I may choose ϕ as I wish, save always one restriction: this function must
be continuous; and, in fact, from the point of view of subjective probability,
the choice of a discontinuous function would have been unreasonable. For
instance, what reason could I have for supposing that the initial longitude
might be exactly 0°, but that it could not lie between 0° and 1°?
But the difficulty reappears if we take the point of view of objective
probability, if we pass from our imaginary distribution in which the
fictitious matter was supposed continuous to the real distribution in which
our representative points form, as it were, discrete atoms.
The mean value of sin (at + b) will be represented quite simply by
(1/n) Σ sin (at + b),

n being the number of minor planets. In lieu of a double integral referring to
a continuous function, we shall have a sum of discrete terms. And yet no
one will seriously doubt that this mean value is practically very small.
Our representative points being very close together, our discrete sum will
in general differ very little from an integral.
An integral is the limit toward which a sum of terms tends when the
number of these terms is indefinitely increased. If the terms are very
numerous, the sum will differ very little from its limit, that is to say from
the integral, and what I said of this latter will still be true of the sum itself.
Nevertheless, there are exceptions. If, for instance, for all the minor
planets,
b = π/2 − at,
the longitude for all the planets at the time t would be π/2, and the mean
value would evidently be equal to unity. For this to be the case, it would be
necessary that at the epoch 0, the minor planets must have all been lying on
a spiral of peculiar form, with its spires very close together. Every one will
admit that such an initial distribution is extremely improbable (and, even
supposing it realized, the distribution would not be uniform at the present
time, for example, on January 1, 1913, but it would become so a few years
later).
Why then do we think this initial distribution improbable? This must be
explained, because if we had no reason for rejecting as improbable this
absurd hypothesis everything would break down, and we could no longer
make any affirmation about the probability of this or that present
distribution.
Once more we shall invoke the principle of sufficient reason to which we
must always recur. We might admit that at the beginning the planets were
distributed almost in a straight line. We might admit that they were
irregularly distributed. But it seems to us that there is no sufficient reason
for the unknown cause that gave them birth to have acted along a curve so
regular and yet so complicated, which would appear to have been expressly
chosen so that the present distribution would not be uniform.

IV. Rouge et Noir.—The questions raised by games of chance, such as
roulette, are, fundamentally, entirely analogous to those we have just
treated. For example, a wheel is partitioned into a great number of equal
subdivisions, alternately red and black. A needle is whirled with force, and
after having made a great number of revolutions, it stops before one of
these subdivisions. The probability that this division is red is evidently 1/2.
The needle describes an angle θ, including several complete revolutions. I
do not know what is the probability that the needle may be whirled with a
force such that this angle should lie between θ and θ + dθ; but I can make a
convention. I can suppose that this probability is ϕ(θ)dθ. As for the function
ϕ(θ), I can choose it in an entirely arbitrary manner. There is nothing that
can guide me in my choice, but I am naturally led to suppose this function
continuous.
Let ε be the length (measured on the circumference of radius 1) of each
red and black subdivision. We have to calculate the integral of ϕ(θ)dθ,
extending it, on the one hand, to all the red divisions and, on the other hand,
to all the black divisions, and to compare the results.
Consider an interval 2ε, comprising a red division and a black division
which follows it. Let M and m be the greatest and least values of the
function ϕ(θ) in this interval. The integral extended to the red divisions will
be smaller than ΣMε; the integral extended to the black divisions will be
greater than Σmε; the difference will therefore be less than Σ(M − m)ε. But,
if the function θ is supposed continuous; if, besides, the interval ε is very
small with respect to the total angle described by the needle, the difference
M − m will be very small. The difference of the two integrals will therefore
be very small, and the probability will be very nearly 1/2.
We see that without knowing anything of the function θ, I must act as if
the probability were 1/2. We understand, on the other hand, why, if, placing
myself at the objective point of view, I observe a certain number of coups,
observation will give me about as many black coups as red.
All players know this objective law; but it leads them into a remarkable
error, which has been often exposed, but into which they always fall again.
When the red has won, for instance, six times running, they bet on the

black, thinking they are playing a safe game; because, say they, it is very
rare that red wins seven times running.
In reality their probability of winning remains 1/2. Observation shows, it
is true, that series of seven consecutive reds are very rare, but series of six
reds followed by a black are just as rare.
They have noticed the rarity of the series of seven reds; if they have not
remarked the rarity of six reds and a black, it is only because such series
strike the attention less.
V. The Probability of Causes.—We now come to the problems of the
probability of causes, the most important from the point of view of
scientific applications. Two stars, for instance, are very close together on
the celestial sphere. Is this apparent contiguity a mere effect of chance? Are
these stars, although on almost the same visual ray, situated at very different
distances from the earth, and consequently very far from one another? Or,
perhaps, does the apparent correspond to a real contiguity? This is a
problem on the probability of causes.
I recall first that at the outset of all problems of the probability of effects
that have hitherto occupied us, we have always had to make a convention,
more or less justified. And if in most cases the result was, in a certain
measure, independent of this convention, this was only because of certain
hypotheses which permitted us to reject a priori discontinuous functions,
for example, or certain absurd conventions.
We shall find something analogous when we deal with the probability of
causes. An effect may be produced by the cause A or by the cause B. The
effect has just been observed. We ask the probability that it is due to the
cause A. This is an a posteriori probability of cause. But I could not
calculate it, if a convention more or less justified did not tell me in advance
what is the a priori probability for the cause A to come into play; I mean the
probability of this event for some one who had not observed the effect.
The better to explain myself I go back to the example of the game of
écarté mentioned above. My adversary deals for the first time and he turns
up a king. What is the probability that he is a sharper? The formulas
ordinarily taught give 8/9, a result evidently rather surprising. If we look at

it closer, we see that the calculation is made as if, before sitting down at the
table, I had considered that there was one chance in two that my adversary
was not honest. An absurd hypothesis, because in that case I should have
certainly not played with him, and this explains the absurdity of the
conclusion.
The convention about the a priori probability was unjustified, and that is
why the calculation of the a posteriori probability led me to an inadmissible
result. We see the importance of this preliminary convention. I shall even
add that if none were made, the problem of the a posteriori probability
would have no meaning. It must always be made either explicitly or tacitly.
Pass to an example of a more scientific character. I wish to determine an
experimental law. This law, when I know it, can be represented by a curve. I
make a certain number of isolated observations; each of these will be
represented by a point. When I have obtained these different points, I draw
a curve between them, striving to pass as near to them as possible and yet
preserve for my curve a regular form, without angular points, or inflections
too accentuated, or brusque variation of the radius of curvature. This curve
will represent for me the probable law, and I assume not only that it will tell
me the values of the function intermediate between those which have been
observed, but also that it will give me the observed values themselves more
exactly than direct observation. This is why I make it pass near the points,
and not through the points themselves.
Here is a problem in the probability of causes. The effects are the
measurements I have recorded; they depend on a combination of two
causes: the true law of the phenomenon and the errors of observation.
Knowing the effects, we have to seek the probability that the phenomenon
obeys this law or that, and that the observations have been affected by this
or that error. The most probable law then corresponds to the curve traced,
and the most probable error of an observation is represented by the distance
of the corresponding point from this curve.
But the problem would have no meaning if, before any observation, I had
not fashioned an a priori idea of the probability of this or that law, and of
the chances of error to which I am exposed.

If my instruments are good (and that I knew before making the
observations), I shall not permit my curve to depart much from the points
which represent the rough measurements. If they are bad, I may go a little
further away from them in order to obtain a less sinuous curve; I shall
sacrifice more to regularity.
Why then is it that I seek to trace a curve without sinuosities? It is
because I consider a priori a law represented by a continuous function (or
by a function whose derivatives of high order are small), as more probable
than a law not satisfying these conditions. Without this belief, the problem
of which we speak would have no meaning; interpolation would be
impossible; no law could be deduced from a finite number of observations;
science would not exist.
Fifty years ago physicists considered, other things being equal, a simple
law as more probable than a complicated law. They even invoked this
principle in favor of Mariotte's law as against the experiments of Regnault.
To-day they have repudiated this belief; and yet, how many times are they
compelled to act as though they still held it! However that may be, what
remains of this tendency is the belief in continuity, and we have just seen
that if this belief were to disappear in its turn, experimental science would
become impossible.
VI. The Theory of Errors.—We are thus led to speak of the theory of
errors, which is directly connected with the problem of the probability of
causes. Here again we find effects, to wit, a certain number of discordant
observations, and we seek to divine the causes, which are, on the one hand,
the real value of the quantity to be measured; on the other hand, the error
made in each isolated observation. It is necessary to calculate what is a
posteriori the probable magnitude of each error, and consequently the
probable value of the quantity to be measured.
But as I have just explained, we should not know how to undertake this
calculation if we did not admit a priori, that is to say, before all observation,
a law of probability of errors. Is there a law of errors?
The law of errors admitted by all calculators is Gauss's law, which is
represented by a certain transcendental curve known under the name of 'the
bell.'

But first it is proper to recall the classic distinction between systematic
and accidental errors. If we measure a length with too long a meter, we shall
always find too small a number, and it will be of no use to measure several
times; this is a systematic error. If we measure with an accurate meter, we
may, however, make a mistake; but we go wrong, now too much, now too
little, and when we take the mean of a great number of measurements, the
error will tend to grow small. These are accidental errors.
It is evident from the first that systematic errors can not satisfy Gauss's
law; but do the accidental errors satisfy it? A great number of
demonstrations have been attempted; almost all are crude paralogisms.
Nevertheless, we may demonstrate Gauss's law by starting from the
following hypotheses: the error committed is the result of a great number of
partial and independent errors; each of the partial errors is very little and
besides, obeys any law of probability, provided that the probability of a
positive error is the same as that of an equal negative error. It is evident that
these conditions will be often but not always fulfilled, and we may reserve
the name of accidental for errors which satisfy them.
We see that the method of least squares is not legitimate in every case; in
general the physicists are more distrustful of it than the astronomers. This
is, no doubt, because the latter, besides the systematic errors to which they
and the physicists are subject alike, have to control with an extremely
important source of error which is wholly accidental; I mean atmospheric
undulations. So it is very curious to hear a physicist discuss with an
astronomer about a method of observation. The physicist, persuaded that
one good measurement is worth more than many bad ones, is before all
concerned with eliminating by dint of precautions the least systematic
errors, and the astronomer says to him: 'But thus you can observe only a
small number of stars; the accidental errors will not disappear.'
What should we conclude? Must we continue to use the method of least
squares? We must distinguish. We have eliminated all the systematic errors
we could suspect; we know well there are still others, but we can not detect
them; yet it is necessary to make up our mind and adopt a definitive value
which will be regarded as the probable value; and for that it is evident the
best thing to do is to apply Gauss's method. We have only applied a

practical rule referring to subjective probability. There is nothing more to be
said.
But we wish to go farther and affirm that not only is the probable value
so much, but that the probable error in the result is so much. This is
absolutely illegitimate; it would be true only if we were sure that all the
systematic errors were eliminated, and of that we know absolutely nothing.
We have two series of observations; by applying the rule of least squares,
we find that the probable error in the first series is twice as small as in the
second. The second series may, however, be better than the first, because
the first perhaps is affected by a large systematic error. All we can say is
that the first series is probably better than the second, since its accidental
error is smaller, and we have no reason to affirm that the systematic error is
greater for one of the series than for the other, our ignorance on this point
being absolute.
VII. Conclusions.—In the lines which precede, I have set many problems
without solving any of them. Yet I do not regret having written them,
because they will perhaps invite the reader to reflect on these delicate
questions.
However that may be, there are certain points which seem well
established. To undertake any calculation of probability, and even for that
calculation to have any meaning, it is necessary to admit, as point of
departure, a hypothesis or convention which has always something arbitrary
about it. In the choice of this convention, we can be guided only by the
principle of sufficient reason. Unfortunately this principle is very vague and
very elastic, and in the cursory examination we have just made, we have
seen it take many different forms. The form under which we have met it
most often is the belief in continuity, a belief which it would be difficult to
justify by apodeictic reasoning, but without which all science would be
impossible. Finally the problems to which the calculus of probabilities may
be applied with profit are those in which the result is independent of the
hypothesis made at the outset, provided only that this hypothesis satisfies
the condition of continuity.

