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% The Project Gutenberg EBook of Science and hypothesis, by Henri Poincaré%
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% This eBook is for the use of anyone anywhere at no cost and with        %
% almost no restrictions whatsoever.  You may copy it, give it away or    %
% re-use it under the terms of the Project Gutenberg License included     %
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%                                                                         %
% Title: Science and hypothesis                                           %
%                                                                         %
% Author: Henri Poincaré                                                  %
%                                                                         %
% Release Date: August 21, 2011 [EBook #37157]                            %
%                                                                         %
% Language: English                                                       %
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% *** START OF THIS PROJECT GUTENBERG EBOOK SCIENCE AND HYPOTHESIS ***    %
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The Project Gutenberg EBook of Science and hypothesis, by Henri Poincaré

This eBook is for the use of anyone anywhere at no cost and with
almost no restrictions whatsoever.  You may copy it, give it away or
re-use it under the terms of the Project Gutenberg License included
with this eBook or online at www.gutenberg.net


Title: Science and hypothesis

Author: Henri Poincaré

Release Date: August 21, 2011 [EBook #37157]

Language: English

Character set encoding: ISO-8859-1

*** START OF THIS PROJECT GUTENBERG EBOOK SCIENCE AND HYPOTHESIS ***
\end{PGtext}
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Produced by Andrew D. Hwang
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%%%%%%%%%%%%%%%%%%%%%%%%%%% FRONT MATTER %%%%%%%%%%%%%%%%%%%%%%%%%%
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{\Large SCIENCE AND HYPOTHESIS}
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\PageSep{iii}
\begin{center}
\huge SCIENCE \\
AND HYPOTHESIS
\vfill

\normalsize
{\footnotesize BY} \\
H. POINCARÉ, \\
{\scriptsize MEMBER OF THE INSTITUTE OF FRANCE.}
\vfill

{\small\textsc{With a Preface by}} \\
\textsc{J. LARMOR, D.Sc., Sec. R.S.}, \\
{\scriptsize\textit{Lucasian Professor of Mathematics in the University of Cambridge.}}
\vfill\vfill

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THE WALTER SCOTT PUBLISHING CO., LTD \\
{\footnotesize NEW YORK: 3 EAST 14TH STREET.} \\
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\iffalse
CONTENTS.

                                       PAGE
Translator's Note........................ix

Introduction.............................xi

Author's Preface........................xxi


PART I.

NUMBER AND MAGNITUDE.

CHAPTER I.
On the Nature of Mathematical Reasoning...1

CHAPTER II.
Mathematical Magnitude and Experiment....17


PART II.

SPACE.

CHAPTER III.
Non-Euclidean Geometries.................35
\PageSep{vi}

CHAPTER IV.
Space and Geometry.......................51

CHAPTER V.
Experiment and Geometry..................72


PART III.

FORCE.

CHAPTER VI.
The Classical Mechanics..................89

CHAPTER VII.
Relative and Absolute Motion............111

CHAPTER VIII.
Energy and Thermo-dynamics..............123


PART IV.

NATURE.

CHAPTER IX.
Hypotheses in Physics...................140
\PageSep{vii}

CHAPTER X.
The Theories of Modern Physics..........160

CHAPTER XI.
The Calculus of Probabilities...........183

CHAPTER XII.
Optics and Electricity..................211

CHAPTER XIII.
Electro-dynamics........................225
\fi
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%[Blank page]
\PageSep{ix}


\OtherChapter{Translator's Note.}

\First{The} translator wishes to express his indebtedness
to Professor Larmor, for kindly consenting
to introduce the author of \Title{Science and Hypothesis}
to English readers; to Dr.~F.~S. Macaulay and
Mr.~C.~S. Jackson,~M.A., who have read the whole
of the proofs and have greatly helped by suggestions;
also to Professor G.~H. Bryan,~F.R.S., who
has read the proofs of \ChapRef{VIII}., and whose
criticisms have been most valuable.

%[** TN: William John Greenstreet (1861--1930), not identified by name]
\Signature{W.\;J.\;G.}{\textit{February} 1905.}
\PageSep{x}
%[Blank page]
\PageSep{xi}


\OtherChapter{Introduction.}

\First{It} is to be hoped that, as a consequence of the
present active scrutiny of our educational aims
and methods, and of the resulting encouragement
of the study of modern languages, we shall not
remain, as a nation, so much isolated from
ideas and tendencies in continental thought and
literature as we have been in the past. As things
are, however, the translation of this book is
doubtless required; at any rate, it brings vividly
before us an instructive point of view. Though
some of M.~Poincaré's chapters have been collected
from well-known treatises written several years
ago, and indeed are sometimes in detail not quite
up to date, besides occasionally suggesting the
suspicion that his views may possibly have been
modified in the interval, yet their publication in
a compact form has excited a warm welcome in
this country.

It must be confessed that the English language
\PageSep{xii}
hardly lends itself as a perfect medium for the
rendering of the delicate shades of suggestion
and allusion characteristic of M.~Poincaré's play
around his subject; notwithstanding the excellence
of the translation, loss in this respect is
inevitable.

There has been of late a growing trend of
opinion, prompted in part by general philosophical
views, in the direction that the theoretical constructions
of physical science are largely factitious,
that instead of presenting a valid image of the
relations of things on which further progress can
be based, they are still little better than a mirage.
The best method of abating this scepticism is to
become acquainted with the real scope and modes
of application of conceptions which, in the popular
language of superficial exposition---and even in
the unguarded and playful paradox of their
authors, intended only for the instructed eye---often
look bizarre enough. But much advantage
will accrue if men of science become their own
epistemologists, and show to the world by critical
exposition in non-technical terms of the results
and methods of their constructive work, that more
than mere instinct is involved in it: the community
has indeed a right to expect as much as
this.
\PageSep{xiii}

It would be hard to find any one better
qualified for this kind of exposition, either
from the profundity of his own mathematical
achievements, or from the extent and freshness
of his interest in the theories of physical science,
than the author of this book. If an appreciation
might be ventured on as regards the later chapters,
they are, perhaps, intended to present the stern
logical analyst quizzing the cultivator of physical
ideas as to what he is driving at, and whither he
expects to go, rather than any responsible attempt
towards a settled confession of faith. Thus, when
M.~Poincaré allows himself for a moment to
indulge in a process of evaporation of the
Principle of Energy, he is content to sum up:
``Eh bien, quelles que soient les notions nouvelles
que les expériences futures nous donneront sur le
monde, nous sommes sûrs d'avance qu'il y aura
quelque chose qui demeurera constant et que nous
pourrons appeler \Foreign{énergie}'' (\Pageref{166}), and to leave
the matter there for his readers to think it out.
Though hardly necessary in the original French, it
may not now be superfluous to point out that
independent reflection and criticism on the part
of the reader are tacitly implied here as elsewhere.

An interesting passage is the one devoted to
\PageSep{xiv}
Maxwell's theory of the functions of the æther,
and the comparison of the close-knit theories of
the classical French mathematical physicists with
the somewhat loosely-connected \Foreign{corpus} of ideas by
which Maxwell, the interpreter and successor of
Faraday, has (posthumously) recast the whole
face of physical science. How many times has
that theory been re-written since Maxwell's day?
and yet how little has it been altered in essence,
except by further developments in the problem of
moving bodies, from the form in which he left it!
If, as M.~Poincaré remarks, the French instinct
for precision and lucid demonstration sometimes
finds itself ill at ease with physical theories of
the British school, he as readily admits (\Pagerefs{223}{224}),
and indeed fully appreciates, the advantages
on the other side. Our own mental philosophers
have been shocked at the point of view indicated
by the proposition hazarded by Laplace, that a
sufficiently developed intelligence, if it were made
acquainted with the positions and motions of the
atoms at any instant, could predict all future
history: no amount of demur suffices sometimes
to persuade them that this is not a conception
universally entertained in physical science. It
was not so even in Laplace's own day. From
the point of view of the study of the evolution
\PageSep{xv}
of the sciences, there are few episodes more
instructive than the collision between Laplace
and Young with regard to the theory of capillarity.
The precise and intricate mathematical
analysis of Laplace, starting from fixed preconceptions
regarding atomic forces which were
to remain intact throughout the logical development
of the argument, came into contrast with the
tentative, mobile intuitions of Young; yet the
latter was able to grasp, by sheer direct mental
force, the fruitful though partial analogies of this
recondite class of phenomena with more familiar
operations of nature, and to form a direct picture
of the way things interacted, such as could only
have been illustrated, quite possibly damaged or
obliterated, by premature effort to translate it
into elaborate analytical formulas. The \Foreign{aperçus}
of Young were apparently devoid of all cogency
to Laplace; while Young expressed, doubtless in
too extreme a way, his sense of the inanity of the
array of mathematical logic of his rival. The
subsequent history involved the Nemesis that the
fabric of Laplace was taken down and reconstructed
in the next generation by Poisson; while
the modern cultivator of the subject turns, at any
rate in England, to neither of those expositions
for illumination, but rather finds in the partial
\PageSep{xvi}
and succinct indications of Young the best starting-point
for further effort.

It seems, however, hard to accept entirely
the distinction suggested (\Pageref{213}) between the
methods of cultivating theoretical physics in
the two countries. To mention only two
transcendent names which stand at the very
front of two of the greatest developments of
physical science of the last century, Carnot and
Fresnel, their procedure was certainly not on the
lines thus described. Possibly it is not devoid of
significance that each of them attained his first
effective recognition from the British school.

It may, in fact, be maintained that the part
played by mechanical and such-like theories---analogies
if you will---is an essential one. The
reader of this book will appreciate that the human
mind has need of many instruments of comparison
and discovery besides the unrelenting logic of the
infinitesimal calculus. The dynamical basis which
underlies the objects of our most frequent experience
has now been systematised into a great
calculus of exact thought, and traces of new real
relationships may come out more vividly when
considered in terms of our familiar acquaintance
with dynamical systems than when formulated
under the paler shadow of more analytical abstractions.
\PageSep{xvii}
It is even possible for a constructive
physicist to conduct his mental operations entirely
by dynamical images, though Helmholtz, as well
as our author, seems to class a predilection in this
direction as a British trait. A time arrives when,
as in other subjects, ideas have crystallised out
into distinctness; their exact verification and
development then becomes a problem in mathematical
physics. But whether the mechanical
analogies still survive, or new terms are now
introduced devoid of all naïve mechanical bias,
it matters essentially little. The precise determination
of the relations of things in the
rational scheme of nature in which we find
ourselves is the fundamental task, and for its
fulfilment in any direction advantage has to be
taken of our knowledge, even when only partial,
of new aspects and types of relationship which
may have become familiar perhaps in quite
different fields. Nor can it be forgotten that the
most fruitful and fundamental conceptions of
abstract pure mathematics itself have often been
suggested from these mechanical ideas of flux
and force, where the play of intuition is our
most powerful guide. The study of the historical
evolution of physical theories is essential to the
complete understanding of their import. It is in
\PageSep{xviii}
the mental workshop of a Fresnel, a Kelvin, or
a Helmholtz, that profound ideas of the deep
things of Nature are struck out and assume
form; when pondered over and paraphrased by
philosophers we see them react on the conduct
of life: it is the business of criticism to polish
them gradually to the common measure of human
understanding. Oppressed though we are with
the necessity of being specialists, if we are
to know anything thoroughly in these days of
accumulated details, we may at any rate profitably
study the historical evolution of knowledge
over a field wider than our own.

The aspect of the subject which has here been
dwelt on is that scientific progress, considered
historically, is not a strictly logical process, and
does not proceed by syllogisms. New ideas
emerge dimly into intuition, come into consciousness
from nobody knows where, and become
the material on which the mind operates, forging
them gradually into consistent doctrine, which
can be welded on to existing domains of knowledge.
But this process is never complete: a
crude connection can always be pointed to by a
logician as an indication of the imperfection of
human constructions.

If intuition plays a part which is so important,
\PageSep{xix}
it is surely necessary that we should possess a firm
grasp of its limitations. In M.~Poincaré's earlier
chapters the reader can gain very pleasantly a
vivid idea of the various and highly complicated
ways of docketing our perceptions of the relations
of external things, all equally valid, that were
open to the human race to develop. Strange to
say, they never tried any of them; and, satisfied
with the very remarkable practical fitness of the
scheme of geometry and dynamics that came
naturally to hand, did not consciously trouble
themselves about the possible existence of others
until recently. Still more recently has it been
found that the good Bishop Berkeley's logical
jibes against the Newtonian ideas of fluxions and
limiting ratios cannot be adequately appeased in
the rigorous mathematical conscience, until our
apparent continuities are resolved mentally into
discrete aggregates which we only partially
apprehend. The irresistible impulse to atomize
everything thus proves to be not merely a disease
of the physicist; a deeper origin, in the nature
of knowledge itself, is suggested.

Everywhere want of absolute, exact adaptation
can be detected, if pains are taken, between the
various constructions that result from our mental
activity and the impressions which give rise to
\PageSep{xx}
them. The bluntness of our unaided sensual
perceptions, which are the source in part of the
intuitions of the race, is well brought out in this
connection by M.~Poincaré. Is there real contradiction?
Harmony usually proves to be recovered
by shifting our attitude to the phenomena.
All experience leads us to interpret the totality of
things as a consistent cosmos---undergoing evolution,
the naturalists will say---in the large-scale
workings of which we are interested spectators
and explorers, while of the inner relations and
ramifications we only apprehend dim glimpses.
When our formulation of experience is imperfect
or even paradoxical, we learn to attribute the
fault to our point of view, and to expect that
future adaptation will put it right. But Truth
resides in a deep well, and we shall never get
to the bottom. Only, while deriving enjoyment
and insight from M.~Poincaré's Socratic exposition
of the limitations of the human outlook on
the universe, let us beware of counting limitation
as imperfection, and drifting into an inadequate
conception of the wonderful fabric of human
knowledge.

\Signature{J. LARMOR.}{}
\PageSep{xxi}


\OtherChapter{Author's Preface.}

\First{To} the superficial observer scientific truth is unassailable,
the logic of science is infallible; and if
scientific men sometimes make mistakes, it is
because they have not understood the rules of
the game. Mathematical truths are derived from
a few self-evident propositions, by a chain of
flawless reasonings; they are imposed not only on
us, but on Nature itself. By them the Creator is
fettered, as it were, and His choice is limited to
a relatively small number of solutions. A few
experiments, therefore, will be sufficient to enable
us to determine what choice He has made. From
each experiment a number of consequences will
follow by a series of mathematical deductions,
and in this way each of them will reveal to us a
corner of the universe. This, to the minds of most
people, and to students who are getting their first
ideas of physics, is the origin of certainty in
science. This is what they take to be the rôle of
\PageSep{xxii}
experiment and mathematics. And thus, too, it
was understood a hundred years ago by many
men of science who dreamed of constructing the
world with the aid of the smallest possible amount
of material borrowed from experiment.

But upon more mature reflection the position
held by hypothesis was seen; it was recognised that
it is as necessary to the experimenter as it is to the
mathematician. And then the doubt arose if all
these constructions are built on solid foundations.
The conclusion was drawn that a breath would
bring them to the ground. This sceptical attitude
does not escape the charge of superficiality. To
doubt everything or to believe everything are two
equally convenient solutions; both dispense with
the necessity of reflection.

Instead of a summary condemnation we should
examine with the utmost care the rôle of hypothesis;
we shall then recognise not only that it is
necessary, but that in most cases it is legitimate.
We shall also see that there are several kinds of
hypotheses; that some are verifiable, and when
once confirmed by experiment become truths of
great fertility; that others may be useful to us in
fixing our ideas; and finally, that others are
hypotheses only in appearance, and reduce to
definitions or to conventions in disguise. The
\PageSep{xxiii}
latter are to be met with especially in mathematics
and in the sciences to which it is applied. From
them, indeed, the sciences derive their rigour;
such conventions are the result of the unrestricted
activity of the mind, which in this domain recognises
no obstacle. For here the mind may affirm
because it lays down its own laws; but let us
clearly understand that while these laws are
imposed on \emph{our} science, which otherwise could
not exist, they are not imposed on Nature. Are
they then arbitrary? No; for if they were, they
would not be fertile. Experience leaves us our
freedom of choice, but it guides us by helping us to
discern the most convenient path to follow. Our
laws are therefore like those of an absolute
monarch, who is wise and consults his council of
state. Some people have been struck by this
characteristic of free convention which may be
recognised in certain fundamental principles of
the sciences. Some have set no limits to their
generalisations, and at the same time they have
forgotten that there is a difference between liberty
and the purely arbitrary. So that they are compelled
to end in what is called \emph{nominalism}; they
have asked if the \Foreign{savant} is not the dupe of his
own definitions, and if the world he thinks he has
discovered is not simply the creation of his own
\PageSep{xxiv}
caprice.\footnote
  {Cf.\ M.~le~Roy: ``Science et Philosophie,'' \Title{Revue de Métaphysique
  et de Morale}, 1901.}
Under these conditions science would
retain its certainty, but would not attain its object,
and would become powerless. Now, we daily see
what science is doing for us. This could not be
unless it taught us something about reality; the
aim of science is not things themselves, as the
dogmatists in their simplicity imagine, but the
relations between things; outside those relations
there is no reality knowable.

Such is the conclusion to which we are led; but
to reach that conclusion we must pass in review
the series of sciences from arithmetic and
geometry to mechanics and experimental physics.
What is the nature of mathematical reasoning?
Is it really deductive, as is commonly supposed?
Careful analysis shows us that it is nothing of the
kind; that it participates to some extent in the
nature of inductive reasoning, and for that reason
it is fruitful. But none the less does it retain its
character of absolute rigour; and this is what
must first be shown.

When we know more of this instrument which
is placed in the hands of the investigator by
mathematics, we have then to analyse another
fundamental idea, that of mathematical magnitude.
\PageSep{xxv}
Do we find it in nature, or have we ourselves
introduced it? And if the latter be the
case, are we not running a risk of coming to
incorrect conclusions all round? Comparing the
rough data of our senses with that extremely complex
and subtle conception which mathematicians
call magnitude, we are compelled to recognise a
divergence. The framework into which we wish
to make everything fit is one of our own construction;
but we did not construct it at random, we
constructed it by measurement so to speak; and
that is why we can fit the facts into it without
altering their essential qualities.

Space is another framework which we impose
on the world. Whence are the first principles of
geometry derived? Are they imposed on us by
logic? Lobatschewsky, by inventing non-Euclidean
geometries, has shown that this is not the case.
Is space revealed to us by our senses? No; for
the space revealed to us by our senses is absolutely
different from the space of geometry. Is geometry
derived from experience? Careful discussion will
give the answer---no! We therefore conclude that
the principles of geometry are only conventions;
but these conventions are not arbitrary, and if
transported into another world (which I shall
call the non-Euclidean world, and which I shall
\PageSep{xxvi}
endeavour to describe), we shall find ourselves
compelled to adopt more of them.

In mechanics we shall be led to analogous conclusions,
and we shall see that the principles of
this science, although more directly based on
experience, still share the conventional character
of the geometrical postulates. So far, nominalism
triumphs; but we now come to the physical
sciences, properly so called, and here the scene
changes. We meet with hypotheses of another
kind, and we fully grasp how fruitful they are.
No doubt at the outset theories seem unsound,
and the history of science shows us how ephemeral
they are; but they do not entirely perish, and of
each of them some traces still remain. It is these
traces which we must try to discover, because in
them and in them alone is the true reality.

The method of the physical sciences is based
upon the induction which leads us to expect the
recurrence of a phenomenon when the circumstances
which give rise to it are repeated. If all
the circumstances could be simultaneously reproduced,
this principle could be fearlessly applied;
but this never happens; some of the circumstances
will always be missing. Are we absolutely certain
that they are unimportant? Evidently not! It
may be probable, but it cannot be rigorously
\PageSep{xxvii}
certain. Hence the importance of the rôle that is
played in the physical sciences by the law of
probability. The calculus of probabilities is therefore
not merely a recreation, or a guide to the
baccarat player; and we must thoroughly examine
the principles on which it is based. In this connection
I have but very incomplete results to lay
before the reader, for the vague instinct which
enables us to determine probability almost defies
analysis. After a study of the conditions under
which the work of the physicist is carried on, I
have thought it best to show him at work. For
this purpose I have taken instances from the
history of optics and of electricity. We shall thus
see how the ideas of Fresnel and Maxwell took
their rise, and what unconscious hypotheses were
made by Ampère and the other founders of
electro-dynamics.
\PageSep{xxviii}
%[Blank page]
\PageSep{1}
\MainMatter
%[** TN: Commented text is printed by the \Part macro]
% SCIENCE AND HYPOTHESIS.


\Part{I.}{Number and Magnitude.}

\Chapter[Nature of Mathematical Reasoning.]{I.}{On the Nature of Mathematical Reasoning.}

\Section{I.}

\First{The} very possibility of mathematical science seems
an insoluble contradiction. If this science is only
deductive in appearance, from whence is derived
that perfect rigour which is challenged by none?
If, on the contrary, all the propositions which it
enunciates may be derived in order by the rules
of formal logic, how is it that mathematics is
not reduced to a gigantic tautology? The syllogism
can teach us nothing essentially new, and
if everything must spring from the principle of
identity, then everything should be capable of
being reduced to that principle. Are we then to
admit that the enunciations of all the theorems
\PageSep{2}
with which so many volumes are filled, are only
indirect ways of saying that A~is~A?

No doubt we may refer back to axioms which
are at the source of all these reasonings. If it is
felt that they cannot be reduced to the principle of
contradiction, if we decline to see in them any
more than experimental facts which have no part
or lot in mathematical necessity, there is still one
resource left to us: we may class them among
\Foreign{à~priori} synthetic views. But this is no solution
of the difficulty---it is merely giving it a name; and
even if the nature of the synthetic views had no
longer for us any mystery, the contradiction would
not have disappeared; it would have only been
shirked. Syllogistic reasoning remains incapable
of adding anything to the data that are given it;
the data are reduced to axioms, and that is all we
should find in the conclusions.

No theorem can be new unless a new axiom
intervenes in its demonstration; reasoning can
only give us immediately evident truths borrowed
from direct intuition; it would only be an intermediary
parasite. Should we not therefore have
reason for asking if the syllogistic apparatus serves
only to disguise what we have borrowed?

The contradiction will strike us the more if we
open any book on mathematics; on every page the
author announces his intention of generalising some
proposition already known. Does the mathematical
method proceed from the particular to the general,
and, if so, how can it be called deductive?
\PageSep{3}

Finally, if the science of number were merely
analytical, or could be analytically derived from a
few synthetic intuitions, it seems that a sufficiently
powerful mind could with a single glance perceive
all its truths; nay, one might even hope that some
day a language would be invented simple enough
for these truths to be made evident to any person
of ordinary intelligence.

Even if these consequences are challenged, it
must be granted that mathematical reasoning has
of itself a kind of creative virtue, and is therefore to
be distinguished from the syllogism. The difference
must be profound. We shall not, for instance,
find the key to the mystery in the frequent use of
the rule by which the same uniform operation
applied to two equal numbers will give identical
results. All these modes of reasoning, whether or
not reducible to the syllogism, properly so called,
retain the analytical character, and \Foreign{ipso facto}, lose
their power.

\Section{II.}

The argument is an old one. Let us see how
Leibnitz tried to show that two and two make
four. I assume the number one to be defined, and
also the operation~$x + 1$---\ie, the adding of unity
to a given number~$x$. These definitions, whatever
they may be, do not enter into the subsequent
reasoning. I next define the numbers $2$,~$3$,~$4$ by
the equalities\Chg{:---}{}
%[** TN: Numbered eqns displayed in the French, but not in the English transl.]
\[
\Tag{(1)} 1 + 1 = 2;\qquad
\Tag{(2)} 2 + 1 = 3;\qquad
\Tag{(3)} 3 + 1 = 4\Chg{,}{;}
\]
and in
\PageSep{4}
the same way I define the operation~$x + 2$ by the
relation\Chg{;}{}
\[
\Tag{(4)}
x + 2 = (x + 1) + 1.
\]

Given this, we have\Chg{:---}{}
\begin{alignat*}{2}
      2 + 2 &= (2 + 1) + 1\Chg{;}{,}\ &&\text{(def.~4)\Chg{.}{;}} \\
(2 + 1) + 1 &= 3 + 1\Add{,}  &&\text{(def.~2)\Chg{.}{;}} \\
      3 + 1 &= 4\Add{,}      &&\text{(def.~3)\Chg{.}{;}} \\
\text{whence } 2 + 2 &= 4\Add{,}&&\quad\QED
\end{alignat*}

It cannot be denied that this reasoning is purely
analytical. But if we ask a mathematician, he will
reply: ``This is not a demonstration properly so
called; it is a verification.'' We have confined
ourselves to bringing together one or other of two
purely conventional definitions, and we have verified
their identity; nothing new has been learned.
\emph{Verification} differs from proof precisely because it
is analytical, and because it leads to nothing. It
leads to nothing because the conclusion is nothing
but the premisses translated into another language.
A real proof, on the other hand, is fruitful, because
the conclusion is in a sense more general than the
premisses. The equality $2 + 2 = 4$ can be verified
because it is particular. Each individual enunciation
in mathematics may be always verified in
the same way. But if mathematics could be
reduced to a series of such verifications it
would not be a science. A chess-player, for
instance, does not create a science by winning a
piece. There is no science but the science of the
general. It may even be said that the object of
the exact sciences is to dispense with these direct
verifications.
\PageSep{5}

\Section{III.}

Let us now see the geometer at work, and try
%[** TN: "surprise" is correct: "...cherchons à surprendre ses procédés."]
to surprise some of his methods. The task is
not without difficulty; it is not enough to open a
book at random and to analyse any proof we may
come across. First of all, geometry must be excluded,
or the question becomes complicated by
difficult problems relating to the rôle of the
postulates, the nature and the origin of the idea
of space. For analogous reasons we cannot
avail ourselves of the infinitesimal calculus. We
must seek mathematical thought where it has
remained pure---\ie, in Arithmetic. But we
still have to choose; in the higher parts of
the theory of numbers the primitive mathematical
ideas have already undergone so profound
an elaboration that it becomes difficult to analyse
them.

It is therefore at the beginning of Arithmetic
that we must expect to find the explanation we
seek; but it happens that it is precisely in the
proofs of the most elementary theorems that the
authors of classic treatises have displayed the least
precision and rigour. We may not impute this to
them as a crime; they have obeyed a necessity.
Beginners are not prepared for real mathematical
rigour; they would see in it nothing but empty,
tedious subtleties. It would be waste of time to
try to make them more exacting; they have to
pass rapidly and without stopping over the road
\PageSep{6}
which was trodden slowly by the founders of the
science.

Why is so long a preparation necessary to
habituate oneself to this perfect rigour, which
it would seem should naturally be imposed on
all minds? This is a logical and psychological
problem which is well worthy of study. But we
shall not dwell on it; it is foreign to our subject.
All I wish to insist on is, that we shall fail in our
purpose unless we reconstruct the proofs of the
elementary theorems, and give them, not the rough
form in which they are left so as not to weary the
beginner, but the form which will satisfy the skilled
geometer.

\Subsection{Definition of Addition.}

I assume that the operation~$x + 1$ has been
defined; it consists in adding the number~$1$ to a
given number~$x$. Whatever may be said of this
definition, it does not enter into the subsequent
reasoning.

We now have to define the operation~$x + a$, which
consists in adding the number~$a$ to any given
number~$x$. Suppose that we have defined the
operation
%[** TN: Displayed eqns as in the French; all are inline in the English transl.]
\[
x + (a - 1);
\]
the operation~$x + a$ will be
defined by the equality\Chg{:}{}
\[
\Tag{(1)}
x + a = \bigl[x + (a - 1)\bigr] + 1.
\]
We shall know what $x + a$~is when we know what
$x + (a - 1)$ is, and as I have assumed that to start
with we know what $x + 1$~is, we can define
successively and ``by recurrence'' the operations
$x + 2$, $x + 3$,~etc. This definition deserves a moment's
\PageSep{7}
attention; it is of a particular nature which
distinguishes it even at this stage from the purely
logical definition; the equality~(1), in fact, contains
an infinite number of distinct definitions, each
having only one meaning when we know the
meaning of its predecessor.

\Subsection{Properties of Addition.}

\Par{Associative.}---I say that
%[** TN: Displayed eqns as in the French; all are inline in the English transl.]
\[
a + (b + c) = (a + b) + c;
\]
in
fact, the theorem is true for $c = 1$. It may then be
written
\[
a + (b + 1) = (a + b) + 1;
\]
which, remembering
the difference of notation, is nothing but the equality~(1)
by which I have just defined addition. Assume
the theorem true for $c = \gamma$, I say that it will be true for
$c = \gamma + 1$. Let
\[
(a + b) + \gamma = a + (b + \gamma)\Chg{,}{;}
\]
it follows that
\[
\bigl[(a + b) + \gamma\bigr] + 1 = \bigl[a + (b + \gamma)\bigr] + 1;
\]
or by def.~(1)\Chg{---}{,}
\[
(a + b) + (\gamma + 1)
  = a + (b + \gamma + 1)
  = a + \bigl[b + (\gamma + 1)\bigr]\Chg{,}{;}
\]
which shows by a series of purely analytical deductions
that the theorem is true for $\gamma + 1$. Being
true for $c = 1$, we see that it is successively true for
$c = 2$, $c = 3$,~etc.

\Par{Commutative.}---(1)~I say that
%[** TN: Displayed eqns as in the French; all are inline in the English transl.]
\[
a + 1 = 1 + a.
\]
The
theorem is evidently true for $a = 1$; we can \emph{verify}
by purely analytical reasoning that if it is true for
$a = \gamma$ it will be true for $a = \gamma + 1$.\footnote
  {For $(\gamma + 1) + 1 = (1 + \gamma) + 1 = 1 + (\gamma + 1)$.\Transl}
Now, it is true for
$a = 1$, and therefore is true for $a = 2$, $a = 3$, and so
on. This is what is meant by saying that the
proof is demonstrated ``by recurrence.''

(2)~I say that
\[
a + b = b + a.
\]
The theorem has just
\PageSep{8}
been shown to hold good for $b = 1$, and it may be
verified analytically that if it is true for $b = \beta$, it
will be true for $b = \beta + 1$. The proposition is thus
established by recurrence.

\Subsection{Definition of Multiplication.}

We shall define multiplication by the equalities\Chg{:}{}
\begin{gather*}
\Tag{(1)}
a × 1 = a\Chg{.}{;} \\
\Tag{(2)}
a × b = \bigl[a × (b - 1)\bigr] + a.
\end{gather*}
Both of
these include an infinite number of definitions;
having defined~$a × 1$, it enables us to define in
succession $a × 2$, $a × 3$, and so on.

\Subsection{Properties of Multiplication.}

\Par{Distributive.}---I say that
%[** TN: Displayed eqns as in the French; all are inline in the English transl.]
\[
(a + b) × c = (a × c) + (b × c).
\]
We can verify analytically that the theorem
is true for $c = 1$; then if it is true for $c = \gamma$, it will be
true for $c = \gamma + 1$. The proposition is then proved
by recurrence.

\Par{Commutative.}---(1) I say that
\[
a × 1 = 1 × a.
\]
The
theorem is obvious for $a = 1$. We can verify
analytically that if it is true for $a = \alpha$, it will be
true for $a = \alpha + 1$.

(2)~I say that
\[
a × b = b × a.
\]
The theorem has
just been proved for $b = 1$. We can verify analytically
that if it be true for $b = \beta$ it will be true for
$b = \beta + 1$.

\Section{IV.}

This monotonous series of reasonings may now
be laid aside; but their very monotony brings
vividly to light the process, which is uniform,
\PageSep{9}
and is met again at every step. The process is
proof by recurrence. We first show that a
theorem is true for $n = 1$; we then show that if
it is true for~$n - 1$ it is true for~$n$, and we conclude
that it is true for all integers. We have now seen
how it may be used for the proof of the rules of
addition and multiplication---that is to say, for the
rules of the algebraical calculus. This calculus
is an instrument of transformation which lends
itself to many more different combinations than
the simple syllogism; but it is still a purely analytical
instrument, and is incapable of teaching us
anything new. If mathematics had no other instrument,
it would immediately be arrested in its
development; but it has recourse anew to the
same process---\ie, to reasoning by recurrence, and
it can continue its forward march. Then if we
look carefully, we find this mode of reasoning at
every step, either under the simple form which we
have just given to it, or under a more or less modified
form. It is therefore mathematical reasoning
\Foreign{par excellence}, and we must examine it closer.

\Section{V.}

The essential characteristic of reasoning by recurrence
is that it contains, condensed, so to
speak, in a single formula, an infinite number of
syllogisms. We shall see this more clearly if we
enunciate the syllogisms one after another. They
follow one another, if one may use the expression,
in a cascade. The following are the hypothetical
\PageSep{10}
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~$3$;
hence it is true of~$3$, and so on. We see that the
conclusion of each syllogism serves as the minor
of its successor. Further, the majors of all our
syllogisms may be reduced to a single form. If
the theorem is true of~$n - 1$, it is true of~$n$.