CHAPTER XII

Optics and Electricity
Fresnel's Theory.—The best example[5] that can be chosen of physics in
the making is the theory of light and its relations to the theory of electricity.
Thanks to Fresnel, optics is the best developed part of physics; the so-called
wave-theory forms a whole truly satisfying to the mind. We must not,
however, ask of it what it can not give us.
The object of mathematical theories is not to reveal to us the true nature
of things; this would be an unreasonable pretension. Their sole aim is to
coordinate the physical laws which experiment reveals to us, but which,
without the help of mathematics, we should not be able even to state.
It matters little whether the ether really exists; that is the affair of
metaphysicians. The essential thing for us is that everything happens as if it
existed, and that this hypothesis is convenient for the explanation of
phenomena. After all, have we any other reason to believe in the existence
of material objects? That, too, is only a convenient hypothesis; only this
will never cease to be so, whereas, no doubt, some day the ether will be
thrown aside as useless. But even at that day, the laws of optics and the
equations which translate them analytically will remain true, at least as a
first approximation. It will always be useful, then, to study a doctrine that
unites all these equations.
The undulatory theory rests on a molecular hypothesis. For those who
think they have thus discovered the cause under the law, this is an
advantage. For the others it is a reason for distrust. But this distrust seems
to me as little justified as the illusion of the former.
These hypotheses play only a secondary part. They might be sacrificed.
They usually are not, because then the explanation would lose in clearness;
but that is the only reason.
In fact, if we looked closer we should see that only two things are
borrowed from the molecular hypotheses: the principle of the conservation

of energy and the linear form of the equations, which is the general law of
small movements, as of all small variations.
This explains why most of Fresnel's conclusions remain unchanged when
we adopt the electromagnetic theory of light.
Maxwell's Theory.—Maxwell, we know, connected by a close bond two
parts of physics until then entirely foreign to one another, optics and
electricity. By blending thus in a vaster whole, in a higher harmony, the
optics of Fresnel has not ceased to be alive. Its various parts subsist, and
their mutual relations are still the same. Only the language we used to
express them has changed; and, on the other hand, Maxwell has revealed to
us other relations, before unsuspected, between the different parts of optics
and the domain of electricity.
When a French reader first opens Maxwell's book, a feeling of uneasiness
and often even of mistrust mingles at first with his admiration. Only after a
prolonged acquaintance and at the cost of many efforts does this feeling
disappear. There are even some eminent minds that never lose it.
Why are the English scientist's ideas with such difficulty acclimatized
among us? It is, no doubt, because the education received by the majority of
enlightened Frenchmen predisposes them to appreciate precision and logic
above every other quality.
The old theories of mathematical physics gave us in this respect complete
satisfaction. All our masters, from Laplace to Cauchy, have proceeded in
the same way. Starting from clearly stated hypotheses, they deduced all
their consequences with mathematical rigor, and then compared them with
experiment. It seemed their aim to give every branch of physics the same
precision as celestial mechanics.
A mind accustomed to admire such models is hard to suit with a theory.
Not only will it not tolerate the least appearance of contradiction, but it will
demand that the various parts be logically connected with one another, and
that the number of distinct hypotheses be reduced to minimum.
This is not all; it will have still other demands, which seem to me less
reasonable. Behind the matter which our senses can reach, and which
experiment tells us of, it will desire to see another, and in its eyes the only

real, matter, which will have only purely geometric properties, and whose
atoms will be nothing but mathematical points, subject to the laws of
dynamics alone. And yet these atoms, invisible and without color, it will
seek by an unconscious contradiction to represent to itself and consequently
to identify as closely as possible with common matter.
Then only will it be fully satisfied and imagine that it has penetrated the
secret of the universe. If this satisfaction is deceitful, it is none the less
difficult to renounce.
Thus, on opening Maxwell, a Frenchman expects to find a theoretical
whole as logical and precise as the physical optics based on the hypothesis
of the ether; he thus prepares for himself a disappointment which I should
like to spare the reader by informing him immediately of what he must look
for in Maxwell, and what he can not find there.
Maxwell does not give a mechanical explanation of electricity and
magnetism; he confines himself to demonstrating that such an explanation
is possible.
He shows also that optical phenomena are only a special case of
electromagnetic phenomena. From every theory of electricity, one can
therefore deduce immediately a theory of light.
The converse unfortunately is not true; from a complete explanation of
light, it is not always easy to derive a complete explanation of electric
phenomena. This is not easy, in particular, if we wish to start from Fresnel's
theory. Doubtless it would not be impossible; but nevertheless we must ask
whether we are not going to be forced to renounce admirable results that we
thought definitely acquired. That seems a step backward; and many good
minds are not willing to submit to it.
When the reader shall have consented to limit his hopes, he will still
encounter other difficulties. The English scientist does not try to construct a
single edifice, final and well ordered; he seems rather to erect a great
number of provisional and independent constructions, between which
communication is difficult and sometimes impossible.
Take as example the chapter in which he explains electrostatic attractions
by pressures and tensions in the dielectric medium. This chapter might be

omitted without making thereby the rest of the book less clear or complete;
and, on the other hand, it contains a theory complete in itself which one
could understand without having read a single line that precedes or follows.
But it is not only independent of the rest of the work; it is difficult to
reconcile with the fundamental ideas of the book. Maxwell does not even
attempt this reconciliation; he merely says: "I have not been able to make
the next step, namely, to account by mechanical considerations for these
stresses in the dielectric."
This example will suffice to make my thought understood; I could cite
many others. Thus who would suspect, in reading the pages devoted to
magnetic rotary polarization, that there is an identity between optical and
magnetic phenomena?
One must not then flatter himself that he can avoid all contradiction; to
that it is necessary to be resigned. In fact, two contradictory theories,
provided one does not mingle them, and if one does not seek in them the
basis of things, may both be useful instruments of research; and perhaps the
reading of Maxwell would be less suggestive if he had not opened up to us
so many new and divergent paths.
The fundamental idea, however, is thus a little obscured. So far is this the
case that in the majority of popularized versions it is the only point
completely left aside.
I feel, then, that the better to make its importance stand out, I ought to
explain in what this fundamental idea consists. But for that a short
digression is necessary.
The Mechanical Explanation of Physical Phenomena.—There is in
every physical phenomenon a certain number of parameters which
experiment reaches directly and allows us to measure. I shall call these the
parameters q.
Observation then teaches us the laws of the variations of these
parameters; and these laws can generally be put in the form of differential
equations, which connect the parameters q with the time.
What is it necessary to do to give a mechanical interpretation of such a
phenomenon?

One will try to explain it either by the motions of ordinary matter, or by
those of one or more hypothetical fluids.
These fluids will be considered as formed of a very great number of
isolated molecules m.
When shall we say, then, that we have a complete mechanical
explanation of the phenomenon? It will be, on the one hand, when we know
the differential equations satisfied by the coordinates of these hypothetical
molecules m, equations which, moreover, must conform to the principles of
dynamics; and, on the other hand, when we know the relations that define
the coordinates of the molecules m as functions of the parameters q
accessible to experiment.
These equations, as I have said, must conform to the principles of
dynamics, and, in particular, to the principle of the conservation of energy
and the principle of least action.
The first of these two principles teaches us that the total energy is
constant and that this energy is divided into two parts:
1º The kinetic energy, or vis viva, which depends on the masses of the
hypothetical molecules m, and their velocities, and which I shall call T.
2º The potential energy, which depends only on the coordinates of these
molecules and which I shall call U. It is the sum of the two energies T and U
which is constant.
What now does the principle of least action tell us? It tells us that to pass
from the initial position occupied at the instant t0 to the final position
occupied at the instant t1, the system must take such a path that, in the
interval of time that elapses between the two instants t0 and t1, the average
value of 'the action' (that is to say, of the difference between the two
energies T and U) shall be as small as possible.
If the two functions T and U are known, this principle suffices to
determine the equations of motion.
Among all the possible ways of passing from one position to another,
there is evidently one for which the average value of the action is less than

for any other. There is, moreover, only one; and it results from this that the
principle of least action suffices to determine the path followed and
consequently the equations of motion.
Thus we obtain what are called the equations of Lagrange.
In these equations, the independent variables are the coordinates of the
hypothetical molecules m; but I now suppose that one takes as variables the
parameters q directly accessible to experiment.
The two parts of the energy must then be expressed as functions of the
parameters q and of their derivatives. They will evidently appear under this
form to the experimenter. The latter will naturally try to define the potential
and the kinetic energy by the aid of quantities that he can directly observe.
[6]

That granted, the system will always go from one position to another by a
path such that the average action shall be a minimum.
It matters little that T and U are now expressed by the aid of the
parameters q and their derivatives; it matters little that it is also by means of
these parameters that we define the initial and final positions; the principle
of least action remains always true.
Now here again, of all the paths that lead from one position to another,
there is one for which the average action is a minimum, and there is only
one. The principle of least action suffices, then, to determine the differential
equations which define the variations of the parameters q.
The equations thus obtained are another form of the equations of
Lagrange.
To form these equations we need to know neither the relations that
connect the parameters q with the coordinates of the hypothetical
molecules, nor the masses of these molecules, nor the expression of U as a
function of the coordinates of these molecules.
All we need to know is the expression of U as a function of the
parameters, and that of T as a function of the parameters q and their

derivatives, that is, the expressions of the kinetic and of the potential energy
as functions of the experimental data.
Then we shall have one of two things: either for a suitable choice of the
functions T and U, the equations of Lagrange, constructed as we have just
said, will be identical with the differential equations deduced from
experiments; or else there will exist no functions T and U, for which this
agreement takes place. In the latter case it is clear that no mechanical
explanation is possible.
The necessary condition for a mechanical explanation to be possible is
therefore that we can choose the functions T and U in such a way as to
satisfy the principle of least action, which involves that of the conservation
of energy.
This condition, moreover, is sufficient. Suppose, in fact, that we have
found a function U of the parameters q, which represents one of the parts of
the energy; that another part of the energy, which we shall represent by T, is
a function of the parameters q and their derivatives, and that it is a
homogeneous polynomial of the second degree with respect to these
derivatives; and finally that the equations of Lagrange, formed by means of
these two functions, T and U, conform to the data of the experiment.
What is necessary in order to deduce from this a mechanical explanation?
It is necessary that U can be regarded as the potential energy of a system
and T as the vis viva of the same system.
There is no difficulty as to U, but can T be regarded as the vis viva of a
material system?
It is easy to show that this is always possible, and even in an infinity of
ways. I will confine myself to referring for more details to the preface of
my work, 'Électricité et optique.'
Thus if the principle of least action can not be satisfied, no mechanical
explanation is possible; if it can be satisfied, there is not only one, but an
infinity, whence it follows that as soon as there is one there is an infinity of
others.
One more observation.

Among the quantities that experiment gives us directly, we shall regard
some as functions of the coordinates of our hypothetical molecules; these
are our parameters q. We shall look upon the others as dependent not only
on the coordinates, but on the velocities, or, what comes to the same thing,
on the derivatives of the parameters q, or as combinations of these
parameters and their derivatives.
And then a question presents itself: among all these quantities measured
experimentally, which shall we choose to represent the parameters q?
Which shall we prefer to regard as the derivatives of these parameters? This
choice remains arbitrary to a very large extent; but, for a mechanical
explanation to be possible, it suffices if we can make the choice in such a
way as to accord with the principle of least action.
And then Maxwell asked himself whether he could make this choice and
that of the two energies T and U, in such a way that the electrical
phenomena would satisfy this principle. Experiment shows us that the
energy of an electromagnetic field is decomposed into two parts, the
electrostatic energy and the electrodynamic energy. Maxwell observed that
if we regard the first as representing the potential energy U, the second as
representing the kinetic energy T; if, moreover, the electrostatic charges of
the conductors are considered as parameters q and the intensities of the
currents as the derivatives of other parameters q; under these conditions, I
say, Maxwell observed that the electric phenomena satisfy the principle of
least action. Thenceforth he was certain of the possibility of a mechanical
explanation.
If he had explained this idea at the beginning of his book instead of
relegating it to an obscure part of the second volume, it would not have
escaped the majority of readers.
If, then, a phenomenon admits of a complete mechanical explanation, it
will admit of an infinity of others, that will render an account equally well
of all the particulars revealed by experiment.
And this is confirmed by the history of every branch of physics; in optics,
for instance, Fresnel believed vibration to be perpendicular to the plane of
polarization; Neumann regarded it as parallel to this plane. An

'experimentum crucis' has long been sought which would enable us to
decide between these two theories, but it has not been found.
In the same way, without leaving the domain of electricity, we may
ascertain that the theory of two fluids and that of the single fluid both
account in a fashion equally satisfactory for all the observed laws of
electrostatics.
All these facts are easily explicable, thanks to the properties of the
equations of Lagrange which I have just recalled.
It is easy now to comprehend what is Maxwell's fundamental idea.
To demonstrate the possibility of a mechanical explanation of electricity,
we need not preoccupy ourselves with finding this explanation itself; it
suffices us to know the expression of the two functions T and U, which are
the two parts of energy, to form with these two functions the equations of
Lagrange and then to compare these equations with the experimental laws.
Among all these possible explanations, how make a choice for which the
aid of experiment fails us? A day will come perhaps when physicists will
not interest themselves in these questions, inaccessible to positive methods,
and will abandon them to the metaphysicians. This day has not yet arrived;
man does not resign himself so easily to be forever ignorant of the
foundation of things.
Our choice can therefore be further guided only by considerations where
the part of personal appreciation is very great; there are, however, solutions
that all the world will reject because of their whimsicality, and others that
all the world will prefer because of their simplicity.
In what concerns electricity and magnetism, Maxwell abstains from
making any choice. It is not that he systematically disdains all that is
unattainable by positive methods; the time he has devoted to the kinetic
theory of gases sufficiently proves that. I will add that if, in his great work,
he develops no complete explanation, he had previously attempted to give
one in an article in the Philosophical Magazine. The strangeness and the
complexity of the hypotheses he had been obliged to make had led him
afterwards to give this up.

The same spirit is found throughout the whole work. What is essential,
that is to say what must remain common to all theories, is made prominent;
all that would only be suitable to a particular theory is nearly always passed
over in silence. Thus the reader finds himself in the presence of a form
almost devoid of matter, which he is at first tempted to take for a fugitive
shadow not to be grasped. But the efforts to which he is thus condemned
force him to think and he ends by comprehending what was often rather
artificial in the theoretic constructs he had previously only wondered at.

CHAPTER XIII

Electrodynamics
The history of electrodynamics is particularly instructive from our point
of view.
Ampère entitled his immortal work, 'Théorie des phénomènes
électrodynamiques, uniquement fondée sur l'expérience.' He therefore
imagined that he had made no hypothesis, but he had made them, as we
shall soon see; only he made them without being conscious of it.
His successors, on the other hand, perceived them, since their attention
was attracted by the weak points in Ampère's solution. They made new
hypotheses, of which this time they were fully conscious; but how many
times it was necessary to change them before arriving at the classic system
of to-day which is perhaps not yet final; this we shall see.
I. Ampere's Theory.—When Ampère studied experimentally the mutual
actions of currents, he operated and he only could operate with closed
currents.
It was not that he denied the possibility of open currents. If two
conductors are charged with positive and negative electricity and brought
into communication by a wire, a current is established going from one to
the other, which continues until the two potentials are equal. According to
the ideas of Ampère's time this was an open current; the current was known

to go from the first conductor to the second, it was not seen to return from
the second to the first.
So Ampère considered as open currents of this nature, for example, the
currents of discharge of condensers; but he could not make them the objects
of his experiments because their duration is too short.
Another sort of open current may also be imagined. I suppose two
conductors, A and B, connected by a wire AMB. Small conducting masses in
motion first come in contact with the conductor B, take from it an electric
charge, leave contact with B and move along the path BNA, and,
transporting with them their charge, come into contact with A and give to it
their charge, which returns then to B along the wire AMB.
Now there we have in a sense a closed circuit, since the electricity
describes the closed circuit BNAMB; but the two parts of this current are
very different. In the wire AMB, the electricity is displaced through a fixed
conductor, like a voltaic current, overcoming an ohmic resistance and
developing heat; we say that it is displaced by conduction. In the part BNA,
the electricity is carried by a moving conductor; it is said to be displaced by
convection.
If then the current of convection is considered as altogether analogous to
the current of conduction, the circuit BNAMB is closed; if, on the contrary,
the convection current is not 'a true current' and, for example, does not act
on the magnet, there remains only the conduction current AMB, which is
open.
For example, if we connect by a wire the two poles of a Holtz machine,
the charged rotating disc transfers the electricity by convection from one
pole to the other, and it returns to the first pole by conduction through the
wire.
But currents of this sort are very difficult to produce with appreciable
intensity. With the means at Ampère's disposal, we may say that this was
impossible.
To sum up, Ampère could conceive of the existence of two kinds of open
currents, but he could operate on neither because they were not strong
enough or because their duration was too short.

Experiment therefore could only show him the action of a closed current
on a closed current, or, more accurately, the action of a closed current on a
portion of a current, because a current can be made to describe a closed
circuit composed of a moving part and a fixed part. It is possible then to
study the displacements of the moving part under the action of another
closed current.
On the other hand, Ampère had no means of studying the action of an
open current, either on a closed current or another open current.
1. The Case of Closed Currents.—In the case of the mutual action of two
closed currents, experiment revealed to Ampère remarkably simple laws.
I recall rapidly here those which will be useful to us in the sequel:
1º If the intensity of the currents is kept constant, and if the two circuits,
after having undergone any deformations and displacements whatsoever,
return finally to their initial positions, the total work of the electrodynamic
actions will be null.
In other words, there is an electrodynamic potential of the two circuits,
proportional to the product of the intensities, and depending on the form
and relative position of the circuits; the work of the electrodynamic actions
is equal to the variation of this potential.
2º The action of a closed solenoid is null.
3º The action of a circuit C on another voltaic circuit C´ depends only on
the 'magnetic field' developed by this circuit. At each point in space we can
in fact define in magnitude and direction a certain force called magnetic
force, which enjoys the following properties:
(a) The force exercised by C on a magnetic pole is applied to that pole
and is equal to the magnetic force multiplied by the magnetic mass of that
pole;
(b) A very short magnetic needle tends to take the direction of the
magnetic force, and the couple to which it tends to reduce is proportional to
the magnetic force, the magnetic moment of the needle and the sine of the
dip of the needle;

(c) If the circuit C is displaced, the work of the electrodynamic action
exercised by C on C´ will be equal to the increment of the 'flow of magnetic
force' which passes through the circuit.
2. Action of a Closed Current on a Portion of Current.—Ampère not
having been able to produce an open current, properly so called, had only
one way of studying the action of a closed current on a portion of current.
This was by operating on a circuit C composed of two parts, the one
fixed, the other movable. The movable part was, for instance, a movable
wire αβ whose extremities α and β could slide along a fixed wire. In one of
the positions of the movable wire, the end α rested on the A of the fixed
wire and the extremity β on the point B of the fixed wire. The current
circulated from α to β, that is to say, from A to B along the movable wire,
and then it returned from B to A along the fixed wire. This current was
therefore closed.
In a second position, the movable wire having slipped, the extremity α
rested on another point A´ of the fixed wire, and the extremity β on another
point B´ of the fixed wire. The current circulated then from α to β, that is to
say from A´ to B´ along the movable wire, and it afterwards returned from B
´ to B, then from B to A, then finally from A to A´, always following the
fixed wire. The current was therefore also closed.
If a like current is subjected to the action of a closed current C, the
movable part will be displaced just as if it were acted upon by a force.
Ampère assumes that the apparent force to which this movable part AB
seems thus subjected, representing the action of the C on the portion αβ of
the current, is the same as if αβ were traversed by an open current, stopping
at α and β, in place of being traversed by a closed current which after
arriving at β returns to α through the fixed part of the circuit.
This hypothesis seems natural enough, and Ampère made it
unconsciously; nevertheless it is not necessary, since we shall see further on
that Helmholtz rejected it. However that may be, it permitted Ampère,
though he had never been able to produce an open current, to enunciate the
laws of the action of a closed current on an open current, or even on an
element of current.

The laws are simple:
1º The force which acts on an element of current is applied to this
element; it is normal to the element and to the magnetic force, and
proportional to the component of this magnetic force which is normal to the
element.
2º The action of a closed solenoid on an element of current is null.
But the electrodynamic potential has disappeared, that is to say that,
when a closed current and an open current, whose intensities have been
maintained constant, return to their initial positions, the total work is not
null.
3. Continuous Rotations.—Among electrodynamic experiments, the most
remarkable are those in which continuous rotations are produced and which
are sometimes called unipolar induction experiments. A magnet may turn
about its axis; a current passes first through a fixed wire, enters the magnet
by the pole N, for example, passes through half the magnet, emerges by a
sliding contact and reenters the fixed wire.
The magnet then begins to rotate continuously without being able ever to
attain equilibrium; this is Faraday's experiment.
How is it possible? If it were a question of two circuits of invariable
form, the one C fixed, the other C´ movable about an axis, this latter could
never take on continuous rotation; in fact there is an electrodynamic
potential; there must therefore be necessarily a position of equilibrium
when this potential is a maximum.
Continuous rotations are therefore possible only when the circuit C´ is
composed of two parts: one fixed, the other movable about an axis, as is the
case in Faraday's experiment. Here again it is convenient to draw a
distinction. The passage from the fixed to the movable part, or inversely,
may take place either by simple contact (the same point of the movable part
remaining constantly in contact with the same point of the fixed part), or by
a sliding contact (the same point of the movable part coming successively
in contact with diverse points of the fixed part).

It is only in the second case that there can be continuous rotation. This is
what then happens: The system tends to take a position of equilibrium; but,
when at the point of reaching that position, the sliding contact puts the
movable part in communication with a new point of the fixed part; it
changes the connections, it changes therefore the conditions of equilibrium,
so that the position of equilibrium fleeing, so to say, before the system
which seeks to attain it, rotation may take place indefinitely.
Ampère assumes that the action of the circuit on the movable part of C´
is the same as if the fixed part of C´ did not exist, and therefore as if the
current passing through the movable part were open.
He concludes therefore that the action of a closed on an open current, or
inversely that of an open current on a closed current, may give rise to a
continuous rotation.
But this conclusion depends on the hypothesis I have enunciated and
which, as I said above, is not admitted by Helmholtz.
4. Mutual Action of Two Open Currents.—In what concerns the mutual
actions of two open currents, and in particular that of two elements of
current, all experiment breaks down. Ampère has recourse to hypothesis. He
supposes:
1º That the mutual action of two elements reduces to a force acting along
their join;
2º That the action of two closed currents is the resultant of the mutual
actions of their diverse elements, which are besides the same as if these
elements were isolated.
What is remarkable is that here again Ampère makes these hypotheses
unconsciously.
However that may be, these two hypotheses, together with the
experiments on closed currents, suffice to determine completely the law of
the mutual action of two elements. But then most of the simple laws we
have met in the case of closed currents are no longer true.

In the first place, there is no electrodynamic potential; nor was there any,
as we have seen, in the case of a closed current acting on an open current.
Next there is, properly speaking, no magnetic force.
And, in fact, we have given above three different definitions of this force:
1º By the action on a magnetic pole;
2º By the director couple which orientates the magnetic needle;
3º By the action on an element of current.
But in the case which now occupies us, not only these three definitions
are no longer in harmony, but each has lost its meaning, and in fact:
1º A magnetic pole is no longer acted upon simply by a single force
applied to this pole. We have seen in fact that the force due to the action of
an element of current on a pole is not applied to the pole, but to the element;
it may moreover be replaced by a force applied to the pole and by a couple;
2º The couple which acts on the magnetic needle is no longer a simple
director couple, for its moment with respect to the axis of the needle is not
null. It breaks up into a director couple, properly so called, and a
supplementary couple which tends to produce the continuous rotation of
which we have above spoken;
3º Finally the force acting on an element of current is not normal to this
element.
In other words, the unity of the magnetic force has disappeared.
Let us see in what this unity consists. Two systems which exercise the
same action on a magnetic pole will exert also the same action on an
indefinitely small magnetic needle, or on an element of current placed at the
same point of space as this pole.
Well, this is true if these two systems contain only closed currents; this
would no longer be true if these two systems contained open currents.
It suffices to remark, for instance, that, if a magnetic pole is placed at A
and an element at B, the direction of the element being along the

prolongation of the sect AB, this element which will exercise no action on
this pole will, on the other hand, exercise an action either on a magnetic
needle placed at the point A, or on an element of current placed at the point
A.
5. Induction.—We know that the discovery of electrodynamic induction
soon followed the immortal work of Ampère.
As long as it is only a question of closed currents there is no difficulty,
and Helmholtz has even remarked that the principle of the conservation of
energy is sufficient for deducing the laws of induction from the
electrodynamic laws of Ampère. But always on one condition, as Bertrand
has well shown; that we make besides a certain number of hypotheses.
The same principle again permits this deduction in the case of open
currents, although of course we can not submit the result to the test of
experiment, since we can not produce such currents.
If we try to apply this mode of analysis to Ampère's theory of open
currents, we reach results calculated to surprise us.
In the first place, induction can not be deduced from the variation of the
magnetic field by the formula well known to savants and practicians, and,
in fact, as we have said, properly speaking there is no longer a magnetic
field.
But, further, if a circuit C is subjected to the induction of a variable
voltaic system S, if this system S be displaced and deformed in any way
whatever, so that the intensity of the currents of this system varies
according to any law whatever, but that after these variations the system
finally returns to its initial situation, it seems natural to suppose that the
mean electromotive force induced in the circuit C is null.
This is true if the circuit C is closed and if the system S contains only
closed currents. This would no longer be true, if one accepts the theory of
Ampère, if there were open currents. So that not only induction will no
longer be the variation of the flow of magnetic force, in any of the usual
senses of the word, but it can not be represented by the variation of
anything whatever.