We see, then, that in reasoning by recurrence
we confine ourselves to the enunciation of the
minor of the first syllogism, and the general
formula which contains as particular cases all the
majors. This unending series of syllogisms is thus
reduced to a phrase of a few lines.

It is now easy to understand why every particular
consequence of a theorem may, as I have
above explained, be verified by purely analytical
processes. If, instead of proving that our theorem
is true for all numbers, we only wish to show that
it is true for the number~$6$ for instance, it will be
enough to establish the first five syllogisms in our
cascade. We shall require~$9$ if we wish to prove
it for the number~$10$; for a greater number we
shall require more still; but however great the
number may be we shall always reach it, and the
analytical verification will always be possible.
But however far we went we should never reach
the general theorem applicable to all numbers,
which alone is the object of science. To reach
it we should require an infinite number of syllogisms,
and we should have to cross an abyss
\PageSep{11}
which the patience of the analyst, restricted to the
resources of formal logic, will never succeed in
crossing.

I asked at the outset why we cannot conceive of
a mind powerful enough to see at a glance the
whole body of mathematical truth. The answer is
now easy. A chess-player can combine for four or
five moves ahead; but, however extraordinary a
player he may be, he cannot prepare for more than
a finite number of moves. If he applies his faculties
to Arithmetic, he cannot conceive its general
truths by direct intuition alone; to prove even the
smallest theorem he must use reasoning by recurrence,
for that is the only instrument which
enables us to pass from the finite to the infinite.
This instrument is always useful, for it enables us
to leap over as many stages as we wish; it frees
us from the necessity of long, tedious, and
monotonous verifications which would rapidly
become impracticable. Then when we take in
hand the general theorem it becomes indispensable,
for otherwise we should ever be approaching
the analytical verification without ever actually
reaching it. In this domain of Arithmetic we may
think ourselves very far from the infinitesimal
analysis, but the idea of mathematical infinity is
already playing a preponderating part, and without
it there would be no science at all, because there
would be nothing general.
\PageSep{12}

\Section{VI.}

The views upon which reasoning by recurrence
is based may be exhibited in other forms; we may
say, for instance, that in any finite collection of
different integers there is always one which is
smaller than any other. We may readily pass from
one enunciation to another, and thus give ourselves
the illusion of having proved that reasoning
by recurrence is legitimate. But we shall
always be brought to a full stop---we shall always
come to an indemonstrable axiom, which will at
bottom be but the proposition we had to prove
translated into another language. We cannot therefore
escape the conclusion that the rule of reasoning
by recurrence is irreducible to the principle of
contradiction. Nor can the rule come to us from
experiment. Experiment may teach us that the
rule is true for the first ten or the first hundred
numbers, for instance; it will not bring us to the
indefinite series of numbers, but only to a more or
less long, but always limited, portion of the series.

Now, if that were all that is in question, the
principle of contradiction would be sufficient, it
would always enable us to develop as many
syllogisms as we wished. It is only when it is a
question of a single formula to embrace an infinite
number of syllogisms that this principle breaks
down, and there, too, experiment is powerless to
aid. This rule, inaccessible to analytical proof
and to experiment, is the exact type of the \Foreign{à~priori}
\PageSep{13}
synthetic intuition. On the other hand, we
cannot see in it a convention as in the case of the
postulates of geometry.

Why then is this view imposed upon us with
such an irresistible weight of evidence? It is
because it is only the affirmation of the power of
the mind which knows it can conceive of the
indefinite repetition of the same act, when the act
is once possible. The mind has a direct intuition
of this power, and experiment can only be for it an
opportunity of using it, and thereby of becoming
conscious of it.

But it will be said, if the legitimacy of reasoning
by recurrence cannot be established by experiment
alone, is it so with 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 manifest, we say, and it is so on
the same ground that every physical law is true
which is based on a very large but limited number
of observations.

It cannot escape our notice that here is a
striking analogy with the usual processes of
induction. But an essential difference exists.
Induction applied to the physical sciences is
always uncertain, because it is based on the belief
in a general order of the universe, an order
which is external to us. Mathematical induction---\ie,
proof by recurrence---is, on the contrary,
necessarily imposed on us, because it is only the
affirmation of a property of the mind itself.
\PageSep{14}

\Section{VII.}

Mathematicians, as I have said before, always
endeavour to generalise the propositions they have
obtained. To seek no further example, we have
just shown the equality\Chg{,}{}
%[** TN: Displayed eqns as in the French; all are inline in the English transl.]
\[
a + 1 = 1 + a,
\]
and we then
used it to establish the equality\Chg{,}{}
\[
a + b = b + a,
\]
which
is obviously more general. Mathematics may,
therefore, like the other sciences, proceed from the
particular to the general. This is a fact which
might otherwise have appeared incomprehensible
to us at the beginning of this study, but which has
no longer anything mysterious about it, since we
have ascertained the analogies between proof by
recurrence and ordinary induction.

No doubt mathematical recurrent reasoning and
physical inductive reasoning are based on different
foundations, but they move in parallel lines and in
the same direction---namely, from the particular
to the general.

Let us examine the case a little more closely.
To prove the equality
\[
\Tag{(1)}
a + 2 = 2 + a,
\]
we need
only apply the rule
\[
a + 1 = 1 + a\Chg{,}{}
\]
twice, and write
\[
\Tag{(2)}
a + 2 = a + 1 + 1 = 1 + a + 1 = 1 + 1 + a = 2 + a.
\]

The equality thus deduced by purely analytical
means is not, however, a simple particular case. It
is something quite different. We may not therefore
even say in the really analytical and deductive
part of mathematical reasoning that we proceed
from the general to the particular in the
ordinary sense of the words. The two sides of
\PageSep{15}
the equality~(2) are merely more complicated
combinations than the two sides of the equality~(1),
and analysis only serves to separate the elements
which enter into these combinations and to
study their relations.

Mathematicians therefore proceed ``by construction,''
they ``construct'' more complicated combinations.
When they analyse these combinations,
these aggregates, so to speak, into their primitive
elements, they see the relations of the elements
and deduce the relations of the aggregates themselves.
The process is purely analytical, but it is
not a passing from the general to the particular,
for the aggregates obviously cannot be regarded as
more particular than their elements.

Great importance has been rightly attached to
this process of ``construction,'' and some claim
to see in it the necessary and sufficient condition
of the progress of the exact sciences.
Necessary, no doubt, but not sufficient! For a
construction to be useful and not mere waste of
mental effort, for it to serve as a stepping-stone to
higher things, it must first of all possess a kind of
unity enabling us to see something more than the
juxtaposition of its elements. Or more accurately,
there must be some advantage in considering the
construction rather than the elements themselves.
What can this advantage be? Why reason on a
polygon, for instance, which is always decomposable
into triangles, and not on elementary
triangles? It is because there are properties of
\PageSep{16}
polygons of any number of sides, and they can be
immediately applied to any particular kind of
polygon. In most cases it is only after long efforts
that those properties can be discovered, by directly
studying the relations of elementary triangles. If
the quadrilateral is anything more than the juxtaposition
of two triangles, it is because it is of the
polygon type.

A construction only becomes interesting when
it can be placed side by side with other analogous
constructions for forming species of the same
genus. To do this we must necessarily go back
from the particular to the general, ascending one
or more steps. The analytical process ``by
construction'' does not compel us to descend, but
it leaves us at the same level. We can only
ascend by mathematical induction, for from it
alone can we learn something new. Without the
aid of this induction, which in certain respects
differs from, but is as fruitful as, physical induction,
construction would be powerless to create
science.

Let me observe, in conclusion, that this induction
is only possible 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 piece are limited and
do not resemble each other.
\PageSep{17}


\Chapter[Mathematical Magnitude.]{II.}{Mathematical Magnitude and Experiment.}

\First{If} we want to know what the mathematicians
mean by a continuum, it is useless to appeal to
geometry. The geometer is always seeking, more
or less, to represent to himself the figures he is
studying, but his representations are only instruments
to him; he uses space in his geometry just
as he uses chalk; and further, too much importance
must not be attached to accidents which are
often nothing more than the whiteness of the
chalk.

The pure analyst has not to dread this pitfall.
He has disengaged mathematics from all extraneous
elements, and he is in a position to answer
our question:---``Tell me exactly what this continuum
is, about which mathematicians reason.''
Many analysts who reflect on their art have
already done so---M.~Tannery, for instance, in
his \Title{Introduction à la théorie des Fonctions d'une
variable}.

Let us start with the integers. Between any
two consecutive sets, intercalate one or more intermediary
sets, and then between these sets others
\PageSep{18}
again, and so on indefinitely. We thus get an
unlimited number of terms, and these will be the
numbers which we call fractional, rational, or
commensurable. But this is not yet all; between
these terms, which, be it marked, are already
infinite in number, other terms are intercalated,
and these are called irrational or incommensurable.

Before going any further, let me make a preliminary
remark. The continuum thus conceived
is no longer a collection of individuals arranged in
a certain order, infinite in number, it is true, but
external the one to the other. This is not the
ordinary conception in which it is supposed that
between the elements of the continuum exists an
intimate connection making of it one whole, in
which the point has no existence previous to the
line, but the line does exist previous to the point.
Multiplicity alone subsists, unity has disappeared---``the
continuum is unity in multiplicity,'' according
to the celebrated formula. The analysts have
even less reason to define their continuum as they
do, since it is always on this that they reason when
they are particularly proud of their rigour. It
is enough to warn the reader that the real
mathematical continuum is quite different from
that of the physicists and from that of the
metaphysicians.

It may also be said, perhaps, that mathematicians
who are contented with this definition are the
dupes of words, that the nature of each of these
sets should be precisely indicated, that it should
\PageSep{19}
be explained how they are to be intercalated, and
that it should be shown how it is possible to do it.
This, however, would be wrong; the only property
of the sets which comes into the reasoning is that of
preceding or succeeding these or those other sets;
this alone should therefore intervene in the definition.
So we need not concern ourselves with the
manner in which the sets are intercalated, and
no one will doubt the possibility of the operation
if he only remembers that ``possible'' in the
language of geometers simply means exempt from
contradiction. But our definition is not yet complete,
and we come back to it after this rather long
digression.

\Par{Definition of Incommensurables.}---The mathematicians
of the Berlin school, and Kronecker
in particular, have devoted themselves to constructing
this continuous scale of irrational and
fractional numbers without using any other
materials than the integer. The mathematical
continuum from this point of view would be a
pure creation of the mind in which experiment
would have no part.

The idea of rational number not seeming to
present to them any difficulty, they have confined
their attention mainly to defining incommensurable
numbers. But before reproducing their definition
here, I must make an observation that will allay
the astonishment which this will not fail to provoke
in readers who are but little familiar with the
habits of geometers.
\PageSep{20}

Mathematicians do not study objects, but the
relations between objects; to them it is a matter
of indifference if these objects are replaced by
others, provided that the relations do not change.
Matter does not engage their attention, they are
interested by form alone.

If we did not remember it, we could hardly
understand that Kronecker gives the name of
incommensurable number to a simple symbol---that
is to say, something very different from the
idea we think we ought to have of a quantity
which should be measurable and almost tangible.

Let us see now what is Kronecker's definition.
Commensurable numbers may be divided into
classes in an infinite number of ways, subject
to the condition that any number whatever
of the first class is greater than any number
of the second. It may happen that among the
numbers of the first class there is one which is
smaller than all the rest; if, for instance, we
arrange in the first class all the numbers greater
than~$2$, and $2$~itself, and in the second class all the
numbers smaller than~$2$, it is clear that $2$~will be
the smallest of all the numbers of the first class.
The number~$2$ may therefore be chosen as the
symbol of this division.

It may happen, on the contrary, that in the
second class there is one which is greater than all
the rest. This is what takes place, for example,
if the first class comprises all the numbers greater
than~$2$, and if, in the second, are all the numbers
\PageSep{21}
less than~$2$, and $2$~itself. Here again the
number~$2$ might be chosen as the symbol of this
division.

But it may equally well happen that we can find
neither in the first class a number smaller than all
the rest, nor in the second class a number greater
than all the rest. Suppose, for instance, we
place in the first class all the numbers whose
squares are greater than~$2$, and in the second all
the numbers whose squares are smaller than~$2$.
We know that in neither of them is a number whose
square is equal to~$2$. Evidently there will be in
the first class no number which is smaller than all
the rest, for however near the square of a number
may be to~$2$, we can always find a commensurable
whose square is still nearer to~$2$. From
Kronecker's point of view, the incommensurable
number~$\sqrt{2}$ is nothing but the symbol of this
particular method of division of commensurable
numbers; and to each mode of repartition corresponds
in this way a number, commensurable or
not, which serves as a symbol. But to be satisfied
with this would be to forget the origin of these
symbols; it remains to explain how we have been
led to attribute to them a kind of concrete
existence, and on the other hand, does not the
difficulty begin with fractions? Should we have
the notion of these numbers if we did not previously
know a matter which we conceive as infinitely
divisible---\ie, as a continuum?

\Par{The Physical Continuum.}---We are next led to ask
\PageSep{22}
if the idea of the mathematical continuum is not
simply drawn from experiment. If that be so, the
rough data of experiment, which are our sensations,
could be measured. We might, indeed, be tempted
to believe that this is so, for in recent times there
has been an attempt 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 the experiments by which the endeavour
has been made to establish this law, we shall be
led to a diametrically opposite conclusion. It has,
for instance, been observed that a weight~$A$ of $10$~grammes
and a weight~$B$ of $11$~grammes produced
identical sensations, that the weight~$B$ could no
longer be distinguished from a weight~$C$ of $12$~grammes,
but that the weight~$A$ was readily
distinguished from the weight~$C$. Thus the rough
results of the experiments may be expressed by
the following relations\Chg{:}{}
%[** TN: Not displayed in the English translation]
\[
A = B,\qquad B = C,\qquad A < C,
\]
which
may be regarded as the formula of the physical
continuum. But here is an intolerable disagreement
with the law of contradiction, and the
necessity of banishing this disagreement 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
it is experiment that has provided the opportunity.
We cannot believe that two quantities which are
equal to a third are not equal to one another, and
we are thus led to suppose that $A$~is different from~$B$,
\PageSep{23}
and $B$~from~$C$, and that if we have not been
aware of this, it is due to the imperfections of our
senses.

\Par{The Creation of the Mathematical Continuum: First
Stage.}---So far it would suffice, in order to account
for facts, to intercalate between $A$~and~$B$ a small
number of terms which would remain discrete.
What happens now if we have recourse to some
instrument to make up for the weakness of our
senses? If, for example, we use a microscope?
Such terms as $A$~and~$B$, which before were
indistinguishable from one another, appear now
to be distinct: but between $A$~and~$B$, which are
distinct, is intercalated another new term~$D$,
which we can distinguish neither from~$A$ nor from~$B$.
Although we may use the most delicate
methods, the rough results of our experiments
will always present the characters of the physical
continuum with the contradiction which is inherent
in it. We only escape from it by incessantly
intercalating new terms between the terms already
distinguished, and this operation must be pursued
indefinitely. We might conceive that it would be
possible to stop if we could imagine an instrument
powerful enough to decompose the physical continuum
into discrete elements, just as the telescope
resolves the Milky Way into stars. But this we
cannot imagine; it is always with our senses that
we use our instruments; it is with the eye that we
observe the image magnified by the microscope,
and this image must therefore always retain the
\PageSep{24}
characters of visual sensation, and therefore those
of the physical continuum.

Nothing distinguishes a length directly observed
from half that length doubled by the microscope.
The whole is homogeneous to the part; and there
is a fresh contradiction---or rather there would be
one if the number of the terms were supposed
to be finite; it is clear that the part containing
less terms than the whole cannot be similar to the
whole. The contradiction ceases as soon as the
number of terms is regarded as infinite. There is
nothing, for example, to prevent us from regarding
the aggregate of integers as similar to the aggregate
of even numbers, which is however only a part
of it; in fact, to each integer corresponds another
even number which is its double. But it is not
only to escape this contradiction contained in the
empiric data that the mind is led to create the
concept of a continuum formed of an indefinite
number of terms.