II. Theory of Helmholtz.—I have dwelt upon the consequences of
Ampère's theory, and of his method of explaining open currents.
It is difficult to overlook the paradoxical and artificial character of the
propositions to which we are thus led. One can not help thinking 'that can
not be so.'
We understand therefore why Helmholtz was led to seek something else.
Helmholtz rejects Ampère's fundamental hypothesis, to wit, that the
mutual action of two elements of current reduces to a force along their join.
He assumes that an element of current is not subjected to a single force, but
to a force and a couple. It is just this which gave rise to the celebrated
polemic between Bertrand and Helmholtz.
Helmholtz replaces Ampère's hypothesis by the following: two elements
always admit of an electrodynamic potential depending solely on their
position and orientation; and the work of the forces that they exercise, one
on the other, is equal to the variation of this potential. Thus Helmholtz can
no more do without hypothesis than Ampère; but at least he does not make
one without explicitly announcing it.
In the case of closed currents, which are alone accessible to experiment,
the two theories agree.
In all other cases they differ.
In the first place, contrary to what Ampère supposed, the force which
seems to act on the movable portion of a closed current is not the same as
would act upon this movable portion if it were isolated and constituted an
open current.
Let us return to the circuit C´, of which we spoke above, and which was
formed of a movable wire αβ sliding on a fixed wire. In the only experiment
that can be made, the movable portion αβ is not isolated, but is part of a
closed circuit. When it passes from AB to A´B´, the total electrodynamic
potential varies for two reasons:
1º It undergoes a first increase because the potential of A´B´ with respect
to the circuit C is not the same as that of AB;

2º It takes a second increment because it must be increased by the
potentials of the elements AA´, BB´ with respect to C.
It is this double increment which represents the work of the force to
which the portion AB seems subjected.
If, on the contrary, αβ were isolated, the potential would undergo only the
first increase, and this first increment alone would measure the work of the
force which acts on AB.
In the second place, there could be no continuous rotation without sliding
contact, and, in fact, that, as we have seen à propos of closed currents, is an
immediate consequence of the existence of an electrodynamic potential.
In Faraday's experiment, if the magnet is fixed and if the part of the
current exterior to the magnet runs along a movable wire, that movable part
may undergo a continuous rotation. But this does not mean to say that if the
contacts of the wire with the magnet were suppressed, and an open current
were to run along the wire, the wire would still take a movement of
continuous rotation.
I have just said in fact that an isolated element is not acted upon in the
same way as a movable element making part of a closed circuit.
Another difference: The action of a closed solenoid on a closed current is
null according to experiment and according to the two theories. Its action on
an open current would be null according to Ampère; it would not be null
according to Helmholtz. From this follows an important consequence. We
have given above three definitions of magnetic force. The third has no
meaning here since an element of current is no longer acted upon by a
single force. No more has the first any meaning. What, in fact, is a magnetic
pole? It is the extremity of an indefinite linear magnet. This magnet may be
replaced by an indefinite solenoid. For the definition of magnetic force to
have any meaning, it would be necessary that the action exercised by an
open current on an indefinite solenoid should depend only on the position
of the extremity of this solenoid, that is to say, that the action on a closed
solenoid should be null. Now we have just seen that such is not the case.
On the other hand, nothing prevents our adopting the second definition,
which is founded on the measurement of the director couple which tends to

orientate the magnetic needle.
But if it is adopted, neither the effects of induction nor the
electrodynamic effects will depend solely on the distribution of the lines of
force in this magnetic field.
III. Difficulties Raised by These Theories.—The theory of Helmholtz is
in advance of that of Ampère; it is necessary, however, that all the
difficulties should be smoothed away. In the one as in the other, the phrase
'magnetic field' has no meaning, or, if we give it one, by a more or less
artificial convention, the ordinary laws so familiar to all electricians no
longer apply; thus the electromotive force induced in a wire is no longer
measured by the number of lines of force met by this wire.
And our repugnance does not come alone from the difficulty of
renouncing inveterate habits of language and of thought. There is something
more. If we do not believe in action at a distance, electrodynamic
phenomena must be explained by a modification of the medium. It is
precisely this modification that we call 'magnetic field.' And then the
electrodynamic effects must depend only on this field.
All these difficulties arise from the hypothesis of open currents.
IV. Maxwell's Theory.—Such were the difficulties raised by the
dominant theories when Maxwell appeared, who with a stroke of the pen
made them all vanish. To his mind, in fact, all currents are closed currents.
Maxwell assumes that if in a dielectric the electric field happens to vary,
this dielectric becomes the seat of a particular phenomenon, acting on the
galvanometer like a current, and which he calls current of displacement.
If then two conductors bearing contrary charges are put in
communication by a wire, in this wire during the discharge there is an open
current of conduction; but there are produced at the same time in the
surrounding dielectric, currents of displacement which close this current of
conduction.
We know that Maxwell's theory leads to the explanation of optical
phenomena, which would be due to extremely rapid electrical oscillations.

At that epoch such a conception was only a bold hypothesis, which could
be supported by no experiment.
At the end of twenty years, Maxwell's ideas received the confirmation of
experiment. Hertz succeeded in producing systems of electric oscillations
which reproduce all the properties of light, and only differ from it by the
length of their wave; that is to say as violet differs from red. In some
measure he made the synthesis of light.
It might be said that Hertz has not demonstrated directly Maxwell's
fundamental idea, the action of the current of displacement on the
galvanometer. This is true in a sense. What he has shown in sum is that
electromagnetic induction is not propagated instantaneously as was
supposed; but with the speed of light.
But to suppose there is no current of displacement, and induction is
propagated with the speed of light; or to suppose that the currents of
displacement produce effects of induction, and that the induction is
propagated instantaneously, comes to the same thing.
This can not be seen at the first glance, but it is proved by an analysis of
which I must not think of giving even a summary here.
V. Rowland's Experiment.—But as I have said above, there are two kinds
of open conduction currents. There are first the currents of discharge of a
condenser or of any conductor whatever.
There are also the cases in which electric discharges describe a closed
contour, being displaced by conduction in one part of the circuit and by
convection in the other part.
For open currents of the first sort, the question might be considered as
solved; they were closed by the currents of displacement.
For open currents of the second sort, the solution appeared still more
simple. It seemed that if the current were closed, it could only be by the
current of convection itself. For that it sufficed to assume that a 'convection
current,' that is to say a charged conductor in motion, could act on the
galvanometer.

But experimental confirmation was lacking. It appeared difficult in fact
to obtain a sufficient intensity even by augmenting as much as possible the
charge and the velocity of the conductors. It was Rowland, an extremely
skillful experimenter, who first triumphed over these difficulties. A disc
received a strong electrostatic charge and a very great speed of rotation. An
astatic magnetic system placed beside the disc underwent deviations.
The experiment was made twice by Rowland, once in Berlin, once in
Baltimore. It was afterwards repeated by Himstedt. These physicists even
announced that they had succeeded in making quantitative measurements.
In fact, for twenty years Rowland's law was admitted without objection
by all physicists. Besides everything seemed to confirm it. The spark
certainly does produce a magnetic effect. Now does it not seem probable
that the discharge by spark is due to particles taken from one of the
electrodes and transferred to the other electrode with their charge? Is not the
very spectrum of the spark, in which we recognize the lines of the metal of
the electrode, a proof of it? The spark would then be a veritable current of
convection.
On the other hand, it is also admitted that in an electrolyte the electricity
is carried by the ions in motion. The current in an electrolyte would
therefore be also a current of convection; now, it acts on the magnetic
needle.
The same for cathode rays. Crookes attributed these rays to a very subtile
matter charged with electricity and moving with a very great velocity. He
regarded them, in other words, as currents of convection. Now these
cathode rays are deviated by the magnet. In virtue of the principle of action
and reaction, they should in turn deviate the magnetic needle. It is true that
Hertz believed he had demonstrated that the cathode rays do not carry
electricity, and that they do not act on the magnetic needle. But Hertz was
mistaken. First of all, Perrin succeeded in collecting the electricity carried
by these rays, electricity of which Hertz denied the existence; the German
scientist appears to have been deceived by effects due to the action of X-
rays, which were not yet discovered. Afterwards, and quite recently, the
action of the cathode rays on the magnetic needle has been put in evidence.

Thus all these phenomena regarded as currents of convection, sparks,
electrolytic currents, cathode rays, act in the same manner on the
galvanometer and in conformity with Rowland's law.
VI. Theory of Lorentz.—We soon went farther. According to the theory
of Lorentz, currents of conduction themselves would be true currents of
convection. Electricity would remain inseparably connected with certain
material particles called electrons. The circulation of these electrons
through bodies would produce voltaic currents. And what would distinguish
conductors from insulators would be that the one could be traversed by
these electrons while the others would arrest their movements.
The theory of Lorentz is very attractive. It gives a very simple
explanation of certain phenomena which the earlier theories, even
Maxwell's in its primitive form, could not explain in a satisfactory way; for
example, the aberration of light, the partial carrying away of luminous
waves, magnetic polarization and the Zeeman effect.
Some objections still remained. The phenomena of an electric system
seemed to depend on the absolute velocity of translation of the center of
gravity of this system, which is contrary to the idea we have of the relativity
of space. Supported by M. Crémieu, M. Lippmann has presented this
objection in a striking form. Imagine two charged conductors with the same
velocity of translation; they are relatively at rest. However, each of them
being equivalent to a current of convection, they ought to attract one
another, and by measuring this attraction we could measure their absolute
velocity.
"No!" replied the partisans of Lorentz. "What we could measure in that
way is not their absolute velocity, but their relative velocity with respect to
the ether, so that the principle of relativity is safe."
Whatever there may be in these latter objections, the edifice of
electrodynamics, at least in its broad lines, seemed definitively constructed.
Everything was presented under the most satisfactory aspect. The theories
of Ampère and of Helmholtz, made for open currents which no longer
existed, seemed to have no longer anything but a purely historic interest,
and the inextricable complications to which these theories led were almost
forgotten.

This quiescence has been recently disturbed by the experiments of M.
Crémieu, which for a moment seemed to contradict the result previously
obtained by Rowland.
But fresh researches have not confirmed them, and the theory of Lorentz
has victoriously stood the test.
The history of these variations will be none the less instructive; it will
teach us to what pitfalls the scientist is exposed, and how he may hope to
escape them.

THE VALUE OF SCIENCE

TRANSLATOR'S INTRODUCTION
1. Does the Scientist create Science?—Professor Rados of Budapest in
his report to the Hungarian Academy of Science on the award to Poincaré of
the Bolyai prize of ten thousand crowns, speaking of him as unquestionably
the most powerful investigator in the domain of mathematics and
mathematical physics, characterized him as the intuitive genius drawing the
inspiration for his wide-reaching researches from the exhaustless fountain
of geometric and physical intuition, yet working this inspiration out in
detail with marvelous logical keenness. With his brilliant creative genius
was combined the capacity for sharp and successful generalization, pushing
far out the boundaries of thought in the most widely different domains, so
that his works must be ranked with the greatest mathematical achievements
of all time. "Finally," says Rados, "permit me to make especial mention of

his intensely interesting book, 'The Value of Science,' in which he in a way
has laid down the scientist's creed." Now what is this creed?
Sense may act as stimulus, as suggestive, yet not to awaken a dormant
depiction, or to educe the conception of an archetypal form, but rather to
strike the hour for creation, to summon to work a sculptor capable of
smoothing a Venus of Milo out of the formless clay. Knowledge is not a gift
of bare experience, nor even made solely out of experience. The creative
activity of mind is in mathematics particularly clear. The axioms of
geometry are conventions, disguised definitions or unprovable hypotheses
precreated by auto-active animal and human minds. Bertrand Russell says
of projective geometry: "It takes nothing from experience, and has, like
arithmetic, a creature of the pure intellect for its object. It deals with an
object whose properties are logically deduced from its definition, not
empirically discovered from data." Then does the scientist create science?
This is a question Poincaré here dissects with a master hand.
The physiologic-psychologic investigation of the space problem must
give the meaning of the words geometric fact, geometric reality. Poincaré
here subjects to the most successful analysis ever made the
tridimensionality of our space.
2. The Mind Dispelling Optical Illusions.—Actual perception of spatial
properties is accompanied by movements corresponding to its character. In
the case of optical illusions, with the so-called false perceptions eye-
movements are closely related. But though the perceived object and its
environment remain constant, the sufficiently powerful mind can, as we say,
dispel these illusions, the perception itself being creatively changed. Photo-
graphs taken at intervals during the presence of these optical illusions,
during the change, perhaps gradual and unconscious, in the perception, and
after these illusions have, as the phrase is, finally disappeared, show quite
clearly that changes in eye-movements corresponding to those internally
created in perception itself successively occur. What is called accuracy of
movement is created by what is called correctness of perception. The higher
creation in the perception is the determining cause of an improvement, a
precision in the motion. Thus we see correct perception in the individual
helping to make that cerebral organization and accurate motor adjustment
on which its possibility and permanence seem in so far to depend. So-called

correct perception is connected with a long-continued process of perceptual
education motived and initiated from within. How this may take place is
here illustrated at length by our author.
3. Euclid not Necessary.—Geometry is a construction of the intellect, in
application not certain but convenient. As Schiller says, when we see these
facts as clearly as the development of metageometry has compelled us to
see them, we must surely confess that the Kantian account of space is
hopelessly and demonstrably antiquated. As Royce says in 'Kant's Doctrine
of the Basis of Mathematics,' "That very use of intuition which Kant
regarded as geometrically ideal, the modern geometer regards as
scientifically defective, because surreptitious. No mathematical exactness
without explicit proof from assumed principles—such is the motto of the
modern geometer. But suppose the reasoning of Euclid purified of this
comparatively surreptitious appeal to intuition. Suppose that the principles
of geometry are made quite explicit at the outset of the treatise, as Pieri and
Hilbert or Professor Halsted or Dr. Veblen makes his principles explicit in
his recent treatment of geometry. Then, indeed, geometry becomes for the
modern mathematician a purely rational science. But very few students of
the logic of mathematics at the present time can see any warrant in the
analysis of geometrical truth for regarding just the Euclidean system of
principles as possessing any discoverable necessity." Yet the environmental
and perhaps hereditary premiums on Euclid still make even the scientist
think Euclid most convenient.
4. Without Hypotheses, no Science.—Nobody ever observed an
equidistantial, but also nobody ever observed a straight line. Emerson's
Uriel
"Gave his sentiment divine
Against the being of a line.
Line in Nature is not found."
Clearly not, being an eject from man's mind. What is called 'a knowledge of
facts' is usually merely a subjective realization that the old hypotheses are
still sufficiently elastic to serve in some domain; that is, with a sufficiency
of conscious or unconscious omissions and doctorings and fudgings more
or less wilful. In the present book we see the very foundation rocks of

science, the conservation of energy and the indestructibility of matter,
beating against the bars of their cages, seemingly anxious to take wing
away into the empyrean, to chase the once divine parallel postulate broken
loose from Euclid and Kant.
5. What Outcome?—What now is the definite, the permanent outcome?
What new islets raise their fronded palms in air within thought's musical
domain? Over what age-gray barriers rise the fragrant floods of this new
spring-tide, redolent of the wolf-haunted forest of Transylvania, of far
Erdély's plunging river, Maros the bitter, or broad mother Volga at Kazan?
What victory heralded the great rocket for which young Lobachevski, the
widow's son, was cast into prison? What severing of age-old mental fetters
symbolized young Bolyai's cutting-off with his Damascus blade the spikes
driven into his door-post, and strewing over the sod the thirteen Austrian
cavalry officers? This book by the greatest mathematician of our time gives
weightiest and most charming answer.
George Bruce Halsted.

INTRODUCTION
The search for truth should be the goal of our activities; it is the sole end
worthy of them. Doubtless we should first bend our efforts to assuage
human suffering, but why? Not to suffer is a negative ideal more surely
attained by the annihilation of the world. If we wish more and more to free
man from material cares, it is that he may be able to employ the liberty
obtained in the study and contemplation of truth.
But sometimes truth frightens us. And in fact we know that it is
sometimes deceptive, that it is a phantom never showing itself for a moment
except to ceaselessly flee, that it must be pursued further and ever further
without ever being attained. Yet to work one must stop, as some Greek,
Aristotle or another, has said. We also know how cruel the truth often is,
and we wonder whether illusion is not more consoling, yea, even more
bracing, for illusion it is which gives confidence. When it shall have
vanished, will hope remain and shall we have the courage to achieve? Thus

would not the horse harnessed to his treadmill refuse to go, were his eyes
not bandaged? And then to seek truth it is necessary to be independent,
wholly independent. If, on the contrary, we wish to act, to be strong, we
should be united. This is why many of us fear truth; we consider it a cause
of weakness. Yet truth should not be feared, for it alone is beautiful.
When I speak here of truth, assuredly I refer first to scientific truth; but I
also mean moral truth, of which what we call justice is only one aspect. It
may seem that I am misusing words, that I combine thus under the same
name two things having nothing in common; that scientific truth, which is
demonstrated, can in no way be likened to moral truth, which is felt. And
yet I can not separate them, and whosoever loves the one can not help
loving the other. To find the one, as well as to find the other, it is necessary
to free the soul completely from prejudice and from passion; it is necessary
to attain absolute sincerity. These two sorts of truth when discovered give
the same joy; each when perceived beams with the same splendor, so that
we must see it or close our eyes. Lastly, both attract us and flee from us;
they are never fixed: when we think to have reached them, we find that we
have still to advance, and he who pursues them is condemned never to
know repose. It must be added that those who fear the one will also fear the
other; for they are the ones who in everything are concerned above all with
consequences. In a word, I liken the two truths, because the same reasons
make us love them and because the same reasons make us fear them.
If we ought not to fear moral truth, still less should we dread scientific
truth. In the first place it can not conflict with ethics. Ethics and science
have their own domains, which touch but do not interpenetrate. The one
shows us to what goal we should aspire, the other, given the goal, teaches
us how to attain it. So they can never conflict since they can never meet.
There can no more be immoral science than there can be scientific morals.
But if science is feared, it is above all because it can not give us
happiness. Of course it can not. We may even ask whether the beast does
not suffer less than man. But can we regret that earthly paradise where man
brute-like was really immortal in knowing not that he must die? When we
have tasted the apple, no suffering can make us forget its savor. We always
come back to it. Could it be otherwise? As well ask if one who has seen and

is blind will not long for the light. Man, then, can not be happy through
science, but to-day he can much less be happy without it.
But if truth be the sole aim worth pursuing, may we hope to attain it? It
may well be doubted. Readers of my little book 'Science and Hypothesis'
already know what I think about the question. The truth we are permitted to
glimpse is not altogether what most men call by that name. Does this mean
that our most legitimate, most imperative aspiration is at the same time the
most vain? Or can we, despite all, approach truth on some side? This it is
which must be investigated.
In the first place, what instrument have we at our disposal for this
conquest? Is not human intelligence, more specifically the intelligence of
the scientist, susceptible of infinite variation? Volumes could be written
without exhausting this subject; I, in a few brief pages, have only touched it
lightly. That the geometer's mind is not like the physicist's or the
naturalist's, all the world would agree; but mathematicians themselves do
not resemble each other; some recognize only implacable logic, others
appeal to intuition and see in it the only source of discovery. And this would
be a reason for distrust. To minds so unlike can the mathematical theorems
themselves appear in the same light? Truth which is not the same for all, is
it truth? But looking at things more closely, we see how these very different
workers collaborate in a common task which could not be achieved without
their cooperation. And that already reassures us.
Next must be examined the frames in which nature seems enclosed and
which are called time and space. In 'Science and Hypothesis' I have already
shown how relative their value is; it is not nature which imposes them upon
us, it is we who impose them upon nature because we find them convenient.
But I have spoken of scarcely more than space, and particularly quantitative
space, so to say, that is of the mathematical relations whose aggregate
constitutes geometry. I should have shown that it is the same with time as
with space and still the same with 'qualitative space'; in particular, I should
have investigated why we attribute three dimensions to space. I may be
pardoned then for taking up again these important questions.
Is mathematical analysis, then, whose principal object is the study of
these empty frames, only a vain play of the mind? It can give to the

physicist only a convenient language; is this not a mediocre service, which,
strictly speaking, could be done without; and even is it not to be feared that
this artificial language may be a veil interposed between reality and the eye
of the physicist? Far from it; without this language most of the intimate
analogies of things would have remained forever unknown to us; and we
should forever have been ignorant of the internal harmony of the world,
which is, we shall see, the only true objective reality.
The best expression of this harmony is law. Law is one of the most recent
conquests of the human mind; there still are people who live in the presence
of a perpetual miracle and are not astonished at it. On the contrary, we it is
who should be astonished at nature's regularity. Men demand of their gods
to prove their existence by miracles; but the eternal marvel is that there are
not miracles without cease. The world is divine because it is a harmony. If it
were ruled by caprice, what could prove to us it was not ruled by chance?
This conquest of law we owe to astronomy, and just this makes the
grandeur of the science rather than the material grandeur of the objects it
considers. It was altogether natural, then, that celestial mechanics should be
the first model of mathematical physics; but since then this science has
developed; it is still developing, even rapidly developing. And it is already
necessary to modify in certain points the scheme from which I drew two
chapters of 'Science and Hypothesis.' In an address at the St. Louis
exposition, I sought to survey the road traveled; the result of this
investigation the reader shall see farther on.
The progress of science has seemed to imperil the best established
principles, those even which were regarded as fundamental. Yet nothing
shows they will not be saved; and if this comes about only imperfectly, they
will still subsist even though they are modified. The advance of science is
not comparable to the changes of a city, where old edifices are pitilessly
torn down to give place to new, but to the continuous evolution of zoologic
types which develop ceaselessly and end by becoming unrecognizable to
the common sight, but where an expert eye finds always traces of the prior
work of the centuries past. One must not think then that the old-fashioned
theories have been sterile and vain.

Were we to stop there, we should find in these pages some reasons for
confidence in the value of science, but many more for distrusting it; an
impression of doubt would remain; it is needful now to set things to rights.
Some people have exaggerated the rôle of convention in science; they
have even gone so far as to say that law, that scientific fact itself, was
created by the scientist. This is going much too far in the direction of
nominalism. No, scientific laws are not artificial creations; we have no
reason to regard them as accidental, though it be impossible to prove they
are not.
Does the harmony the human intelligence thinks it discovers in nature
exist outside of this intelligence? No, beyond doubt a reality completely
independent of the mind which conceives it, sees or feels it, is an
impossibility. A world as exterior as that, even if it existed, would for us be
forever inaccessible. But what we call objective reality is, in the last
analysis, what is common to many thinking beings, and could be common
to all; this common part, we shall see, can only be the harmony expressed
by mathematical laws. It is this harmony then which is the sole objective
reality, the only truth we can attain; and when I add that the universal
harmony of the world is the source of all beauty, it will be understood what
price we should attach to the slow and difficult progress which little by little
enables us to know it better.

PART I

THE MATHEMATICAL SCIENCES

CHAPTER I

Intuition and Logic in Mathematics

I
It is impossible to study the works of the great mathematicians, or even
those of the lesser, without noticing and distinguishing two opposite
tendencies, or rather two entirely different kinds of minds. The one sort are
above all preoccupied with logic; to read their works, one is tempted to
believe they have advanced only step by step, after the manner of a Vauban
who pushes on his trenches against the place besieged, leaving nothing to
chance. The other sort are guided by intuition and at the first stroke make
quick but sometimes precarious conquests, like bold cavalrymen of the
advance guard.
The method is not imposed by the matter treated. Though one often says
of the first that they are analysts and calls the others geometers, that does
not prevent the one sort from remaining analysts even when they work at
geometry, while the others are still geometers even when they occupy
themselves with pure analysis. It is the very nature of their mind which
makes them logicians or intuitionalists, and they can not lay it aside when
they approach a new subject.
Nor is it education which has developed in them one of the two
tendencies and stifled the other. The mathematician is born, not made, and it
seems he is born a geometer or an analyst. I should like to cite examples

and there are surely plenty; but to accentuate the contrast I shall begin with
an extreme example, taking the liberty of seeking it in two living
mathematicians.
M. Méray wants to prove that a binomial equation always has a root, or,
in ordinary words, that an angle may always be subdivided. If there is any
truth that we think we know by direct intuition, it is this. Who could doubt
that an angle may always be divided into any number of equal parts? M.
Méray does not look at it that way; in his eyes this proposition is not at all
evident and to prove it he needs several pages.
On the other hand, look at Professor Klein: he is studying one of the most
abstract questions of the theory of functions: to determine whether on a
given Riemann surface there always exists a function admitting of given
singularities. What does the celebrated German geometer do? He replaces
his Riemann surface by a metallic surface whose electric conductivity
varies according to certain laws. He connects two of its points with the two
poles of a battery. The current, says he, must pass, and the distribution of
this current on the surface will define a function whose singularities will be
precisely those called for by the enunciation.
Doubtless Professor Klein well knows he has given here only a sketch;
nevertheless he has not hesitated to publish it; and he would probably
believe he finds in it, if not a rigorous demonstration, at least a kind of
moral certainty. A logician would have rejected with horror such a
conception, or rather he would not have had to reject it, because in his mind
it would never have originated.
Again, permit me to compare two men, the honor of French science, who
have recently been taken from us, but who both entered long ago into
immortality. I speak of M. Bertrand and M. Hermite. They were scholars of
the same school at the same time; they had the same education, were under
the same influences; and yet what a difference! Not only does it blaze forth
in their writings; it is in their teaching, in their way of speaking, in their
very look. In the memory of all their pupils these two faces are stamped in
deathless lines; for all who have had the pleasure of following their
teaching, this remembrance is still fresh; it is easy for us to evoke it.