Here everything takes place just as in the series
of the integers. We have the faculty of conceiving
that a unit may be added to a collection of units.
Thanks to experiment, we have had the opportunity
of exercising this faculty and are conscious of
it; but from this fact we feel that our power is
unlimited, and that we can count indefinitely,
although we have never had to count more than
a finite number of objects. In the same way, as
soon as we have intercalated terms between two
consecutive terms of a series, we feel that this
\PageSep{25}
operation may be continued without limit, and
that, so to speak, there is no intrinsic reason for
stopping. As an abbreviation, I may give the
name of a mathematical continuum of the first
order to every aggregate of terms formed after the
same law as the scale of commensurable numbers.
If, then, we intercalate new sets according to the
laws of incommensurable numbers, we obtain
what may be called a continuum of the second
order.

\Par{Second Stage.}---We have only taken our first
step. We have explained the origin of continuums
of the first order; we must now see why
this is not sufficient, and why the incommensurable
numbers had to be invented.

If we try to imagine a line, it must have the
characters of the physical continuum---that is to
say, our representation must have a certain
breadth. Two lines will therefore appear to us
under the form of two narrow bands, and if we
are content with this rough image, it is clear
that where two lines cross they must have some
common part. But the pure geometer makes one
further effort; without entirely renouncing the
aid of his senses, he tries to imagine a line without
breadth and a point without size. This he can
do only by imagining a line as the limit towards
which tends a band that is growing thinner and
thinner, and the point as the limit towards which
is tending an area that is growing smaller and
smaller. Our two bands, however narrow they
\PageSep{26}
may be, will always have a common area; the
smaller they are the smaller it will be, and its
limit is what the geometer calls a point. This is
why it is said that the two lines which cross
must have a common point, and this truth seems
intuitive.

But a contradiction would be implied if we
conceived of lines as continuums of the first order---\ie,
the lines traced by the geometer should only
give us points, the co-ordinates of which are
rational numbers. The contradiction would be
manifest if we were, for instance, to assert the
existence of lines and circles. It is clear, in fact,
that if the points whose co-ordinates are commensurable
were alone regarded as real, the
in-circle of a square and the diagonal of the
square would not intersect, since the co-ordinates
of the point of intersection are incommensurable.

Even then we should have only certain incommensurable
numbers, and not all these numbers.

But let us imagine a line divided into two half-rays
(\Foreign{demi-droites}). Each of these half-rays will
appear to our minds as a band of a certain breadth;
these bands will fit close together, because there
must be no interval between them. The common
part will appear to us to be a point which will still
remain as we imagine the bands to become thinner
and thinner, so that we admit as an intuitive truth
that if a line be divided into two half-rays the
common frontier of these half-rays is a point.
Here we recognise the conception of Kronecker,
\PageSep{27}
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.

\Par{Summary.}---To sum up, 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. The only
limit to its power is the necessity of avoiding all
contradiction; but the mind only makes use of it
when experiment gives a reason for it.

In the case with which we are concerned, the
reason is given by the idea of the physical continuum,
drawn from the rough data of the senses.
But this idea leads to a series of contradictions
from each of which in turn we must be freed.
In this way we are forced to imagine a more
and more complicated system of symbols. That
on which we shall dwell is not merely exempt
from internal contradiction,---it was so already at
all the steps we have taken,---but it is no longer in
contradiction with the various propositions which
are called intuitive, and which are derived from
more or less elaborate empirical notions.

\Par{Measurable Magnitude.}---So far we have not
spoken of the measure of magnitudes; we can tell
if any one of them is greater than any other,
but we cannot say that it is two or three times
as large.

So far, I have only considered the order in which
\PageSep{28}
the terms are arranged; but that is not sufficient
for most applications. We must learn how to
compare the interval which separates any two
terms. On this condition alone will the continuum
become measurable, and the operations
of arithmetic be applicable. This can only be
done by the aid of a new and special convention;
and this convention is, that in such a
case the interval between the terms $A$~and~$B$ is
equal to the interval which separates $C$~and~$D$.
For instance, we started with the integers, and
between two consecutive sets we intercalated $n$~intermediary
sets; by convention we now assume
these new sets to be equidistant. This is one
of the ways of defining the addition of two
magnitudes; for if the interval~$AB$ is by definition
equal to the interval~$CD$, the interval~$AD$ will by
definition be the sum of the intervals $AB$~and~$AC$.
This definition is very largely, but not altogether,
arbitrary. It must satisfy certain conditions---the
commutative and associative laws of addition, for
instance; but, provided the definition we choose
satisfies these laws, the choice is indifferent, and
we need not state it precisely.

\Par{Remarks.}---We are now in a position to discuss
several important questions.

(1) Is the creative power of the mind exhausted
by the creation of the mathematical continuum?
The answer is in the negative, and this is shown
in a very striking manner by the work of Du~Bois
Reymond.
\PageSep{29}

We know that mathematicians distinguish
between infinitesimals of different orders, and that
infinitesimals of the second order are infinitely
small, not only absolutely so, 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 here once more we find the
mathematical continuum which has been dealt
with in the preceding pages. Further, there are
infinitesimals which are infinitely small with
reference to those of the first order, and infinitely
large with respect to the order~$1 + \epsilon$, however
small~$\epsilon$ may be. Here, then, are new terms intercalated
in our series; and if I may be permitted to
revert to the terminology used in the preceding
pages, a terminology which is very convenient,
although it has not been consecrated by usage, I
shall say that we have created a kind of continuum
of the third order.

It is an easy matter to go further, but it is idle
to do so, for we would only be imagining symbols
without any possible application, and no one will
dream of doing that. This continuum of the third
order, to which we are led by the consideration of
the different orders of infinitesimals, is in itself
of but little use and hardly worth quoting.
Geometers look on it as a mere curiosity. The
mind only uses its creative faculty when experiment
requires it.

(2) When we are once in possession of the
conception of the mathematical continuum, are
\PageSep{30}
we protected from contradictions analogous to
those which gave it birth? No, and the following
is an instance:---

He is a \Foreign{savant} indeed who will not take it as
evident that every curve has a tangent; and, in
fact, if we think of a curve and a straight line as
two narrow bands, we can always arrange them in
such a way that they have a common part without
intersecting. Suppose now that the breadth of
the bands diminishes indefinitely: the common
part will still remain, and in the limit, so to speak,
the two lines will have a common point, although
they do not intersect---\ie, they will touch. The
geometer who reasons in this way is only doing
what we have done when we proved that two lines
which intersect have a common point, and his
intuition might also seem to be quite legitimate.
But this is not the case. We can show that there
are curves which have no tangent, if we define
such a curve as an analytical continuum of the
second order. No doubt some artifice analogous
to those we have discussed above would enable us
to get rid of this contradiction, but as the latter is
only met with in very exceptional cases, we need
not trouble to do so. Instead of endeavouring to
reconcile intuition and analysis, we are content to
sacrifice one of them, and as analysis must be
flawless, intuition must go to the wall.

\Par{The Physical Continuum of several Dimensions.}---We
have discussed above the physical continuum
as it is derived from the immediate evidence of our
\PageSep{31}
senses---or, if the reader prefers, from the rough
results of Fechner's experiments; I have shown
that these results are summed up in the contradictory
formulæ\Chg{:---}{}
\[
A = B,\qquad B = C,\qquad A < C.
\]

Let us now see how this notion is generalised,
and how from it may be derived the concept of
continuums of several dimensions. Consider any
two aggregates of sensations. We can either
distinguish between them, or we cannot; just as in
Fechner's experiments the weight of $10$~grammes
could be distinguished from the weight of $12$~grammes,
but not from the weight of $11$~grammes.
This is all that is required to construct the continuum
of several dimensions.

Let us call one of these aggregates of sensations
an \emph{element}. It will be in a measure analogous to
the \emph{point} of the mathematicians, but will not be,
however, the same thing. We cannot say that
our element has no size, for we cannot distinguish
it from its immediate neighbours, and it is thus
surrounded by a kind of fog. If the astronomical
comparison may be allowed, our ``elements''
would be like nebulæ, whereas the mathematical
points would be like stars.

If this be 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 cannot be distinguished
from its predecessor. This \emph{linear} series is to the
\emph{line} of the mathematician what the isolated \emph{element}
was to the point.
\PageSep{32}

Before going further, I must explain what is
meant by a \emph{cut}. Let us consider a continuum~$C$,
and remove from it certain of its elements, which
for a moment we shall regard as no longer belonging
to the continuum. We shall call the aggregate
of elements thus removed a \emph{cut}. By means of this
cut, the continuum~$C$ will be \emph{subdivided} into
several distinct continuums; the aggregate of
elements which remain will cease to form a single
continuum. There will then be on~$C$ two elements,
$A$~and~$B$, which we must look upon as
belonging to two distinct continuums; and we see
that this must be so, because it will be impossible
to find a linear series of consecutive elements of~$C$
(each of the elements indistinguishable from the
preceding, the first being~$A$ and the last~$B$), \emph{unless
one of the elements of this series is indistinguishable
from one of the elements of the cut}.

It may happen, on the contrary, that the cut
may not be sufficient to subdivide the continuum~$C$.
To classify the physical continuums, we must
first of all ascertain the nature of the cuts which
must be made in order to subdivide them. If a
physical continuum,~$C$, may be subdivided by a cut
reducing to a finite number of elements, all distinguishable
the one from the other (and therefore
forming neither one continuum nor several continuums),
we shall call~$C$ a continuum \emph{of one
dimension}. If, on the contrary, $C$~can only be subdivided
by cuts which are themselves continuums,
we shall say that $C$~is of several dimensions; if
\PageSep{33}
the cuts are continuums of one dimension, then
we shall say that $C$~has two dimensions; if cuts of
two dimensions are sufficient, we shall say that $C$~is
of three dimensions, and so on. Thus the
notion of the physical continuum of several dimensions
is defined, thanks to the very simple fact,
that two aggregates of sensations may be distinguishable
or indistinguishable.

\Par{The Mathematical Continuum of Several Dimensions.}---The
conception of the mathematical continuum
of $n$~dimensions may be led up to quite naturally
by a process similar to that which we discussed at
the beginning of this chapter. A point of such a
continuum is defined by a system of $n$~distinct
magnitudes which we call its co-ordinates.

The magnitudes need not always be measurable;
there is, for instance, one branch of geometry
independent of the measure of magnitudes, in
which we are only concerned with knowing, for
example, if, on a curve~$ABC$, the point~$B$ is
between the points $A$~and~$C$, and in which it is
immaterial whether the arc~$AB$ is equal to or
twice the arc~$BC$. This branch is called \emph{Analysis
Situs}. It contains quite a large body of doctrine
which has attracted the attention of the greatest
geometers, and from which are derived, one from
another, a whole series of remarkable theorems.
What distinguishes these theorems from those of
ordinary geometry is that they are purely qualitative.
They are still true if the figures are copied
by an unskilful draughtsman, with the result that
\PageSep{34}
the proportions are distorted and the straight lines
replaced by lines which are more or less curved.

As soon as measurement is introduced into the
continuum we have just defined, the continuum
becomes space, and geometry is born. But the
discussion of this is reserved for Part~II.
\PageSep{35}


\Part{II.}{Space.}

\Chapter{III.}{Non-Euclidean Geometries.}

\First{Every} conclusion presumes premisses. These
premisses are either self-evident and need no
demonstration, or can be established only if based
on other propositions; and, as we cannot go back
in this way to infinity, every deductive science,
and geometry in particular, must rest upon a
certain number of indemonstrable axioms. All
treatises of geometry begin therefore with the
enunciation of these axioms. But there is a
distinction to be drawn between them. Some of
these, for example, ``Things which are equal to
the same thing are equal to one another,'' are not
propositions in geometry but propositions in
analysis. I look upon them as analytical \Foreign{à~priori}
intuitions, and they concern me no further. But
I must insist on other axioms which are special
to geometry. Of these most treatises explicitly
enunciate three:---(1)~Only one line can pass
through two points; (2)~a straight line is the
\PageSep{36}
shortest distance between two points; (3)~through
one point only one parallel can be drawn to a
given straight line. Although we generally dispense
with proving the second of these axioms, it
would be possible to deduce it from the other two,
and from those much more numerous axioms
which are implicitly admitted without enunciation,
as I shall explain further on. For a long
time a proof of the third axiom known as Euclid's
postulate was sought in vain. It is impossible to
imagine the efforts that have been spent in pursuit
of this chimera. Finally, at the beginning of the
nineteenth century, and almost simultaneously,
%[** TN: Correct ("Hongrois") in the French edition]
two scientists, a Russian and a \Reword{Bulgarian}{Hungarian}, Lobatschewsky
and Bolyai, showed irrefutably that this
proof is impossible. They have nearly rid us of
inventors of geometries without a postulate, and
ever since the Académic des Sciences receives only
about one or two new demonstrations a year.
But the question was not exhausted, and it was
not long before a great step was taken by the
celebrated memoir of Riemann, entitled: \Title{Ueber
die Hypothesen welche der Geometrie zum Grunde
liegen}. This little work has inspired most of the
recent treatises to which I shall later on refer, and
among which I may mention those of Beltrami
and Helmholtz.

\Par{The Geometry of Lobatschewsky.}---If it were
possible to deduce Euclid's postulate from the
several axioms, it is evident that by rejecting
the postulate and retaining the other axioms we
\PageSep{37}
should be led to contradictory consequences. It
would be, therefore, impossible to found on those
premisses a coherent geometry. Now, this is
precisely what Lobatschewsky has done. He
assumes at the outset that several parallels may
be drawn through a point to a given straight line,
and he retains all the other axioms of Euclid.
From these hypotheses he deduces a series of
theorems between which it is impossible to find
any contradiction, and he constructs a geometry
as impeccable in its logic as Euclidean geometry.
The theorems are very different, however, from
those to which we are accustomed, and at first
will be found a little disconcerting. For instance,
the sum of the angles of a triangle is always less
than two right angles, and the difference between
that sum and two right angles is proportional to
the area of the triangle. It is impossible to construct
a figure similar to a given figure but of
different dimensions. If the circumference of a
circle be divided into $n$~equal parts, and tangents
be drawn at the points of intersection, the $n$~tangents
will form a polygon if the radius of
the circle is small enough, but if the radius is
large enough they will never meet. We need not
multiply these examples. Lobatschewsky's propositions
have no relation to those of Euclid,
but they are none the less logically interconnected.

\Par{Riemann's Geometry.}---Let us imagine to ourselves
a world only peopled with beings of no
thickness, and suppose these ``infinitely flat''
\PageSep{38}
animals are all in one and the same plane, from
which they cannot emerge. Let us further admit
that this world is sufficiently distant from other
worlds to be withdrawn from their influence, and
while we are making these hypotheses it will not
cost us much to endow these beings with reasoning
power, and to believe them capable of making
a geometry. In that case they will certainly
attribute to space only two dimensions. But
now suppose 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, from which they cannot escape.
What kind of a geometry will they construct? In
the first place, it is clear that they will attribute to
space only two dimensions. The straight line to
them will be the shortest distance from one point
on the sphere to another---that is to say, an arc of
a great circle. In a word, their geometry will be
spherical geometry. What they will call space
will be the sphere on which they are confined, and
on which take place all the phenomena with
which they are acquainted. Their space will
therefore be \emph{unbounded}, since on a sphere one may
always walk forward without ever being brought
to a stop, and yet it will be \emph{finite}; the end will
never be found, but the complete tour can be
made. Well, Riemann's geometry is spherical
geometry extended to three dimensions. To construct
it, the German mathematician had first of
all to throw overboard, not only Euclid's postulate
\PageSep{39}
but also the first axiom that \emph{only one line can pass
through two points}. On a sphere, through two
given points, we can \emph{in general} draw only one great
circle which, as we have just seen, would be to
our imaginary beings a straight line. But there
was one exception. If the two given points are
at the ends of a diameter, an infinite number 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 only one
straight line can in general be drawn, but there are
exceptional cases in which through two points
an infinite number of straight lines can be drawn.
So there is a kind of opposition between the
geometries of Riemann and Lobatschewsky. For
instance, 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 Lobatschewsky,
and greater than two right angles in that
of Riemann. The number of parallel lines that
can be drawn through a given point to a given
line is one in Euclid's geometry, none in Riemann's,
and an infinite number in the geometry of Lobatschewsky.
Let us add that Riemann's space is
finite, although unbounded in the sense which we
have above attached to these words.

\Par{Surfaces with Constant Curvature.}---One objection,
however, remains possible. There is no contradiction
between the theorems of Lobatschewsky and
Riemann; but however numerous are the other
consequences that these geometers have deduced
\PageSep{40}
from their hypotheses, they had to arrest their
course before they exhausted them all, for the
number would be infinite; and who can say that
if they had carried their deductions further they
would not have eventually reached some contradiction?
This difficulty does not exist for
Riemann's geometry, provided it is limited to
two dimensions. As we have seen, the two-dimensional
geometry of Riemann, in fact, does
not differ from spherical geometry, which is only a
branch of ordinary geometry, and is therefore outside
all contradiction. Beltrami, by showing that
Lobatschewsky's two-dimensional geometry was
only a branch of ordinary geometry, has equally
refuted the objection as far as it is concerned.
This is the course of his argument: Let us consider
any figure whatever on a surface. Imagine
this figure to be traced on a flexible and inextensible
canvas applied to the surface, in such
a way that when the canvas is displaced and
deformed the different lines of the figure change
their form without changing their length. As a
rule, this flexible and inextensible figure cannot be
displaced without leaving the surface. But there
are certain surfaces for which such a movement
would be possible. They are surfaces of constant
curvature. If we resume the comparison that we
made just now, and imagine beings without thickness
living on one of these surfaces, they will
regard as possible the motion of a figure all the
lines of which remain of a constant length. Such
\PageSep{41}
a movement would appear absurd, on the other
hand, to animals without thickness living on a
surface of variable curvature. These surfaces of
constant curvature are of two kinds. The
curvature of some is \emph{positive}, and they may be
deformed so as to be applied to a sphere. The
geometry of these surfaces is therefore reduced to
spherical geometry---namely, Riemann's. The curvature
of others is \emph{negative}. Beltrami has shown
that the geometry of these surfaces is identical
with that of Lobatschewsky. Thus the two-dimensional
geometries of Riemann and Lobatschewsky
are connected with Euclidean geometry.

\Par{Interpretation of Non-Euclidean Geometries.}---Thus
vanishes the objection so far as two-dimensional
geometries are concerned. It would be easy to
extend Beltrami's reasoning to three-dimensional
geometries, and minds which do not recoil before
space of four dimensions will see no difficulty in
it; but such minds are few in number. I prefer,
then, to proceed otherwise. Let us consider a
certain plane, which I shall call the fundamental
plane, and let us construct a kind of dictionary by
making a double series of terms written in two
columns, and corresponding each to each, just as
in ordinary dictionaries the words in two languages
which have the same signification correspond to
one another:---
\Dict{Space}{\raggedright The portion of space situated
above the fundamental
plane.}
\PageSep{42}
\Dict{Plane}{\raggedright Sphere cutting orthogonally
the fundamental plane.}
\Dict{Line}{\raggedright Circle cutting orthogonally
the fundamental plane.}
\Dict{Sphere}{Sphere.}
\Dict{Circle}{Circle.}
\Dict{Angle}{Angle.}
\Dict{Distance between
two points}{Logarithm of the anharmonic
ratio of these two points
and of the intersection
of the fundamental plane
with the circle passing
through these two points
and cutting it orthogonally.}
\Dict{Etc.}{Etc.}

Let us now take Lobatschewsky's theorems and
translate them by the aid of this dictionary, as we
would translate a German text with the aid of
a German-French dictionary. \emph{We shall then
obtain the theorems of ordinary geometry.} For
instance, Lobatschewsky's theorem: ``The sum of
the angles of a triangle is less than two right
angles,'' may be translated thus: ``If a curvilinear
triangle has for its sides arcs of circles which if
produced 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 Lobatschewsky's
hypotheses are carried, they will never lead to a
\PageSep{43}
contradiction; in fact, if two of Lobatschewsky's
theorems were contradictory, the translations of
these two theorems made by the aid of our
dictionary would be contradictory also. But
these translations are theorems of ordinary
geometry, and no one doubts that ordinary
geometry is exempt from contradiction. Whence
is the certainty derived, and how far is it justified?
That is a question upon which I cannot enter
here, but it is a very interesting question, and I
think not insoluble. Nothing, therefore, is left of
the objection I formulated above. But this is not
all. Lobatschewsky's geometry being susceptible
of a concrete interpretation, ceases to be a useless
logical exercise, and may be applied. I have no
time here to deal with these applications, nor
with what Herr Klein and myself have done by
using them in the integration of linear equations.
Further, this interpretation is not unique, and
several dictionaries may be constructed analogous
to that above, which will enable us by a simple
translation to convert Lobatschewsky's theorems
into the theorems of ordinary geometry.

\Par{Implicit Axioms.}---Are the axioms implicitly
enunciated in our text-books the only foundation
of geometry? We may be assured of the contrary
when we see that, when they are abandoned one
after another, there are still left standing some
propositions which are common to the geometries
of Euclid, Lobatschewsky, and Riemann. These
propositions must be based on premisses that
\PageSep{44}
geometers admit without enunciation. It is interesting
to try and extract them from the classical
proofs.

John Stuart Mill asserted\footnote
  {\Title{Logic}, c.~viii., cf.\ Definitions, §5--6.\Transl}
that every definition
contains an axiom, because by defining we implicitly
affirm the existence of the object defined.
That is going rather too far. It is but rarely in
mathematics that a definition is given without
following it up by the proof of the existence of the
object defined, and when this is not done it is
generally because the reader can easily supply
it; and it must not be forgotten that the word
``existence'' has not the same meaning when it
refers to a mathematical entity as when it refers to
a material object.

A mathematical entity exists provided there is
no contradiction implied in its definition, either in
itself, or with the propositions previously admitted.
But if the observation of John Stuart Mill cannot
be applied to all definitions, it is none the less true
for some of them. A plane is sometimes defined
in the following manner:---The plane is a surface
such that the line which joins any two points
upon it lies wholly on that surface. Now, there is
obviously a new axiom concealed in this definition.
It is true we might change it, and that would be
preferable, but then we should have to enunciate
the axiom explicitly. Other definitions may give
rise to no less important reflections, such as, for
example, that of the equality of two figures. Two
\PageSep{45}
figures are equal when they can be superposed.
To superpose them, one of them must be displaced
until it coincides with the other. But how must
it be displaced? If we asked that question, no
doubt we should be told that it ought to be done
without deforming it, and as an invariable solid is
displaced. The vicious circle would then be evident.
As a matter of fact, this definition defines
nothing. It has no meaning to a being living in a
world in which there are only fluids. If it seems
clear to us, it is because we are accustomed to the
properties of natural solids which do not much
differ from those of the ideal solids, all of whose
dimensions are invariable. However, imperfect as
it may be, this definition implies an axiom. The
possibility of the motion of an invariable figure is
not a self-evident truth. At least it is only so in
the application to Euclid's postulate, and not as an
analytical \Foreign{à~priori} intuition would be. Moreover,
when we study the definitions and the proofs
of geometry, we see that we are compelled to
admit without proof not only the possibility of
this motion, but also some of its properties. This
first arises in the definition of the straight line.
Many defective definitions have been given, but
the true one is that which is understood in all the
proofs in which the straight line intervenes. ``It
may happen that the motion of an invariable figure
may be such that all the points of a line belonging
to the figure are motionless, while all the points
situate outside that line are in motion. Such a
\PageSep{46}
line would be called a straight line.'' We have
deliberately in this enunciation separated the
definition from the axiom which it implies. Many
proofs such as those of the cases of the equality of
triangles, of the possibility of drawing a perpendicular
from a point to a straight line, assume propositions
the enunciations of which are dispensed
with, for they necessarily imply that it is possible
to move a figure in space in a certain way.

\Par{The Fourth Geometry.}---Among these explicit
axioms there is one which seems to me to deserve
some attention, because when we abandon it we
can construct a fourth geometry as coherent as
those of Euclid, Lobatschewsky, and Riemann.
To prove that we can always draw a perpendicular
at a point~$A$ to a straight line~$AB$, we consider a
straight line~$AC$ movable about the point~$A$, and
initially identical with the fixed straight line~$AB$.
We then can make it turn about the point~$A$ until
it lies in~$AB$ produced. Thus we assume two
propositions---first, that such a rotation is possible,
and then that it may continue until the two lines
lie the one in the other produced. If the first
point is conceded and the second rejected, we are
led to a series of theorems even stranger than those
of Lobatschewsky and Riemann, but equally free
from contradiction. I shall give only one of these
theorems, and I shall not choose the least remarkable
of them. \emph{A real straight line may be perpendicular
to itself.}

\Par{Lie's Theorem.}---The number of axioms implicitly
\PageSep{47}
introduced into classical proofs is greater than
necessary, and it would be interesting to reduce
them to a minimum. It may be asked, in the first
place, if this reduction is possible---if the number of
necessary axioms and that of imaginable geometries
is not infinite? A theorem due to Sophus Lie is of
weighty importance in this discussion. It may be
enunciated in the following manner:---Suppose the
following premisses are admitted: (1)~space has $n$~dimensions;
(2)~the movement of an invariable
figure is possible; (3)~$p$~conditions are necessary to
determine the position of this figure in space.

\emph{The number of geometries compatible with these
premisses 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 the movement is
granted, we can only invent a finite and even
a rather restricted number of three-dimensional
geometries.

\Par{Riemann's Geometries.}---However, this result
seems contradicted by Riemann, for that scientist
constructs an infinite number of geometries, and
that to which his name is usually attached is only
a particular case of them. All depends, he says,
on the manner in which the length of a curve is
defined. Now, there is an infinite number 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 movement of a variable figure
such as we assume to be possible in Lie's theorem.
\PageSep{48}
These geometries of Riemann, so interesting on
various grounds, can never be, therefore, purely
analytical, and would not lend themselves to
proofs analogous to those of Euclid.

\Par{On the Nature of Axioms.}---Most mathematicians
regard Lobatschewsky's geometry as a mere logical
curiosity. Some of them have, however, gone
further. If several geometries are possible, they
say, is it certain that our geometry is the one that
is true? Experiment 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 small. According to Lobatschewsky,
the difference is proportional to the area
of the triangle, and will not this become sensible
when we operate on much larger triangles, and
when our measurements become more accurate?
Euclid's geometry would thus be a provisory
geometry. Now, to discuss this view we must
first of all ask ourselves, what is the nature of
geometrical axioms? Are they synthetic \Foreign{à~priori}
intuitions, as Kant affirmed? They would then
be imposed upon us with such a force that we
could not conceive of the contrary proposition, nor
could we build upon it a theoretical edifice. There
would be no non-Euclidean geometry. To convince
ourselves of this, let us take a true synthetic
\Foreign{à~priori} intuition---the following, for instance, which
played an important part 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
\PageSep{49}
true of~$n$, it will be true for all positive integers.
Let us next try to get rid of this, and while rejecting
this proposition let us construct a false
arithmetic analogous to non-Euclidean geometry.
We shall not be able to do it. We shall be even
tempted at the outset to look upon these intuitions
as analytical. Besides, to take up again
our fiction of animals without thickness, we can
scarcely admit that these beings, if their minds
are like ours, would adopt the Euclidean geometry,
which would be contradicted by all their experience.
Ought we, then, to conclude that the
axioms of geometry are experimental truths?
But we do not make experiments on ideal lines or
ideal circles; we can only make them on material
objects. On what, therefore, would experiments
serving as a foundation for geometry be based?
The answer is easy. We have seen above that we
constantly reason as if the geometrical figures
behaved like solids. What geometry would borrow
from experiment would be therefore the properties
of these bodies. The properties of light
and its propagation in a straight line have also
given rise to some of the propositions of geometry,
and in particular to those of projective geometry,
so that from that point of view one would be
tempted to say that metrical geometry is the study
of solids, and projective geometry that of light.
But a difficulty remains, and is unsurmountable.
If geometry were an experimental science, it would
not be an exact science. It would be subjected to
\PageSep{5O}
continual revision. Nay, it would from that day
forth be proved to be erroneous, for we know that
no rigorously invariable solid exists. \emph{The geometrical
axioms are therefore neither synthetic \Foreign{à~priori}
intuitions nor experimental facts.} They are conventions.
Our choice among all possible conventions
is \emph{guided} by experimental facts; but it remains
\emph{free}, and is only limited by the necessity of avoiding
every contradiction, and thus it is that postulates
may remain rigorously true even when the
experimental laws which have determined their
adoption are only approximate. In other words,
\emph{the axioms of geometry} (I do not speak of those of
arithmetic) \emph{are only definitions in disguise}. What,
then, are we to think of the question: Is
Euclidean geometry true? It has no meaning.
We might as well ask if the metric system is true,
and if the old weights and measures are false; if
Cartesian co-ordinates are true and polar co-ordinates
false. One geometry cannot be more
true than another; it can only be more convenient.
Now, Euclidean geometry is, and will remain, the
most convenient: 1st,~because it is the simplest,
and it is not so only because of our mental habits
or because of the kind of direct intuition that we
have of Euclidean space; it is the simplest in
itself, just as a polynomial of the first degree is
simpler than a polynomial of the second degree;
2nd,~because it sufficiently agrees with the properties
of natural solids, those bodies which we
can compare and measure by means of our senses.
\PageSep{51}


\Chapter{IV.}{Space and Geometry.}

\First{Let} us begin with a little paradox. Beings whose
minds were made as ours, and with senses like
ours, but without any preliminary education,
might receive from a suitably-chosen external
world impressions which would lead them to
construct a geometry other than that of Euclid,
and to localise the phenomena of this external
world in a non-Euclidean space, or even in space
of four dimensions. As for us, whose education
has been made by our actual world, if we were
suddenly transported into this new world, we
should have no difficulty in referring phenomena
to our Euclidean space. Perhaps somebody may
appear on the scene some day who will devote his
life to it, and be able to represent to himself the
fourth dimension.

\Par{Geometrical Space and Representative Space.}---It is
often said that the images we form of external
objects are localised in space, and even that they
can only be formed on this condition. It is also
said that this space, which thus serves as a kind of
framework ready prepared for our sensations and
representations, is identical with the space of the
\PageSep{52}
geometers, having all the properties of that space.
To all clear-headed men who think in this way,
the preceding statement might well appear extraordinary;
but it is as well to see if they are not
the victims of some illusion which closer analysis
may be able to dissipate. In the first place, what
are the properties of space properly so called?
I mean of that space which is the object of
geometry, and which I shall call geometrical
space. The following are some of the more
essential:---

1st,~it is continuous; 2nd,~it is infinite; 3rd,~it
is of three dimensions; 4th,~it is homogeneous---that
is to say, all its points are identical one
with another; 5th,~it is isotropic. Compare this
now with the framework of our representations
and sensations, which I may call \emph{representative
space}.

\Par{Visual Space.}---First of all let us consider a
purely visual impression, due to an image formed
on the back of the retina. A cursory analysis shows
us this image as continuous, but as possessing only
two dimensions, which already distinguishes purely
visual from what may be called geometrical space.
On the other hand, the image is enclosed within
a limited framework; and there is a no less
important difference: \emph{this pure visual space is not
homogeneous}. All the points on the retina, apart
from the images which may be formed, do not
play the same rôle. The yellow spot can in no
way be regarded as identical with a point on the
\PageSep{53}
edge of the retina. Not only does the same object
produce on it much brighter impressions, but in
the whole of the \emph{limited} framework the point
which occupies the centre will not appear identical
with a point near one of the edges. Closer
analysis no doubt would show us that this continuity
of visual space and its two dimensions are
but an illusion. It would make visual space even
more different than before from geometrical space,
but we may treat this remark as incidental.

However, sight enables us to appreciate distance,
and therefore to perceive a third dimension.
But every one knows that this perception of the
third dimension reduces to a sense of the effort of
accommodation which must be made, and to a
sense of the convergence of the two eyes, that
must take place in order to perceive an object
distinctly. These are muscular sensations quite
different from the visual sensations which have
given us the concept of the two first dimensions.
The third dimension will therefore not appear to us
as playing the same rôle as the two others. What
may be called \emph{complete visual space} is not therefore
an isotropic space. It has, it is true, exactly
three dimensions; which means that the elements
of our visual sensations (those at least which
concur in forming the concept of extension) will
be completely defined if we know three of them;
or, in mathematical language, they will be functions
of three independent variables. But let us
look at the matter a little closer. The third
\PageSep{54}
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 in harmony; there is between
them a constant relation; or, in mathematical
language, the two variables which measure these
two muscular sensations do not appear to us as
independent. Or, again, to avoid an appeal to
mathematical ideas which are already rather too
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 accompany them
respectively will also be indistinguishable. But
that is, so to speak, an experimental fact. Nothing
prevents us \Foreign{à~priori} from assuming the contrary,
and if the contrary takes place, if these two
muscular sensations both vary independently, we
must take into account one more independent
variable, and complete visual space will appear
to us as a physical continuum of four dimensions.
And so in this there is also a fact of \emph{external}
experiment. Nothing prevents us from assuming
that a being with a mind like ours, with the same
sense-organs as ourselves, may be placed in a world
in which light would only reach him after being
passed through refracting media of complicated
form. The two indications which enable us to
appreciate distances would cease to be connected
by a constant relation. A being educating his
\PageSep{55}
senses in such a world would no doubt attribute
four dimensions to complete visual space.