While speaking, M. Bertrand is always in motion; now he seems in
combat with some outside enemy, now he outlines with a gesture of the
hand the figures he studies. Plainly he sees and he is eager to paint, this is
why he calls gesture to his aid. With M. Hermite, it is just the opposite; his
eyes seem to shun contact with the world; it is not without, it is within he
seeks the vision of truth.
Among the German geometers of this century, two names above all are
illustrious, those of the two scientists who founded the general theory of
functions, Weierstrass and Riemann. Weierstrass leads everything back to
the consideration of series and their analytic transformations; to express it
better, he reduces analysis to a sort of prolongation of arithmetic; you may
turn through all his books without finding a figure. Riemann, on the
contrary, at once calls geometry to his aid; each of his conceptions is an
image that no one can forget, once he has caught its meaning.
More recently, Lie was an intuitionalist; this might have been doubted in
reading his books, no one could doubt it after talking with him; you saw at
once that he thought in pictures. Madame Kovalevski was a logician.
Among our students we notice the same differences; some prefer to treat
their problems 'by analysis,' others 'by geometry.' The first are incapable of
'seeing in space,' the others are quickly tired of long calculations and
become perplexed.
The two sorts of minds are equally necessary for the progress of science;
both the logicians and the intuitionalists have achieved great things that
others could not have done. Who would venture to say whether he preferred
that Weierstrass had never written or that there had never been a Riemann?
Analysis and synthesis have then both their legitimate rôles. But it is
interesting to study more closely in the history of science the part which
belongs to each.

II
Strange! If we read over the works of the ancients we are tempted to
class them all among the intuitionalists. And yet nature is always the same;
it is hardly probable that it has begun in this century to create minds
devoted to logic. If we could put ourselves into the flow of ideas which

reigned in their time, we should recognize that many of the old geometers
were in tendency analysts. Euclid, for example, erected a scientific structure
wherein his contemporaries could find no fault. In this vast construction, of
which each piece however is due to intuition, we may still to-day, without
much effort, recognize the work of a logician.
It is not minds that have changed, it is ideas; the intuitional minds have
remained the same; but their readers have required of them greater
concessions.
What is the cause of this evolution? It is not hard to find. Intuition can
not give us rigor, nor even certainty; this has been recognized more and
more. Let us cite some examples. We know there exist continuous functions
lacking derivatives. Nothing is more shocking to intuition than this
proposition which is imposed upon us by logic. Our fathers would not have
failed to say: "It is evident that every continuous function has a derivative,
since every curve has a tangent."
How can intuition deceive us on this point? It is because when we seek to
imagine a curve we can not represent it to ourselves without width; just so,
when we represent to ourselves a straight line, we see it under the form of a
rectilinear band of a certain breadth. We well know these lines have no
width; we try to imagine them narrower and narrower and thus to approach
the limit; so we do in a certain measure, but we shall never attain this limit.
And then it is clear we can always picture these two narrow bands, one
straight, one curved, in a position such that they encroach slightly one upon
the other without crossing. We shall thus be led, unless warned by a
rigorous analysis, to conclude that a curve always has a tangent.
I shall take as second example Dirichlet's principle on which rest so
many theorems of mathematical physics; to-day we establish it by
reasoning very rigorous but very long; heretofore, on the contrary, we were
content with a very summary proof. A certain integral depending on an
arbitrary function can never vanish. Hence it is concluded that it must have
a minimum. The flaw in this reasoning strikes us immediately, since we use
the abstract term function and are familiar with all the singularities
functions can present when the word is understood in the most general
sense.

But it would not be the same had we used concrete images, had we, for
example, considered this function as an electric potential; it would have
been thought legitimate to affirm that electrostatic equilibrium can be
attained. Yet perhaps a physical comparison would have awakened some
vague distrust. But if care had been taken to translate the reasoning into the
language of geometry, intermediate between that of analysis and that of
physics, doubtless this distrust would not have been produced, and perhaps
one might thus, even to-day, still deceive many readers not forewarned.
Intuition, therefore, does not give us certainty. This is why the evolution
had to happen; let us now see how it happened.
It was not slow in being noticed that rigor could not be introduced in the
reasoning unless first made to enter into the definitions. For the most part
the objects treated of by mathematicians were long ill defined; they were
supposed to be known because represented by means of the senses or the
imagination; but one had only a crude image of them and not a precise idea
on which reasoning could take hold. It was there first that the logicians had
to direct their efforts.
So, in the case of incommensurable numbers. The vague idea of
continuity, which we owe to intuition, resolved itself into a complicated
system of inequalities referring to whole numbers.
By that means the difficulties arising from passing to the limit, or from
the consideration of infinitesimals, are finally removed. To-day in analysis
only whole numbers are left or systems, finite or infinite, of whole numbers
bound together by a net of equality or inequality relations. Mathematics, as
they say, is arithmetized.

III
A first question presents itself. Is this evolution ended? Have we finally
attained absolute rigor? At each stage of the evolution our fathers also
thought they had reached it. If they deceived themselves, do we not
likewise cheat ourselves?
We believe that in our reasonings we no longer appeal to intuition; the
philosophers will tell us this is an illusion. Pure logic could never lead us to

anything but tautologies; it could create nothing new; not from it alone can
any science issue. In one sense these philosophers are right; to make
arithmetic, as to make geometry, or to make any science, something else
than pure logic is necessary. To designate this something else we have no
word other than intuition. But how many different ideas are hidden under
this same word?
Compare these four axioms: (1) Two quantities equal to a third are equal
to one another; (2) if a theorem is true of the number 1 and if we prove that
it is true of n + 1 if true for n, then will it be true of all whole numbers; (3)
if on a straight the point C is between A and B and the point D between A
and C, then the point D will be between A and B; (4) through a given point
there is not more than one parallel to a given straight.
All four are attributed to intuition, and yet the first is the enunciation of
one of the rules of formal logic; the second is a real synthetic a priori
judgment, it is the foundation of rigorous mathematical induction; the third
is an appeal to the imagination; the fourth is a disguised definition.
Intuition is not necessarily founded on the evidence of the senses; the
senses would soon become powerless; for example, we can not represent to
ourselves a chiliagon, and yet we reason by intuition on polygons in
general, which include the chiliagon as a particular case.
You know what Poncelet understood by the principle of continuity. What
is true of a real quantity, said Poncelet, should be true of an imaginary
quantity; what is true of the hyperbola whose asymptotes are real, should
then be true of the ellipse whose asymptotes are imaginary. Poncelet was
one of the most intuitive minds of this century; he was passionately, almost
ostentatiously, so; he regarded the principle of continuity as one of his
boldest conceptions, and yet this principle did not rest on the evidence of
the senses. To assimilate the hyperbola to the ellipse was rather to
contradict this evidence. It was only a sort of precocious and instinctive
generalization which, moreover, I have no desire to defend.
We have then many kinds of intuition; first, the appeal to the senses and
the imagination; next, generalization by induction, copied, so to speak, from
the procedures of the experimental sciences; finally, we have the intuition of
pure number, whence arose the second of the axioms just enunciated, which

is able to create the real mathematical reasoning. I have shown above by
examples that the first two can not give us certainty; but who will seriously
doubt the third, who will doubt arithmetic?
Now in the analysis of to-day, when one cares to take the trouble to be
rigorous, there can be nothing but syllogisms or appeals to this intuition of
pure number, the only intuition which can not deceive us. It may be said
that to-day absolute rigor is attained.

IV
The philosophers make still another objection: "What you gain in rigor,"
they say, "you lose in objectivity. You can rise toward your logical ideal
only by cutting the bonds which attach you to reality. Your science is
infallible, but it can only remain so by imprisoning itself in an ivory tower
and renouncing all relation with the external world. From this seclusion it
must go out when it would attempt the slightest application."
For example, I seek to show that some property pertains to some object
whose concept seems to me at first indefinable, because it is intuitive. At
first I fail or must content myself with approximate proofs; finally I decide
to give to my object a precise definition, and this enables me to establish
this property in an irreproachable manner.
"And then," say the philosophers, "it still remains to show that the object
which corresponds to this definition is indeed the same made known to you
by intuition; or else that some real and concrete object whose conformity
with your intuitive idea you believe you immediately recognize corresponds
to your new definition. Only then could you affirm that it has the property
in question. You have only displaced the difficulty."
That is not exactly so; the difficulty has not been displaced, it has been
divided. The proposition to be established was in reality composed of two
different truths, at first not distinguished. The first was a mathematical
truth, and it is now rigorously established. The second was an experimental
verity. Experience alone can teach us that some real and concrete object
corresponds or does not correspond to some abstract definition. This second
verity is not mathematically demonstrated, but neither can it be, no more

than can the empirical laws of the physical and natural sciences. It would be
unreasonable to ask more.
Well, is it not a great advance to have distinguished what long was
wrongly confused? Does this mean that nothing is left of this objection of
the philosophers? That I do not intend to say; in becoming rigorous,
mathematical science takes a character so artificial as to strike every one; it
forgets its historical origins; we see how the questions can be answered, we
no longer see how and why they are put.
This shows us that logic is not enough; that the science of demonstration
is not all science and that intuition must retain its rôle as complement, I was
about to say as counterpoise or as antidote of logic.
I have already had occasion to insist on the place intuition should hold in
the teaching of the mathematical sciences. Without it young minds could
not make a beginning in the understanding of mathematics; they could not
learn to love it and would see in it only a vain logomachy; above all,
without intuition they would never become capable of applying
mathematics. But now I wish before all to speak of the rôle of intuition in
science itself. If it is useful to the student it is still more so to the creative
scientist.

V
We seek reality, but what is reality? The physiologists tell us that
organisms are formed of cells; the chemists add that cells themselves are
formed of atoms. Does this mean that these atoms or these cells constitute
reality, or rather the sole reality? The way in which these cells are arranged
and from which results the unity of the individual, is not it also a reality
much more interesting than that of the isolated elements, and should a
naturalist who had never studied the elephant except by means of the
microscope think himself sufficiently acquainted with that animal?
Well, there is something analogous to this in mathematics. The logician
cuts up, so to speak, each demonstration into a very great number of
elementary operations; when we have examined these operations one after
the other and ascertained that each is correct, are we to think we have
grasped the real meaning of the demonstration? Shall we have understood it

even when, by an effort of memory, we have become able to repeat this
proof by reproducing all these elementary operations in just the order in
which the inventor had arranged them? Evidently not; we shall not yet
possess the entire reality; that I know not what, which makes the unity of
the demonstration, will completely elude us.
Pure analysis puts at our disposal a multitude of procedures whose
infallibility it guarantees; it opens to us a thousand different ways on which
we can embark in all confidence; we are assured of meeting there no
obstacles; but of all these ways, which will lead us most promptly to our
goal? Who shall tell us which to choose? We need a faculty which makes us
see the end from afar, and intuition is this faculty. It is necessary to the
explorer for choosing his route; it is not less so to the one following his trail
who wants to know why he chose it.
If you are present at a game of chess, it will not suffice, for the
understanding of the game, to know the rules for moving the pieces. That
will only enable you to recognize that each move has been made
conformably to these rules, and this knowledge will truly have very little
value. Yet this is what the reader of a book on mathematics would do if he
were a logician only. To understand the game is wholly another matter; it is
to know why the player moves this piece rather than that other which he
could have moved without breaking the rules of the game. It is to perceive
the inward reason which makes of this series of successive moves a sort of
organized whole. This faculty is still more necessary for the player himself,
that is, for the inventor.
Let us drop this comparison and return to mathematics. For example, see
what has happened to the idea of continuous function. At the outset this was
only a sensible image, for example, that of a continuous mark traced by the
chalk on a blackboard. Then it became little by little more refined; ere long
it was used to construct a complicated system of inequalities, which
reproduced, so to speak, all the lines of the original image; this construction
finished, the centering of the arch, so to say, was removed, that crude
representation which had temporarily served as support and which was
afterward useless was rejected; there remained only the construction itself,
irreproachable in the eyes of the logician. And yet if the primitive image

had totally disappeared from our recollection, how could we divine by what
caprice all these inequalities were erected in this fashion one upon another?
Perhaps you think I use too many comparisons; yet pardon still another.
You have doubtless seen those delicate assemblages of silicious needles
which form the skeleton of certain sponges. When the organic matter has
disappeared, there remains only a frail and elegant lace-work. True, nothing
is there except silica, but what is interesting is the form this silica has taken,
and we could not understand it if we did not know the living sponge which
has given it precisely this form. Thus it is that the old intuitive notions of
our fathers, even when we have abandoned them, still imprint their form
upon the logical constructions we have put in their place.
This view of the aggregate is necessary for the inventor; it is equally
necessary for whoever wishes really to comprehend the inventor. Can logic
give it to us? No; the name mathematicians give it would suffice to prove
this. In mathematics logic is called analysis and analysis means division,
dissection. It can have, therefore, no tool other than the scalpel and the
microscope.
Thus logic and intuition have each their necessary rôle. Each is
indispensable. Logic, which alone can give certainty, is the instrument of
demonstration; intuition is the instrument of invention.