\Par{Tactile and Motor Space.}---``Tactile space'' is
more complicated still than visual space, and differs
even more widely from geometrical space. It is
useless to repeat for the sense of touch my remarks
on the sense of sight. But outside the data of
sight and touch there are other sensations which
contribute as much and more than they do to the
genesis of the concept of space. They are those
which everybody knows, which accompany all our
movements, and which we usually call muscular
sensations. The corresponding framework constitutes
what may be called \emph{motor space}. Each
muscle gives rise to a special sensation which may
be increased or diminished so that the aggregate
of our muscular sensations will depend upon as
many variables as we have muscles. From this
point of view \emph{motor space would have as many dimensions
as we have muscles}. I know that it is said
that if the muscular sensations contribute to form
the concept of space, it is because we have the
sense of the \emph{direction} of each movement, and that
this is an integral part of the sensation. If this
were so, and if a muscular sense could not be
aroused unless it were accompanied by this geometrical
sense of direction, geometrical space
would certainly be a form imposed upon our
sensitiveness. But I do not see this at all when
I analyse my sensations. What I do see is that
the sensations which correspond to movements in
\PageSep{56}
the same direction are connected in my mind by a
simple \emph{association of ideas}. It is to this association
that what we call the sense of direction is reduced.
We cannot therefore discover this sense 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 very different movements of direction. Moreover,
it is evidently acquired; it is like all
associations of ideas, the result of a \emph{habit}. This
habit itself is the result of a very large number of
\emph{experiments}, and no doubt if the education of our
senses had taken place in a different medium,
where we would have been subjected to different
impressions, then contrary habits would have been
acquired, and our muscular sensations would have
been associated according to other laws.

\Par{Characteristics of Representative Space.}---Thus representative
space in its triple form---visual,
tactile, and motor---differs essentially from geometrical
space. It is neither homogeneous nor
isotropic; we cannot even say that it is of three
dimensions. It is often said that we ``project''
into geometrical space the objects of our external
perception; that we ``localise'' them. Now, has
that any meaning, and if so what is that meaning?
Does it mean that we \emph{represent} to ourselves external
objects in geometrical space? Our representations
are only the reproduction of our sensations;
they cannot therefore be arranged in the
same framework---that is to say, in representative
\PageSep{57}
space. It is also just as impossible for us to represent
to ourselves external objects in geometrical
space, as it is impossible for a painter to paint on
a flat surface objects with their three dimensions.
Representative space is only an image of geometrical
space, an image deformed by a kind of
perspective, and we can only represent to ourselves
objects by making them obey the laws of
this perspective. Thus we do not \emph{represent} to ourselves
external bodies in geometrical space, but we
\emph{reason} about these bodies as if they were situated
in geometrical space. When it is said, on the
other hand, that we ``localise'' such an object in
such a point of space, what does it mean? \emph{It
simply means that we represent to ourselves the movements
that must take place to reach that object.} And
it does not mean that to represent to ourselves
these movements they must be projected into
space, and that the concept of space must therefore
pre-exist. When I say that we represent to ourselves
these movements, I only mean that we
represent to ourselves the muscular sensations
which accompany them, and which have no
geometrical character, and which therefore in no
way imply the pre-existence of the concept of
space.

\Par{Changes of State and Changes of Position.}---But,
it may be said, if the concept of geometrical space
is not imposed upon our minds, and if, on the
other hand, none of our sensations can furnish us
with that concept, how then did it ever come into
\PageSep{58}
existence? This is what we have now to examine,
and it will take some time; but I can sum up in a
few words the attempt at explanation which I am
going to develop. \emph{None of our sensations, if isolated,
could have brought us to the concept of space; we are
brought to it solely by studying the laws by which those
sensations succeed one another.} We see at first that
our impressions are subject to change; but among
the changes that we ascertain, we are very soon
led to make a distinction. Sometimes we say that
the objects, the causes of these impressions, have
changed their state, sometimes that they have
changed their position, that they have only been
displaced. Whether an object changes its state or
only its position, this is always translated for us in
the same manner, \emph{by a modification in an aggregate
of impressions}. How then have we been enabled
to distinguish them? If there were only change
of position, we could restore the primitive aggregate
of impressions by making movements which
would confront us with the movable object in
the same \emph{relative} situation. We thus \emph{correct} the
modification which was produced, and we re-establish
the initial state by an inverse modification.
If, for example, it were a question of the
sight, and if an object be displaced before our
eyes, we can ``follow it with the eye,'' and retain
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
\PageSep{59}
muscular sensations. But that does not mean
that we represent them to ourselves in geometrical
space. So what characterises change of position,
what distinguishes it from change of state, is that
it can always be \emph{corrected} by this means. It may
therefore happen that we pass from the aggregate
of impressions~$A$ to the aggregate~$B$ in two different
ways. First, involuntarily and without experiencing
muscular sensations---which happens
when it is the object that is displaced; secondly,
voluntarily, and with muscular sensation---which
happens when the object is motionless, but when
we displace ourselves in such a way that the
object has relative motion with respect to us. If
this be so, the translation of the aggregate~$A$ to
the aggregate~$B$ is only a change of position. It
follows that sight and touch could not have given
us the idea of space without the help of the
``muscular sense.'' Not only could this concept
not be derived from a single sensation, or even from
\emph{a series of sensations}; but a \emph{motionless} being could
never have acquired it, because, not being able to
correct by his movements the effects of the change
of position of external objects, he would have had
no reason to distinguish them from changes of
state. Nor would he have been able to acquire
it if his movements had not been voluntary,
or if they were unaccompanied by any sensations
whatever.

\Par{Conditions of Compensation.}---How is such a
compensation possible in such a way that two
\PageSep{60}
changes, otherwise mutually independent, may be
reciprocally corrected? A mind \emph{already familiar
with geometry} would reason as follows:---If there
is to be compensation, the different parts of the
external object on the one hand, and the different
organs of our senses on the other, must be in the
same \emph{relative} position after the double change.
And for that to be the case, the different parts of
the external body on the one hand, and the different
organs of our senses on the other, must have
the same relative position to each other after the
double change; and so with the different parts of
our body with respect to each other. In other
words, the external object in the first change must
be displaced as an invariable solid would be displaced,
and it must also be so with the whole of our
body in the second change, which is to correct the
first. Under these conditions compensation may
be produced. But we who as yet know nothing of
geometry, whose ideas of space are not yet formed,
we cannot reason in this way---we cannot predict
\Foreign{à~priori} if compensation is possible. But experiment
shows us that it sometimes does take place,
and we start from this experimental fact in order
to distinguish changes of state from changes of
position.

\Par{Solid Bodies and Geometry.}---Among surrounding
objects there are some which frequently experience
displacements that may be thus corrected by a
\emph{correlative} movement of our own body---namely,
\emph{solid bodies}. The other objects, whose form is variable,
\PageSep{61}
only in exceptional circumstances undergo
similar displacement (change of position without
change of form). When the displacement of a
body takes place with deformation, we can no
longer by appropriate movements place the organs
of our body in the same \emph{relative} situation with
respect to this body; we can no longer, therefore,
reconstruct the primitive aggregate of impressions.

It is only later, and after a series of new experiments,
that we learn how to decompose a body of
variable form into smaller elements such that each
is displaced approximately according to the same
laws as solid bodies. We thus distinguish ``deformations''
from other changes of state. In these
deformations each element undergoes a simple
change of position which may be corrected; but the
modification of the aggregate is more profound,
and can no longer be corrected by a correlative
movement. Such a concept is very complex even
at this stage, and has been relatively slow in
its appearance. It would not have been conceived
at all had not the observation of solid bodies shown
us beforehand how to distinguish changes of
position.

\emph{If, then, there were no solid bodies in nature there
would be no geometry.}

Another remark deserves a moment's attention.
Suppose a solid body to occupy successively the
positions $\alpha$~and~$\beta$; in the first position it will give
us an aggregate of impressions~$A$, and in the second
position the aggregate of impressions~$B$. Now let
\PageSep{62}
there be a second solid body, of qualities entirely
different from the first---of different colour, for
instance. Assume it to pass from the position~$\alpha$,
where it gives us the aggregate of impressions~$A'$ to
the position~$\beta$, where it gives the aggregate of
impressions~$B'$. In general, the aggregate~$A$ will
have nothing in common with the aggregate~$A'$,
nor will the aggregate~$B$ have anything in common
with the aggregate~$B'$. The transition from the
aggregate~$A$ to the aggregate~$B$, and that of the
aggregate~$A'$ to the aggregate~$B'$, are therefore
two changes which \emph{in themselves} have in general
nothing in common. Yet we consider both
these changes as displacements; and, further, we
consider them the \emph{same} displacement. How can
this be? It is simply because they may be both
corrected by the \emph{same} correlative movement of our
body. ``Correlative movement,'' therefore, constitutes
the \emph{sole connection} between two phenomena
which otherwise we should never have dreamed of
connecting.

On the other hand, our body, thanks to the
number of its articulations and muscles, may have
a multitude of different movements, but all are not
capable of ``correcting'' a modification of external
objects; those alone are capable of it in which
our whole body, or at least all those in which
the organs of our senses enter into play are
displaced \Foreign{en bloc}---\ie, without any variation of
their relative positions, as in the case of a solid
body.
\PageSep{63}

To sum up:\Add{---}

1. In the first place, we distinguish two categories
of phenomena:---The first involuntary, unaccompanied
by muscular sensations, and attributed to
external objects---they are external changes; the
second, of opposite character and attributed to the
movements of our own body, are internal changes.

2. We notice that certain changes of each in
these categories may be corrected by a correlative
change of the other category.

3. We distinguish among external changes those
that have a correlative in the other category---which
we call displacements; and in the same way
we distinguish among the internal changes those
which have a correlative in the first category.

Thus by means of this reciprocity is defined a
particular class of phenomena called displacements.
\emph{The laws of these phenomena are the object of
geometry.}

\Par{Law of Homogeneity.}---The first of these laws
is the law of homogeneity. Suppose that by an
external change we pass from the aggregate of
impressions~$A$ to the aggregate~$B$, and that then
this change~$\alpha$ is corrected by a correlative
voluntary movement~$\beta$, so that we are brought
back to the aggregate~$A$. Suppose now that
another external change~$\alpha'$ brings us again from
the aggregate~$A$ to the aggregate~$B$. Experiment
then shows us that this change~$\alpha'$, like the change~$\alpha$,
may be corrected by a voluntary correlative
movement~$\beta'$, and that this movement~$\beta'$ corresponds
\PageSep{64}
to the same muscular sensations as the
movement~$\beta$ which corrected~$\alpha$.

This fact is usually enunciated as follows:---\emph{Space
is homogeneous and isotropic.} We may also say that a
movement which is once produced may be repeated
a second and a third time, and so on, without any
variation of its properties. In the first chapter, in
which we discussed the nature of mathematical
reasoning, we saw the importance that should be
attached to the possibility of repeating the same
operation indefinitely. The virtue of mathematical
reasoning is due to this repetition; by means of the
law of homogeneity geometrical facts are apprehended.
To be complete, to the law of homogeneity
must be added a multitude of other laws,
into the details of which I do not propose to enter,
but which mathematicians sum up by saying that
these displacements form a ``group.''

\Par{The Non-Euclidean World.}---If geometrical space
were a framework imposed on \emph{each} of our representations
considered individually, it would be
impossible to represent to ourselves an image
without this framework, and we should be quite
unable to change our geometry. But this is not
the case; geometry is only the summary of the
laws by which these images succeed each other.
There is nothing, therefore, to prevent us from
imagining a series of representations, similar in
every way to our ordinary representations, but
succeeding one another according to laws which
differ from those to which we are accustomed. We
\PageSep{65}
may thus conceive that beings whose education
has taken place in a medium in which those laws
would be so different, might have a very different
geometry from ours.

Suppose, for example, a world enclosed in a large
sphere and subject to the following laws:---The
temperature is not uniform; it is greatest at the
centre, and gradually decreases as we move towards
the circumference of the sphere, where it is absolute
zero. The law of this temperature is as follows:---If
$R$~be the radius of the sphere, and $r$~the distance
of the point considered from the centre, the absolute
temperature will be proportional to~$R^{2} - r^{2}$.
Further, I shall suppose that in this world all bodies
have the same co-efficient of dilatation, so that the
linear dilatation of any body is proportional to its
absolute temperature. Finally, I shall assume that
a body transported from one point to another of
different temperature is instantaneously in thermal
equilibrium with its new environment. There is
nothing in these hypotheses either contradictory
or unimaginable. A moving object will become
smaller and smaller as it approaches the circumference
of the sphere. Let us observe, in the first
place, that although from the point of view of our
ordinary geometry this world is finite, to its inhabitants
it will appear infinite. As they approach the
surface of the sphere they become colder, and at
the same time smaller and smaller. The steps
they take are therefore also smaller and smaller,
so that they can never reach the boundary of the
\PageSep{66}
sphere. If to us geometry is only the study of the
laws according to which invariable solids move, to
these imaginary beings it will be the study of the
laws of motion of solids \emph{deformed by the differences
of temperature} alluded to.

No doubt, in our world, natural solids also experience
variations of form and volume due to
differences of temperature. But in laying the
foundations of geometry we neglect these variations;
for besides being but small they are irregular,
and consequently appear to us to be accidental.
In our hypothetical world this will no longer be
the case, the variations will obey very simple and
regular laws. On the other hand, the different
solid parts of which the bodies of these inhabitants
are composed will undergo the same variations of
form and volume.

Let me make another hypothesis: suppose that
light passes through media of different refractive
indices, such that the index of refraction is inversely
proportional to~$R^{2} - r^{2}$. Under these conditions it
is clear that the rays of light will no longer be
rectilinear but circular. To justify what has been
said, we have to prove that certain changes in the
position of external objects may be corrected by
correlative movements of the beings which inhabit
this imaginary world; and in such a way as to
restore the primitive aggregate of the impressions
experienced by these sentient beings. Suppose,
for example, that an object is displaced and
deformed, not like an invariable solid, but like a
\PageSep{67}
solid subjected to unequal dilatations in exact conformity
with the law of temperature assumed
above. To use an abbreviation, we shall call such
a movement a non-Euclidean displacement.

If a sentient being be in the neighbourhood of
such a displacement of the object, his impressions
will be modified; but by moving in a suitable
manner, he may reconstruct them. For this
purpose, all that is required is that the aggregate
of the sentient being and the object, considered as
forming a single body, shall experience one of those
special displacements which I have just called non-Euclidean.
This is possible if we suppose that the
limbs of these beings dilate according to the same
laws 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 although their different
parts are no longer in the same relative position,
nevertheless we shall see that the impressions of
the sentient being remain the same as before; in
fact, though the mutual distances of the different
parts have varied, yet the parts which at first were
in contact are still in contact. It follows that
tactile impressions will be unchanged. On the
other hand, from the hypothesis as to refraction
and the curvature of the rays of light, visual impressions
will also be unchanged. These imaginary
beings will therefore be led to classify the phenomena
they observe, and to distinguish among them
the ``changes of position,'' which may be corrected
\PageSep{68}
by a voluntary correlative movement, just as we
do.

If they construct a geometry, it will not be like
ours, which is the study of the movements of our
invariable solids; it will be the study of the
changes of position which they will have thus
distinguished, and will be ``non-Euclidean displacements,''
and \emph{this will be non-Euclidean geometry}.
So that beings like ourselves, educated in
such a world, will not have the same geometry as
ours.

\Par{The World of Four Dimensions.}---Just as we have
pictured to ourselves a non-Euclidean world, so we
may picture a world of four dimensions.