VI
But at the moment of formulating this conclusion I am seized with
scruples. At the outset I distinguished two kinds of mathematical minds, the
one sort logicians and analysts, the others intuitionalists and geometers.
Well, the analysts also have been inventors. The names I have just cited
make my insistence on this unnecessary.
Here is a contradiction, at least apparently, which needs explanation. And
first, do you think these logicians have always proceeded from the general
to the particular, as the rules of formal logic would seem to require of them?
Not thus could they have extended the boundaries of science; scientific
conquest is to be made only by generalization.

In one of the chapters of 'Science and Hypothesis,' I have had occasion to
study the nature of mathematical reasoning, and I have shown how this
reasoning, without ceasing to be absolutely rigorous, could lift us from the
particular to the general by a procedure I have called mathematical
induction. It is by this procedure that the analysts have made science
progress, and if we examine the detail itself of their demonstrations, we
shall find it there at each instant beside the classic syllogism of Aristotle.
We, therefore, see already that the analysts are not simply makers of
syllogisms after the fashion of the scholastics.
Besides, do you think they have always marched step by step with no
vision of the goal they wished to attain? They must have divined the way
leading thither, and for that they needed a guide. This guide is, first,
analogy. For example, one of the methods of demonstration dear to analysts
is that founded on the employment of dominant functions. We know it has
already served to solve a multitude of problems; in what consists then the
rôle of the inventor who wishes to apply it to a new problem? At the outset
he must recognize the analogy of this question with those which have
already been solved by this method; then he must perceive in what way this
new question differs from the others, and thence deduce the modifications
necessary to apply to the method.
But how does one perceive these analogies and these differences? In the
example just cited they are almost always evident, but I could have found
others where they would have been much more deeply hidden; often a very
uncommon penetration is necessary for their discovery. The analysts, not to
let these hidden analogies escape them, that is, in order to be inventors,
must, without the aid of the senses and imagination, have a direct sense of
what constitutes the unity of a piece of reasoning, of what makes, so to
speak, its soul and inmost life.
When one talked with M. Hermite, he never evoked a sensuous image,
and yet you soon perceived that the most abstract entities were for him like
living beings. He did not see them, but he perceived that they are not an
artificial assemblage and that they have some principle of internal unity.
But, one will say, that still is intuition. Shall we conclude that the
distinction made at the outset was only apparent, that there is only one sort

of mind and that all the mathematicians are intuitionalists, at least those
who are capable of inventing?
No, our distinction corresponds to something real. I have said above that
there are many kinds of intuition. I have said how much the intuition of
pure number, whence comes rigorous mathematical induction, differs from
sensible intuition to which the imagination, properly so called, is the
principal contributor.
Is the abyss which separates them less profound than it at first appeared?
Could we recognize with a little attention that this pure intuition itself could
not do without the aid of the senses? This is the affair of the psychologist
and the metaphysician and I shall not discuss the question. But the thing's
being doubtful is enough to justify me in recognizing and affirming an
essential difference between the two kinds of intuition; they have not the
same object and seem to call into play two different faculties of our soul;
one would think of two search-lights directed upon two worlds strangers to
one another.
It is the intuition of pure number, that of pure logical forms, which
illumines and directs those we have called analysts. This it is which enables
them not alone to demonstrate, but also to invent. By it they perceive at a
glance the general plan of a logical edifice, and that too without the senses
appearing to intervene. In rejecting the aid of the imagination, which, as we
have seen, is not always infallible, they can advance without fear of
deceiving themselves. Happy, therefore, are those who can do without this
aid! We must admire them; but how rare they are!
Among the analysts there will then be inventors, but they will be few.
The majority of us, if we wished to see afar by pure intuition alone, would
soon feel ourselves seized with vertigo. Our weakness has need of a staff
more solid, and, despite the exceptions of which we have just spoken, it is
none the less true that sensible intuition is in mathematics the most usual
instrument of invention.
Apropos of these reflections, a question comes up that I have not the time
either to solve or even to enunciate with the developments it would admit
of. Is there room for a new distinction, for distinguishing among the

analysts those who above all use pure intuition and those who are first of all
preoccupied with formal logic?
M. Hermite, for example, whom I have just cited, can not be classed
among the geometers who make use of the sensible intuition; but neither is
he a logician, properly so called. He does not conceal his aversion to purely
deductive procedures which start from the general and end in the particular.

CHAPTER II

The Measure of Time

I
So long as we do not go outside the domain of consciousness, the notion
of time is relatively clear. Not only do we distinguish without difficulty
present sensation from the remembrance of past sensations or the
anticipation of future sensations, but we know perfectly well what we mean
when we say that of two conscious phenomena which we remember, one
was anterior to the other; or that, of two foreseen conscious phenomena,
one will be anterior to the other.
When we say that two conscious facts are simultaneous, we mean that
they profoundly interpenetrate, so that analysis can not separate them
without mutilating them.
The order in which we arrange conscious phenomena does not admit of
any arbitrariness. It is imposed upon us and of it we can change nothing.
I have only a single observation to add. For an aggregate of sensations to
have become a remembrance capable of classification in time, it must have
ceased to be actual, we must have lost the sense of its infinite complexity,
otherwise it would have remained present. It must, so to speak, have
crystallized around a center of associations of ideas which will be a sort of
label. It is only when they thus have lost all life that we can classify our
memories in time as a botanist arranges dried flowers in his herbarium.

But these labels can only be finite in number. On that score, psychologic
time should be discontinuous. Whence comes the feeling that between any
two instants there are others? We arrange our recollections in time, but we
know that there remain empty compartments. How could that be, if time
were not a form pre-existent in our minds? How could we know there were
empty compartments, if these compartments were revealed to us only by
their content?

II
But that is not all; into this form we wish to put not only the phenomena
of our own consciousness, but those of which other consciousnesses are the
theater. But more, we wish to put there physical facts, these I know not
what with which we people space and which no consciousness sees directly.
This is necessary because without it science could not exist. In a word,
psychologic time is given to us and must needs create scientific and
physical time. There the difficulty begins, or rather the difficulties, for there
are two.
Think of two consciousnesses, which are like two worlds impenetrable
one to the other. By what right do we strive to put them into the same mold,
to measure them by the same standard? Is it not as if one strove to measure
length with a gram or weight with a meter? And besides, why do we speak
of measuring? We know perhaps that some fact is anterior to some other,
but not by how much it is anterior.
Therefore two difficulties: (1) Can we transform psychologic time, which
is qualitative, into a quantitative time? (2) Can we reduce to one and the
same measure facts which transpire in different worlds?

III
The first difficulty has long been noticed; it has been the subject of long
discussions and one may say the question is settled. We have not a direct
intuition of the equality of two intervals of time. The persons who believe
they possess this intuition are dupes of an illusion. When I say, from noon
to one the same time passes as from two to three, what meaning has this
affirmation?

The least reflection shows that by itself it has none at all. It will only
have that which I choose to give it, by a definition which will certainly
possess a certain degree of arbitrariness. Psychologists could have done
without this definition; physicists and astronomers could not; let us see how
they have managed.
To measure time they use the pendulum and they suppose by definition
that all the beats of this pendulum are of equal duration. But this is only a
first approximation; the temperature, the resistance of the air, the barometric
pressure, make the pace of the pendulum vary. If we could escape these
sources of error, we should obtain a much closer approximation, but it
would still be only an approximation. New causes, hitherto neglected,
electric, magnetic or others, would introduce minute perturbations.
In fact, the best chronometers must be corrected from time to time, and
the corrections are made by the aid of astronomic observations;
arrangements are made so that the sidereal clock marks the same hour when
the same star passes the meridian. In other words, it is the sidereal day, that
is, the duration of the rotation of the earth, which is the constant unit of
time. It is supposed, by a new definition substituted for that based on the
beats of the pendulum, that two complete rotations of the earth about its
axis have the same duration.
However, the astronomers are still not content with this definition. Many
of them think that the tides act as a check on our globe, and that the rotation
of the earth is becoming slower and slower. Thus would be explained the
apparent acceleration of the motion of the moon, which would seem to be
going more rapidly than theory permits because our watch, which is the
earth, is going slow.

IV
All this is unimportant, one will say; doubtless our instruments of
measurement are imperfect, but it suffices that we can conceive a perfect
instrument. This ideal can not be reached, but it is enough to have
conceived it and so to have put rigor into the definition of the unit of time.
The trouble is that there is no rigor in the definition. When we use the
pendulum to measure time, what postulate do we implicitly admit? It is that

the duration of two identical phenomena is the same; or, if you prefer, that
the same causes take the same time to produce the same effects.
And at first blush, this is a good definition of the equality of two
durations. But take care. Is it impossible that experiment may some day
contradict our postulate?
Let me explain myself. I suppose that at a certain place in the world the
phenomenon α happens, causing as consequence at the end of a certain time
the effect α´. At another place in the world very far away from the first,
happens the phenomenon β, which causes as consequence the effect β´. The
phenomena α and β are simultaneous, as are also the effects α´ and β´.
Later, the phenomenon α is reproduced under approximately the same
conditions as before, and simultaneously the phenomenon β is also
reproduced at a very distant place in the world and almost under the same
circumstances. The effects α´ and β´ also take place. Let us suppose that the
effect α´ happens perceptibly before the effect β´.
If experience made us witness such a sight, our postulate would be
contradicted. For experience would tell us that the first duration αα´ is equal
to the first duration ββ´ and that the second duration αα´ is less than the
second duration ββ´. On the other hand, our postulate would require that the
two durations αα´ should be equal to each other, as likewise the two
durations ββ´. The equality and the inequality deduced from experience
would be incompatible with the two equalities deduced from the postulate.
Now can we affirm that the hypotheses I have just made are absurd?
They are in no wise contrary to the principle of contradiction. Doubtless
they could not happen without the principle of sufficient reason seeming
violated. But to justify a definition so fundamental I should prefer some
other guarantee.

V
But that is not all. In physical reality one cause does not produce a given
effect, but a multitude of distinct causes contribute to produce it, without
our having any means of discriminating the part of each of them.

Physicists seek to make this distinction; but they make it only
approximately, and, however they progress, they never will make it except
approximately. It is approximately true that the motion of the pendulum is
due solely to the earth's attraction; but in all rigor every attraction, even of
Sirius, acts on the pendulum.
Under these conditions, it is clear that the causes which have produced a
certain effect will never be reproduced except approximately. Then we
should modify our postulate and our definition. Instead of saying: 'The
same causes take the same time to produce the same effects,' we should say:
'Causes almost identical take almost the same time to produce almost the
same effects.'
Our definition therefore is no longer anything but approximate. Besides,
as M. Calinon very justly remarks in a recent memoir:[7]
One of the circumstances of any phenomenon is the velocity of the earth's rotation; if this velocity
of rotation varies, it constitutes in the reproduction of this phenomenon a circumstance which no
longer remains the same. But to suppose this velocity of rotation constant is to suppose that we know
how to measure time.

Our definition is therefore not yet satisfactory; it is certainly not that
which the astronomers of whom I spoke above implicitly adopt, when they
affirm that the terrestrial rotation is slowing down.
What meaning according to them has this affirmation? We can only
understand it by analyzing the proofs they give of their proposition. They
say first that the friction of the tides producing heat must destroy vis viva.
They invoke therefore the principle of vis viva, or of the conservation of
energy.
They say next that the secular acceleration of the moon, calculated
according to Newton's law, would be less than that deduced from
observations unless the correction relative to the slowing down of the
terrestrial rotation were made. They invoke therefore Newton's law. In other
words, they define duration in the following way: time should be so defined
that Newton's law and that of vis viva may be verified. Newton's law is an
experimental truth; as such it is only approximate, which shows that we still
have only a definition by approximation.