The sense of light, even with one eye, together
with the muscular sensations relative to the movements
of the eyeball, will suffice to enable us to
conceive of space of three dimensions. The images
of external objects are painted on the retina, which
is a plane of two dimensions; these are \emph{perspectives}.
But as eye and objects are movable, we see in
succession different perspectives of the same body
taken from different points of view. We find at
the same time 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 of the
perspective~$A'$ to the perspective~$B'$ are accompanied
by the same muscular sensations, we
connect them as we do other operations of the
same nature. Then when we study the laws
\PageSep{69}
according to which these operations are combined,
we see that they form a group, which has
the same structure as that of the movements of
invariable solids. Now, we have seen that it is
from the properties of this group that we derive
the idea of geometrical space and that of three
dimensions. We thus understand how these
perspectives gave rise to the conception of three
dimensions, although each perspective is of only
two dimensions,---because \emph{they succeed each other
according to certain laws}. Well, in the same way
that we draw the perspective of a three-dimensional
figure on a plane, so we can draw that of a
four-dimensional figure on a canvas of three (or
two) dimensions. To a geometer this is but child's
play. We can even draw several perspectives of
the same figure from several different points of
view. We can easily represent to ourselves these
perspectives, since they are of only three dimensions.
Imagine that the different perspectives of
one and the same object to occur in succession,
and that the transition from one to the other is
accompanied by muscular sensations. It is understood
that we shall consider two of these transitions
as two operations of the same nature when they
are associated with the same muscular sensations.
There is nothing, then, to prevent us from imagining
that these operations are combined according
to any law we choose---for instance, by forming
a group with the same structure as that of the
movements of an invariable four-dimensional solid.
\PageSep{70}
In this there is nothing that we cannot represent
to ourselves, and, moreover, these sensations are
those which a being would experience who has a
retina of two dimensions, and who may be displaced
in space of four dimensions. In this sense
we may say that we can represent to ourselves the
fourth dimension.

\Par{Conclusions.}---It is seen that experiment plays a
considerable rôle in the genesis of geometry; but
it would be a mistake to conclude from that that
geometry is, even in part, an experimental science.
If it were experimental, it would only be approximative
and provisory. And what a rough
approximation it would be! Geometry would be
only the study of the movements of solid bodies;
but, in reality, it is not concerned with natural
solids: its object is certain ideal solids, absolutely
invariable, which are but a greatly simplified and
very remote image of them. The concept of these
ideal bodies is entirely mental, and experiment is
but the opportunity which enables us to reach the
idea. The object of geometry is the study of a
particular ``group''; but the general concept of
group pre-exists in our minds, at least potentially.
It is imposed on us not as a form of our sensitiveness,
but as a form of our understanding; only,
from among all possible groups, we must choose
one that will be the \emph{standard}, so to speak, to
which we shall refer natural phenomena.

Experiment guides us in this choice, which it
does not impose on us. It tells us not what is the
\PageSep{71}
truest, but what is the most convenient geometry.
It will be noticed that my description of these
fantastic worlds has required no language other
than that of ordinary geometry. Then, were we
transported to those worlds, there would be no
need to change that language. Beings educated
there would no doubt find it more convenient to
create a geometry different from ours, and better
adapted to their impressions; but as for us, in the
presence of the same impressions, it is certain that
we should not find it more convenient to make a
change.
\PageSep{72}


\Chapter{V.}{Experiment and Geometry.}

\ParSkip1. I have on several occasions in the preceding
pages tried to show how the principles of geometry
are not experimental facts, and that in particular
Euclid's postulate cannot be proved by experiment.
However convincing the reasons already given
may appear to me, I feel I must dwell upon them,
because there is a profoundly false conception
deeply rooted in many minds.

2. Think of a material circle, measure its radius
and circumference, and see if the ratio of the two
lengths is equal to~$\pi$. What have we done? We
have made an experiment on the properties of the
matter with which this \emph{roundness} has been realised,
and of which the measure we used is made.

\Par[3.\ ]{Geometry and Astronomy.}---The same question
may also be asked in another way. If Lobatschewsky'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 the results which
seem within the reach of experiment, and it is
hoped that astronomical observations may enable
%[** TN: "...les trois géométries" in the French edition]
us to decide between the \Reword{two}{three} geometries. But
\PageSep{73}
what we call a straight line in astronomy is simply
the path of a ray of light. If, therefore, we were
to discover negative parallaxes, or to prove that all
parallaxes are higher than a certain limit, we
should have a choice between two conclusions:
we could give up Euclidean geometry, or modify
the laws of optics, and suppose that light is not
rigorously propagated in a straight line. It is
needless to add that every one would look upon
this solution as the more advantageous. Euclidean
geometry, therefore, has nothing to fear from fresh
experiments.

4. Can we maintain that certain phenomena
which are possible in Euclidean space would be
impossible in non-Euclidean space, so that experiment
in establishing these phenomena would
directly contradict the non-Euclidean hypothesis?
I think that such a question cannot be seriously
asked. To me it is exactly equivalent to the following,
the absurdity of which is obvious:---There
are lengths which can be expressed in metres and
centimetres, but cannot be measured in toises, feet,
and inches; so that experiment, by ascertaining the
existence of these lengths, would directly contradict
this hypothesis, that there are toises divided
into six feet. Let us look at the question a little
more closely. I assume that the straight line in
Euclidean space possesses any two properties,
which I shall call $A$~and~$B$; that in non-Euclidean
space it still possesses the property~$A$, but no
longer possesses the property~$B$; and, finally, I
\PageSep{74}
assume that in both Euclidean and non-Euclidean
space the straight line is the only line that possesses
the property~$A$. If this were so, experiment
would be able to decide between the hypotheses of
Euclid and Lobatschewsky. It would be found
that some concrete object, upon which we can
experiment---for example, a pencil of rays of light---possesses
the property~$A$. We should conclude
that it is rectilinear, and we should then endeavour
to find out if it does, or does not, possess the property~$B$.
But \emph{it is not so}. There exists no
property which can, like this property~$A$, be an
absolute criterion enabling us to recognise the
straight line, and to distinguish it from every
other line. Shall we say, for instance, ``This property
will be the following: the straight line is a
line such that a figure of which this line is a part
can move without the mutual distances of its
points varying, and in such a way that all the
points in this straight line remain fixed''? Now,
this is a property which in either Euclidean or
non-Euclidean space belongs to the straight line,
and belongs to it alone. But how can we ascertain
by experiment if it belongs to any particular
concrete object? Distances must be measured,
and how shall we know that any concrete magnitude
which I have measured with my material
instrument really represents the abstract distance?
We have only removed the difficulty a little farther
off. In reality, the property that I have just
enunciated is not a property of the straight line
\PageSep{75}
alone; it is a property of the straight line and of
distance. For it to serve as an absolute criterion,
we must be able to show, not only that it does not
also belong to any other line than the straight line
and to distance, but also that it does not belong
to any other line than the straight line, and to any
other magnitude than distance. Now, that is not
true, and if we are not convinced by these considerations,
I challenge any one to give me a
concrete experiment which can be interpreted in
the Euclidean system, and which cannot be interpreted
in the system of Lobatschewsky. As I
am well aware that this challenge will never be
accepted, I may conclude that no experiment will
ever be in contradiction with Euclid's postulate;
but, on the other hand, no experiment will ever be
in contradiction with Lobatschewsky's postulate.

5. But it is not sufficient that the Euclidean
(or non-Euclidean) geometry can ever be directly
contradicted by experiment. Nor could it happen
that it can only agree with experiment by a violation
of the principle of sufficient reason, and of
that of the relativity of space. Let me explain
myself. Consider any material system whatever.
We have to consider on the one hand the ``state''
of the various bodies of this system---for example,
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 distinguish the mutual distances
of these bodies that define their relative positions,
\PageSep{76}
and the conditions which define the absolute position
of the system and its absolute orientation in
space. The law of the phenomena which will be
produced in this system will depend on the state
of these bodies, and on their mutual distances;
but because of the relativity and the inertia 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 moment will solely depend on
the state of the same bodies and on their mutual
distances at the initial moment, but will in no
way depend on the absolute initial position of
the system and of its absolute initial orientation.
This is what we shall call, for the sake of
abbreviation, \emph{the law of relativity}.

So far I have spoken as a Euclidean geometer.
But I have said that an experiment, whatever it
may be, requires an interpretation on the Euclidean
hypothesis; it equally requires one on the non-Euclidean
hypothesis. Well, we have made a series
of experiments. We have interpreted them on the
Euclidean hypothesis, and we have recognised
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 experiment interpreted in this new manner
\PageSep{77}
be still in agreement with our ``law of relativity,''
and if this agreement had not taken place, would
we not still have the right to say that experiment
has proved the falsity of non-Euclidean geometry?
It is easy to see that this is an idle fear. In fact,
to apply the law of relativity in all its rigour, it
must be applied to the entire universe; for if we
were to consider only a part of the universe, and
if the absolute position of this part were to vary,
the distances of the other bodies of the universe
would equally vary; their influence on the part of
the universe considered might therefore increase
or diminish, and this might modify the laws of
the phenomena which take place in it. But if
our system is the entire universe, experiment is
powerless to give us any opinion on its position
and its absolute orientation in space. All that
our instruments, however perfect they may be,
can let us know will be the state of the different
parts of the universe, and their mutual distances.
Hence, our law of relativity may be enunciated as
follows:---The readings that we can make with our
instruments at any given moment will depend
only on the readings that we were able to make
on the same instruments at the initial moment.
Now such an enunciation is independent of all
interpretation by experiments. If the law is true
in the Euclidean interpretation, it will be also true
in the non-Euclidean interpretation. Allow me
to make a short digression on this point. I have
spoken above of the data which define the position
\PageSep{78}
of the different bodies of the system. I might also
have spoken of those which define their velocities.
I should then have to distinguish the velocity with
which the mutual distances of the different bodies
are changing, 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 are changing. For the mind
to be fully satisfied, the law of relativity would
have to be enunciated as follows:---The state of
bodies and their mutual distances at any given
moment, as well as the velocities with which
those distances are changing at that moment,
will depend only on the state of those bodies,
on their mutual distances at the initial moment,
and on the velocities with which those distances
were changing at the initial moment. But they
will not depend on the absolute initial position
of the system nor on its absolute orientation, nor
on the velocities with which that absolute position
and orientation were changing at the initial
moment. Unfortunately, the law thus enunciated
does not agree with experiments---at least, as they
are ordinarily interpreted. Suppose a man were
translated to a planet, the sky of which was constantly
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.
But he would notice that it revolves, either by
measuring its ellipticity (which is ordinarily done
by means of astronomical observations, but which
\PageSep{79}
could be done by purely geodesic means), or by
repeating the experiment of Foucault's pendulum.
The absolute rotation of this planet might be
clearly shown in this way. Now, here is a fact
which shocks the philosopher, but which the
physicist is compelled to accept. We know that
from this fact Newton concluded the existence of
absolute space. I myself cannot accept this way
of looking at it. I shall explain why in Part~III.,
but for the moment it is not my intention to
discuss this difficulty. I must therefore 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, the difficulty is the same for
both Euclid's geometry and for Lobatschewsky's.
I need not therefore trouble about it further, and
I have only mentioned it incidentally. 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. They do not and cannot
give us the relations of bodies and space, nor the
mutual relations of the different parts of space.
``Yes!'' you reply, ``a single experiment is not
enough, because it only gives us one equation with
several unknowns; but when I have made enough
experiments I shall have enough equations to
calculate all my unknowns.'' If I know the height
of the main-mast, that is not sufficient to enable
\PageSep{80}
me to calculate the age of the captain. When
you have measured every fragment of wood in a
ship you will have many equations, but you will
be no nearer knowing the captain's age. All your
measurements bearing on your fragments of wood
can tell you only what concerns those fragments;
and similarly, your experiments, however numerous
they may be, referring only to the relations of
bodies with one another, will tell you nothing
about the mutual relations of the different parts
of space.

7. Will you say that if the experiments have
reference to the bodies, they at least have reference
to the geometrical properties of the bodies. First,
what do you understand by the geometrical properties
of bodies? I assume that it is a question
of the relations of the bodies to space. These
properties therefore are not reached by experiments
which only have reference to the relations
of bodies to one another, and that is enough to
show that it is not of those properties that there
can be a question. Let us therefore begin by
making ourselves clear as to the sense of the
phrase: geometrical properties of bodies. When
I say that a body is composed of several parts, I
presume that I am thus enunciating a geometrical
property, and that will be true even if I agree to
give the improper name of points to the very
small parts I am considering. When I say that
this or that part of a certain body is in contact
with this or that part of another body, I am
\PageSep{81}
enunciating a proposition which concerns the
mutual relations of the two bodies, and not their
relations with space. I assume that you will
agree with me that these are not geometrical
properties. I am sure that at least you will
grant that these properties are independent of
all knowledge of metrical geometry. Admitting
this, I suppose that we have a solid body formed
of eight thin iron rods, $oa$, $ob$, $oc$, $od$, $oe$, $of$, $og$, $oh$,
connected at one of their extremities,~$o$. And let
us take a second solid body---for example, a piece
of wood, on which are marked three little spots
of ink which I shall call $\alpha\ \beta\ \gamma$. I now suppose
that we find that we can bring into contact $\Chg{\alpha\ \beta\ \gamma}{\alpha\beta\gamma}$
with~$ago$; by that I mean $\alpha$~with~$a$, and at the
same time $\beta$~with~$g$, and $\gamma$~with~$o$. Then we can
successively bring into contact $\alpha\beta\gamma$ with $bgo$, $cgo$,
$dgo$, $ego$, $fgo$, then with $aho$, $bho$, $cho$, $dho$, $eho$, $fho$;
and then $\alpha\gamma$ successively with $ab$, $bc$, $cd$, $de$, $ef$, $fa$.
Now these are observations that can be made
without having any idea beforehand as to the
form or the metrical properties of space. They
have no reference whatever to the ``geometrical
properties of bodies.'' These observations will
not be possible if the bodies on which we experiment
move in a group having the same structure
as the Lobatschewskian group (I mean according
to the same laws as solid bodies in Lobatschewsky's
geometry). They therefore suffice to prove that
these bodies move according to the Euclidean
group; or at least that they do not move according
\PageSep{82}
to the Lobatschewskian group. That they may
be compatible with the Euclidean group is easily
seen; for we might make them so if the body~$\alpha\beta\gamma$
were an invariable solid of our ordinary
geometry in the shape of a right-angled triangle,
and if the points $abcdefgh$ were the vertices of
a polyhedron formed of two regular hexagonal
pyramids of our ordinary geometry having $abcdef$
as their common base, and having the one~$g$ and
the other~$h$ as their vertices. Suppose now,
instead of the previous observations, we note that
we can as before apply~$\alpha\beta\gamma$ successively to~$ago$,
$bgo$, $cgo$, $dgo$, $ego$, $fgo$, $aho$, $bho$, $cho$, $dho$, $eho$, $fho$,
and then that we can apply~$\alpha\beta$ (and no longer~$\alpha\gamma$)
successively to~$ab$, $bc$, $cd$, $de$, $ef$, and~$fa$. These are
observations that could be made if non-Euclidean
geometry were true. If the bodies~$\alpha\beta\gamma$, $oabcdefgh$
were invariable solids, if the former were a right-angled
triangle, and the latter a double regular
hexagonal pyramid of suitable dimensions. These
new verifications are therefore impossible if the
bodies move according to the Euclidean group;
but they become possible if we suppose the bodies
to move according to the Lobatschewskian group.
They would therefore suffice to show, if we carried
them out, that the bodies in question do not move
according to the Euclidean group. And so, without
making any hypothesis on the form and the
nature of space, on the relations of the bodies
and space, and without attributing to bodies any
geometrical property, I have made observations
\PageSep{83}
which have enabled me to show in one case that
the bodies experimented upon move according to
a group, the structure of which is Euclidean, and
in the other case, that they move in a group, the
structure of which is Lobatschewskian. It cannot
be said that all the first observations would
constitute an experiment proving that space is
Euclidean, and the second an experiment proving
that space is non-Euclidean; in fact, it might be
imagined (note that I use the word \emph{imagined}) that
there are bodies moving in such a manner as
to render possible the second series of observations:
and the proof is that the first mechanic who came
our way could construct it if he would only take
the trouble. But you must not conclude, however,
that space is non-Euclidean. In the same way,
just as ordinary solid bodies would continue
to exist when the mechanic had constructed the
strange bodies I have just mentioned, he would
have to conclude that space is both Euclidean
and non-Euclidean. Suppose, for instance, that
we have a large sphere of radius~$R$, and that its
temperature decreases from the centre to the
surface of the sphere according to the law of
which I spoke when I was describing the non-Euclidean
world. We might have bodies whose
dilatation is \Typo{negligeable}{negligible}, and which would behave
as ordinary invariable solids; and, on the other
hand, we might have very dilatable bodies, which
would behave as non-Euclidean solids. We
might have two double pyramids~$oabcdefgh$ and
\PageSep{84}
$o'a'b'c'd'e'f'g'h'$, and two triangles $\alpha\beta\gamma$~and~$\alpha'\beta'\gamma'$.
The first double pyramid would be rectilinear, and
the second curvilinear. The triangle~$\alpha\beta\gamma$ would
consist of undilatable matter, and the other of very
dilatable matter. We might therefore make our
first observations with the double pyramid~$o'a'h'$
and the triangle~$\alpha'\beta'\gamma'$.