If now it be supposed that another way of measuring time is adopted, the
experiments on which Newton's law is founded would none the less have
the same meaning. Only the enunciation of the law would be different,
because it would be translated into another language; it would evidently be
much less simple. So that the definition implicitly adopted by the
astronomers may be summed up thus: Time should be so defined that the
equations of mechanics may be as simple as possible. In other words, there
is not one way of measuring time more true than another; that which is
generally adopted is only more convenient. Of two watches, we have no
right to say that the one goes true, the other wrong; we can only say that it
is advantageous to conform to the indications of the first.
The difficulty which has just occupied us has been, as I have said, often
pointed out; among the most recent works in which it is considered, I may
mention, besides M. Calinon's little book, the treatise on mechanics of
Andrade.

VI
The second difficulty has up to the present attracted much less attention;
yet it is altogether analogous to the preceding; and even, logically, I should
have spoken of it first.
Two psychological phenomena happen in two different consciousnesses;
when I say they are simultaneous, what do I mean? When I say that a
physical phenomenon, which happens outside of every consciousness, is
before or after a psychological phenomenon, what do I mean?
In 1572, Tycho Brahe noticed in the heavens a new star. An immense
conflagration had happened in some far distant heavenly body; but it had
happened long before; at least two hundred years were necessary for the
light from that star to reach our earth. This conflagration therefore happened
before the discovery of America. Well, when I say that; when, considering
this gigantic phenomenon, which perhaps had no witness, since the
satellites of that star were perhaps uninhabited, I say this phenomenon is
anterior to the formation of the visual image of the isle of Española in the
consciousness of Christopher Columbus, what do I mean?

A little reflection is sufficient to understand that all these affirmations
have by themselves no meaning. They can have one only as the outcome of
a convention.

VII
We should first ask ourselves how one could have had the idea of putting
into the same frame so many worlds impenetrable to one another. We
should like to represent to ourselves the external universe, and only by so
doing could we feel that we understood it. We know we never can attain this
representation: our weakness is too great. But at least we desire the ability
to conceive an infinite intelligence for which this representation could be
possible, a sort of great consciousness which should see all, and which
should classify all in its time, as we classify, in our time, the little we see.
This hypothesis is indeed crude and incomplete, because this supreme
intelligence would be only a demigod; infinite in one sense, it would be
limited in another, since it would have only an imperfect recollection of the
past; and it could have no other, since otherwise all recollections would be
equally present to it and for it there would be no time. And yet when we
speak of time, for all which happens outside of us, do we not unconsciously
adopt this hypothesis; do we not put ourselves in the place of this imperfect
god; and do not even the atheists put themselves in the place where god
would be if he existed?
What I have just said shows us, perhaps, why we have tried to put all
physical phenomena into the same frame. But that can not pass for a
definition of simultaneity, since this hypothetical intelligence, even if it
existed, would be for us impenetrable. It is therefore necessary to seek
something else.

VIII
The ordinary definitions which are proper for psychologic time would
suffice us no more. Two simultaneous psychologic facts are so closely
bound together that analysis can not separate without mutilating them. Is it
the same with two physical facts? Is not my present nearer my past of
yesterday than the present of Sirius?

It has also been said that two facts should be regarded as simultaneous
when the order of their succession may be inverted at will. It is evident that
this definition would not suit two physical facts which happen far from one
another, and that, in what concerns them, we no longer even understand
what this reversibility would be; besides, succession itself must first be
defined.

IX
Let us then seek to give an account of what is understood by simultaneity
or antecedence, and for this let us analyze some examples.
I write a letter; it is afterward read by the friend to whom I have
addressed it. There are two facts which have had for their theater two
different consciousnesses. In writing this letter I have had the visual image
of it, and my friend has had in his turn this same visual image in reading the
letter. Though these two facts happen in impenetrable worlds, I do not
hesitate to regard the first as anterior to the second, because I believe it is its
cause.
I hear thunder, and I conclude there has been an electric discharge; I do
not hesitate to consider the physical phenomenon as anterior to the auditory
image perceived in my consciousness, because I believe it is its cause.
Behold then the rule we follow, and the only one we can follow: when a
phenomenon appears to us as the cause of another, we regard it as anterior.
It is therefore by cause that we define time; but most often, when two facts
appear to us bound by a constant relation, how do we recognize which is the
cause and which the effect? We assume that the anterior fact, the
antecedent, is the cause of the other, of the consequent. It is then by time
that we define cause. How save ourselves from this petitio principii?
We say now post hoc, ergo propter hoc; now propter hoc, ergo post hoc;
shall we escape from this vicious circle?

X
Let us see, not how we succeed in escaping, for we do not completely
succeed, but how we try to escape.

I execute a voluntary act A and I feel afterward a sensation D, which I
regard as a consequence of the act A; on the other hand, for whatever
reason, I infer that this consequence is not immediate, but that outside my
consciousness two facts B and C, which I have not witnessed, have
happened, and in such a way that B is the effect of A, that C is the effect of
B, and D of C.
But why? If I think I have reason to regard the four facts A, B, C, D, as
bound to one another by a causal connection, why range them in the causal
order A B C D, and at the same time in the chronologic order A B C D,
rather than in any other order?
I clearly see that in the act A I have the feeling of having been active,
while in undergoing the sensation D I have that of having been passive.
This is why I regard A as the initial cause and D as the ultimate effect; this
is why I put A at the beginning of the chain and D at the end; but why put B
before C rather than C before B?
If this question is put, the reply ordinarily is: we know that it is B which
is the cause of C because we always see B happen before C. These two
phenomena, when witnessed, happen in a certain order; when analogous
phenomena happen without witness, there is no reason to invert this order.
Doubtless, but take care; we never know directly the physical phenomena
B and C. What we know are sensations B´ and C´ produced respectively by
B and C. Our consciousness tells us immediately that B´ precedes C´ and
we suppose that B and C succeed one another in the same order.
This rule appears in fact very natural, and yet we are often led to depart
from it. We hear the sound of the thunder only some seconds after the
electric discharge of the cloud. Of two flashes of lightning, the one distant,
the other near, can not the first be anterior to the second, even though the
sound of the second comes to us before that of the first?

XI
Another difficulty; have we really the right to speak of the cause of a
phenomenon? If all the parts of the universe are interchained in a certain
measure, any one phenomenon will not be the effect of a single cause, but

the resultant of causes infinitely numerous; it is, one often says, the
consequence of the state of the universe a moment before. How enunciate
rules applicable to circumstances so complex? And yet it is only thus that
these rules can be general and rigorous.
Not to lose ourselves in this infinite complexity, let us make a simpler
hypothesis. Consider three stars, for example, the sun, Jupiter and Saturn;
but, for greater simplicity, regard them as reduced to material points and
isolated from the rest of the world. The positions and the velocities of three
bodies at a given instant suffice to determine their positions and velocities
at the following instant, and consequently at any instant. Their positions at
the instant t determine their positions at the instant t + h as well as their
positions at the instant t − h.
Even more; the position of Jupiter at the instant t, together with that of
Saturn at the instant t + a, determines the position of Jupiter at any instant
and that of Saturn at any instant.
The aggregate of positions occupied by Jupiter at the instant t + e and
Saturn at the instant t + a + e is bound to the aggregate of positions
occupied by Jupiter at the instant t and Saturn at the instant t + a, by laws as
precise as that of Newton, though more complicated. Then why not regard
one of these aggregates as the cause of the other, which would lead to
considering as simultaneous the instant t of Jupiter and the instant t + a of
Saturn?
In answer there can only be reasons, very strong, it is true, of
convenience and simplicity.

XII
But let us pass to examples less artificial; to understand the definition
implicitly supposed by the savants, let us watch them at work and look for
the rules by which they investigate simultaneity.
I will take two simple examples, the measurement of the velocity of light
and the determination of longitude.

When an astronomer tells me that some stellar phenomenon, which his
telescope reveals to him at this moment, happened, nevertheless, fifty years
ago, I seek his meaning, and to that end I shall ask him first how he knows
it, that is, how he has measured the velocity of light.
He has begun by supposing that light has a constant velocity, and in
particular that its velocity is the same in all directions. That is a postulate
without which no measurement of this velocity could be attempted. This
postulate could never be verified directly by experiment; it might be
contradicted by it if the results of different measurements were not
concordant. We should think ourselves fortunate that this contradiction has
not happened and that the slight discordances which may happen can be
readily explained.
The postulate, at all events, resembling the principle of sufficient reason,
has been accepted by everybody; what I wish to emphasize is that it
furnishes us with a new rule for the investigation of simultaneity, entirely
different from that which we have enunciated above.
This postulate assumed, let us see how the velocity of light has been
measured. You know that Roemer used eclipses of the satellites of Jupiter,
and sought how much the event fell behind its prediction. But how is this
prediction made? It is by the aid of astronomic laws; for instance Newton's
law.
Could not the observed facts be just as well explained if we attributed to
the velocity of light a little different value from that adopted, and supposed
Newton's law only approximate? Only this would lead to replacing
Newton's law by another more complicated. So for the velocity of light a
value is adopted, such that the astronomic laws compatible with this value
may be as simple as possible. When navigators or geographers determine a
longitude, they have to solve just the problem we are discussing; they must,
without being at Paris, calculate Paris time. How do they accomplish it?
They carry a chronometer set for Paris. The qualitative problem of
simultaneity is made to depend upon the quantitative problem of the
measurement of time. I need not take up the difficulties relative to this latter
problem, since above I have emphasized them at length.

Or else they observe an astronomic phenomenon, such as an eclipse of
the moon, and they suppose that this phenomenon is perceived
simultaneously from all points of the earth. That is not altogether true, since
the propagation of light is not instantaneous; if absolute exactitude were
desired, there would be a correction to make according to a complicated
rule.
Or else finally they use the telegraph. It is clear first that the reception of
the signal at Berlin, for instance, is after the sending of this same signal
from Paris. This is the rule of cause and effect analyzed above. But how
much after? In general, the duration of the transmission is neglected and the
two events are regarded as simultaneous. But, to be rigorous, a little
correction would still have to be made by a complicated calculation; in
practise it is not made, because it would be well within the errors of
observation; its theoretic necessity is none the less from our point of view,
which is that of a rigorous definition. From this discussion, I wish to
emphasize two things: (1) The rules applied are exceedingly various. (2) It
is difficult to separate the qualitative problem of simultaneity from the
quantitative problem of the measurement of time; no matter whether a
chronometer is used, or whether account must be taken of a velocity of
transmission, as that of light, because such a velocity could not be measured
without measuring a time.

XIII
To conclude: We have not a direct intuition of simultaneity, nor of the
equality of two durations. If we think we have this intuition, this is an
illusion. We replace it by the aid of certain rules which we apply almost
always without taking count of them.
But what is the nature of these rules? No general rule, no rigorous rule; a
multitude of little rules applicable to each particular case.
These rules are not imposed upon us and we might amuse ourselves in
inventing others; but they could not be cast aside without greatly
complicating the enunciation of the laws of physics, mechanics and
astronomy.

We therefore choose these rules, not because they are true, but because
they are the most convenient, and we may recapitulate them as follows:
"The simultaneity of two events, or the order of their succession, the
equality of two durations, are to be so defined that the enunciation of the
natural laws may be as simple as possible. In other words, all these rules, all
these definitions are only the fruit of an unconscious opportunism."

CHAPTER III

The Notion of Space

1. Introduction
In the articles I have heretofore devoted to space I have above all
emphasized the problems raised by non-Euclidean geometry, while leaving
almost completely aside other questions more difficult of approach, such as
those which pertain to the number of dimensions. All the geometries I
considered had thus a common basis, that tridimensional continuum which
was the same for all and which differentiated itself only by the figures one
drew in it or when one aspired to measure it.
In this continuum, primitively amorphous, we may imagine a network of
lines and surfaces, we may then convene to regard the meshes of this net as
equal to one another, and it is only after this convention that this continuum,
become measurable, becomes Euclidean or non-Euclidean space. From this
amorphous continuum can therefore arise indifferently one or the other of
the two spaces, just as on a blank sheet of paper may be traced indifferently
a straight or a circle.
In space we know rectilinear triangles the sum of whose angles is equal
to two right angles; but equally we know curvilinear triangles the sum of
whose angles is less than two right angles. The existence of the one sort is
not more doubtful than that of the other. To give the name of straights to the
sides of the first is to adopt Euclidean geometry; to give the name of
straights to the sides of the latter is to adopt the non-Euclidean geometry. So