And then the experiment would seem to show---first,
that Euclidean geometry is true, and then
that it is false. Hence, \emph{experiments have reference
not to space but to bodies}.

\Subsection{Supplement.}

\ParSkip8. To round the matter off, I ought to speak of
a very delicate question, which will require considerable
development; but I shall confine myself
to summing up what I have written in the \Title{Revue
de Métaphysique et de Morale} and in the \Title{Monist}.
When we say that space has three dimensions,
what do we mean? We have seen the importance
of these ``internal changes'' which are revealed to
us by our muscular sensations. They may serve
to characterise the different attitudes of our body.
Let us take arbitrarily as our origin one of these
attitudes,~$A$. When we pass from this initial
attitude to another attitude~$B$ we experience a
series of muscular sensations, and this series~$S$ of
muscular sensations will define~$B$. Observe, however,
that we shall often look upon two series $S$~and~$S'$
as defining the same attitude~$B$ (since the
\PageSep{85}
initial and final attitudes $A$~and~$B$ remaining the
same, the intermediary attitudes of the corresponding
sensations may differ). How then can
we recognise the equivalence of these two series?
Because they may serve to compensate for the same
external change, or more generally, because, when
it is a question of compensation for an external
change, one of the series may be replaced by the
other. Among these series we have distinguished
those which can alone compensate for an external
change, and which we have called ``displacements.''
As we cannot distinguish two displacements which
are very close together, the aggregate of these
displacements presents the characteristics of a
physical continuum. Experience teaches us that
they are the characteristics of a physical continuum
of six dimensions; but we do not know as
yet how many dimensions space itself possesses, so
we must first of all answer another question.
What is a point in space? Every one thinks he
knows, but that is an illusion. What we see when
we try to represent to ourselves a point in space is
a black spot on white paper, a spot 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
point which a moment before was occupied by the
object~$A$? Again, what criterion will enable
me to recognise it? I mean that \emph{although I have
not moved} (my muscular sense tells me this), my
finger, which just now touched the object~$A$, is
\PageSep{86}
now touching the object~$B$. I might 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 in the affirmative all
other criteria will give the same answer. I know
it from experiment. I cannot know it \Foreign{à~priori}.
For the same reason I say that touch cannot
be exercised at a distance; that is another way of
enunciating the same experimental fact. If I
say, on the contrary, that sight is exercised at a
distance, it means that the criterion furnished by
sight may give an affirmative answer while the
others reply in the negative.

To sum up. For each attitude of my body my
finger determines a point, and it is that and that
only which defines a point in space. To each
attitude corresponds in this way a point. But it
often happens that the same point corresponds to
several different attitudes (in this case we say that
our finger has not moved, but the rest of our body
has). We distinguish, therefore, among changes
of attitude those in which the finger does not
move. How are we led to this? It is because we
often remark that in these changes the object
which is in touch with the finger remains in contact
with it. Let us arrange then in the same
class all the attitudes which are deduced one from
the other by one of the changes that we have thus
distinguished. To all these attitudes of the same
class will correspond the same point in space.
Then to each class will correspond a point, and to
\PageSep{87}
each point a class. Yet it may be said that what
we get from this experiment is not the point, but
the class of changes, or, better still, the corresponding
class of muscular sensations. Thus, when
we say that space has three dimensions, we merely
mean that the aggregate of these classes appears to
us with the characteristics of a physical continuum
of three dimensions. Then if, instead of defining
the points in space with the aid of the first finger,
I use, for example, another finger, would the
results be the same? That is by no means \Foreign{à~priori}
evident. But, as we have seen, experiment
has shown us that all our criteria are in agreement,
and this enables us to answer in the
affirmative. If we recur to what we have called
displacements, the aggregate of which forms, as
we have seen, a group, we shall be brought to
distinguish those in which a finger does not move;
and by what has preceded, those are the displacements
which characterise a point in space, and
their aggregate will form a sub-group of our
group. To each sub-group of this kind, then, will
correspond a point in space. We might be
tempted to conclude that experiment has taught
us the number of dimensions of space; but in
reality our experiments have referred not to space,
but to our body and its relations with neighbouring
objects. What is more, our experiments
are exceeding crude. In our mind the latent idea
of a certain number of groups pre-existed; these
are the groups with which Lie's theory is concerned.
\PageSep{88}
Which shall we choose to form a kind of
standard by which to compare natural phenomena?
And when this group is chosen, which
of the sub-groups shall we take to characterise a
point in space? Experiment has guided us by
showing us what choice adapts itself best to the
properties of our body; but there its rôle ends.
\PageSep{89}


\Part{III.}{Force.}

\Chapter{VI.}{The Classical Mechanics.}

\First{The} English teach mechanics as an experimental
science; on the Continent it is taught always more
or less as a deductive and \Foreign{à~priori} science. The
English are right, no doubt. How is it that the
other method has been persisted in for so long; how
is it that Continental scientists who have tried to
escape from the practice of their predecessors have
in most cases been unsuccessful? On the other
hand, if the principles of mechanics are only of
experimental origin, are they not merely approximate
and provisory? May we not be some day
compelled by new experiments to modify or even
to abandon them? These are the questions which
naturally arise, and the difficulty of solution is
largely due to the fact that treatises on mechanics
do not clearly distinguish between what is experiment,
what is mathematical reasoning, what is
convention, and what is hypothesis. This is not
all.
\PageSep{90}

1. There is no absolute space, and we only
conceive of relative motion; and yet in most cases
mechanical facts are enunciated as if there is an
absolute space to which they can be referred.

2. There is no absolute time. When we say that
two periods are equal, the statement has no
meaning, and can only acquire a meaning by a
convention.

3. Not only have we no direct intuition of the
equality of two periods, but we have not even
direct intuition of the simultaneity of two events
occurring in two different places. I have explained
this in an article entitled ``Mesure du
Temps.''\footnote
  {\Title{Revue de Métaphysique et de Morale}, t.~vi., pp.~1--13, January,
  1898.}

4. Finally, is not our Euclidean geometry in
itself only a kind of convention of language?
Mechanical facts might be enunciated with reference
to a non-Euclidean space which would be
less convenient but quite as legitimate as our
ordinary space; the enunciation would become
more complicated, but it still would be possible.

Thus, absolute space, absolute time, and even
geometry are not conditions which are imposed on
mechanics. All these things no more existed
before mechanics than the French language can
be logically said to have existed before the truths
which are expressed in French. We might
endeavour to enunciate the fundamental law of
mechanics in a language independent of all these
\PageSep{91}
conventions; and no doubt we should in this way
get a clearer idea of those laws in themselves.
This is what M.~Andrade has tried to do, to
some extent at any rate, in his \Title{Leçons de Mécanique
physique}. Of course the enunciation of these laws
would become much more complicated, because all
these conventions have been adopted for the very
purpose of abbreviating and simplifying the enunciation.
As far as we are concerned, I shall ignore
all these difficulties; not because I disregard
them, far from it; but because they have received
sufficient attention in the first two parts,
of the book. Provisionally, then, we shall admit
absolute time and Euclidean geometry.

\Par{The Principle of Inertia.}---A body under the
action of no force can only move uniformly in a
straight line. Is this a truth imposed on the mind
\Foreign{à~priori}? If this be so, how is it that the Greeks
ignored it? How could they have believed that
motion ceases with the cause of motion? or, again,
that every body, if there is nothing to prevent it,
will move in a circle, the noblest of all forms of
motion?

If it be said that the velocity of a body cannot
change, if there is no reason for it to change, may
we not just as legitimately maintain that the
position of a body cannot change, or that the
curvature of its path cannot change, without the
agency of an external cause? Is, then, the principle
of inertia, which is not an \Foreign{à~priori} truth, an
experimental fact? Have there ever been experiments
\PageSep{92}
on bodies acted on by no forces? and, if so,
how did we know that no forces were acting?
The usual instance is that of a ball rolling for a
very long time on a marble table; but why do
we say it is under the action of no force? Is it
because it is too remote from all other bodies to
experience any sensible action? It is not further
from the earth than if it were thrown freely into
the air; and we all know that in that case it
would be subject 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.
This is very badly expressed; they
evidently mean that various consequences may be
verified by a more general principle, of which the
principle of inertia is only a particular case. I
shall propose for this general principle the
following enunciation:---The acceleration of a
body depends only on its position and that of
neighbouring bodies, and on their velocities.
Mathematicians would say that 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 a
generalisation of the law of inertia we may again
have recourse to our imagination. The law of
inertia, as I have said above, is not imposed on us
\Foreign{à~priori}; other laws would be just as compatible
with the principle of sufficient reason. If a body
is not acted upon by a force, instead of supposing
\PageSep{93}
that its velocity is unchanged we may suppose
that its position or its acceleration is unchanged.

Let us for a moment suppose that one of these
two laws is a law of nature, and substitute it for
the law of inertia: what will be the natural
generalisation? A moment's reflection will show
us. In the first case, we may suppose that the
velocity of a body depends only on its position and
that of neighbouring bodies; in the second case,
that the variation of the acceleration of a body
depends only on the position of the body and of
neighbouring bodies, on their velocities and
accelerations; or, in mathematical terms, the
differential equations of the motion would be of
the first order in the first case and of the third
order in the second.

Let us now modify our supposition a little.
Suppose a world analogous to our solar system,
but one in which by a singular chance the orbits
of all the planets have neither eccentricity nor
inclination; and further, I suppose that the
masses of the planets are too small for their
mutual perturbations to be sensible. Astronomers
living in one of these planets would not hesitate 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 moment would then
be sufficient to determine its velocity and path.
The law of inertia which they would adopt would
be the former of the two hypothetical laws I have
mentioned.
\PageSep{94}

Now, imagine this system to be some day
crossed by a body of vast mass and immense
velocity coming from distant constellations. All
the orbits would be profoundly disturbed. Our
astronomers would not be greatly astonished.
They would guess that this new star is in itself
quite capable of doing all the mischief; but, they
would say, as soon as it has passed by, order will
again be established. No doubt the distances of
the planets from the sun will not be the same as
before the cataclysm, but the orbits will become
circular again as soon as the disturbing cause has
disappeared. It would be only when the perturbing
body is remote, and when the orbits, instead of
being circular are found to be elliptical, that the
astronomers would find out their mistake, and
discover the necessity of reconstructing their
mechanics.

I have dwelt on these hypotheses, for it seems to
me that we can clearly understand our generalised
law of inertia only by opposing it to a contrary
hypothesis.

Has this generalised law of inertia been verified
by experiment, and can it be so verified?
When Newton wrote the \Title{Principia}, he certainly
regarded this truth as experimentally acquired and
demonstrated. It was so in his eyes, not only
from the anthropomorphic conception to which I
shall later refer, but also because of the work of
Galileo. It was so proved by the laws of Kepler.
According to those laws, in fact, the path of a
\PageSep{95}
planet is entirely determined by its initial position
and initial velocity; this, indeed, is what our
generalised law of inertia requires.

For this principle to be only true in appearance---lest
we should fear that some day it must be replaced
by one of the analogous principles which I
opposed to it just now---we must have been led
astray by some amazing chance such as that which
had led into error our imaginary astronomers.
Such an hypothesis is so unlikely that it need not
delay us. No one will believe that there can be
such chances; no doubt the probability that two
eccentricities are both exactly zero is not smaller
than the probability that one is~$0.1$ and the other~$0.2$.
The probability of a simple event is not
smaller than that of a complex one. If, however,
the former does occur, we shall not attribute its
occurrence to chance; we shall not be inclined to
believe that nature has done it deliberately to
deceive us. The hypothesis of an error of this
kind being discarded, we may admit that 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 that some day a new experiment
will falsify the law in some domain of
physics? An experimental law is always subject
to revision; we may always expect to see it replaced
by some other and more exact law. But
no one seriously thinks that the law of which we
speak will ever be abandoned or amended. Why?
\PageSep{96}
Precisely because it will never be submitted to a
decisive test.

In the first place, for this test to be complete,
all the bodies of the universe must return with
their initial velocities to their initial positions after
a certain time. We ought then to find that they
would resume their original paths. But this test
is impossible; it can be only partially applied, and
even when it is applied there will still be some
bodies which will not return to their original
positions. Thus there will be a ready explanation
of any breaking down of the law.

Yet this is not all. In Astronomy we \emph{see} the
bodies whose motion we are studying, and in most
cases we grant that they are not subject to the
action of other invisible bodies. Under these conditions,
our law must certainly be either verified or
not. But it is not so in Physics. If physical
phenomena are due to motion, it is to the motion
of molecules which we cannot see. If, then, the
acceleration of bodies we cannot see depends on
something else than the positions or velocities of
other visible bodies or of invisible molecules, the
existence of which we have been led previously
to admit, there is nothing to prevent us from
supposing that this something else is the position
or velocity of other molecules of which we have
not so far suspected the existence. The law
will be safeguarded. Let me express the same
thought in another form in mathematical language.
Suppose we are observing $n$~molecules, and find
\PageSep{97}
that their $3n$~co-ordinates satisfy a system of $3n$~differential
equations of the fourth order (and
not of the second, as required by the law of
inertia). We know that by introducing $3n$~variable
auxiliaries, a system of $3n$~equations of the fourth
order may be reduced to a system of $6n$~equations
of the second order. If, then, we suppose that the
$3n$~auxiliary variables represent the co-ordinates of
$n$~invisible molecules, the result is again conformable
to the law of inertia. To sum up, this law,
verified experimentally in some particular cases,
may be extended fearlessly to the most general
cases; for we know that in these general cases
it can neither be confirmed nor contradicted by
experiment.

\Par{The Law of Acceleration.}---The acceleration of a
body is equal to the force which acts on it divided
by its mass.

Can this law be verified by experiment? If so,
we have to measure the three magnitudes mentioned
in the enunciation: acceleration, force,
and mass. I admit that acceleration may be
measured, because I pass over the difficulty
arising from the measurement of time. But how
are we to measure force and mass? We do not
even know what they are. What is mass?
Newton replies: ``The product of the volume and
the density.'' ``It were better to say,'' answer
Thomson and Tait, ``that density is the quotient
of the mass by the volume.'' What is force?
``It is,'' replies Lagrange, ``that which moves or
\PageSep{98}
tends to move a body.'' ``It is,'' according to
Kirchoff, ``the product of the mass and the
acceleration.'' Then why not say that mass is
the quotient of the force by the acceleration?
These difficulties are insurmountable.

When we say force is the cause of motion, we
are talking metaphysics; and this definition, if we
had to be content with it, would be absolutely
fruitless, would lead to absolutely nothing. For a
definition to be of any use it must tell us how to
measure force; and that is quite sufficient, for it is
by no means necessary to tell what force is in
itself, nor whether it is the cause or the effect of
motion. We must therefore first define what is
meant by the equality of two forces. When are
two forces equal? We are told that it is when
they give the same acceleration to the same mass,
or when acting in opposite directions they are in
equilibrium. This definition is a sham. A force
applied to a body cannot be uncoupled and
applied to another body as an engine is uncoupled
from one train and coupled to another. It is
therefore impossible to say what acceleration such
a force, applied to such a body, would give to
another body if it were applied to it. It is impossible
to tell how two forces which are not
acting in exactly opposite directions would behave
if they were acting in opposite directions.
It is this definition which we try to materialise, as
it were, when we measure a force with a dynamometer
or with a balance. Two forces, $F$~and~$F'$,
\PageSep{99}
which I suppose, for simplicity, to be acting
vertically upwards, are respectively applied to two
bodies, $C$~and~$C'$. I attach a body weighing~$P$
first to~$C$ and then to~$C'$; if there is equilibrium in
both cases I conclude that the two forces $F$~and~$F'$
are equal, for they are both equal to the weight
of the body~$P$. But am I certain that the body~$P$
has kept its weight when I transferred it from the
first body to the second? Far from it. I am
certain of the contrary. I know that the magnitude
of the weight varies from one point to
another, and that it is greater, for instance, at the
pole than at the equator. No doubt the difference
is very small, and we neglect it in practice; but a
definition must have mathematical rigour; this
rigour does not exist. What I say of weight
would apply equally to the force of the spring of
a dynamometer, which would vary according to
temperature and many other circumstances. Nor
is this all. We cannot say that the weight of the
body~$P$ is applied to the body~$C$ and keeps in
equilibrium the force~$F$. What is applied to
the body~$C$ is the action of the body~$P$ on the
body~$C$. On the other hand, the body~$P$ is
acted on by its weight, and by the reaction~$R$
of the body~$C$ on~$P$ the forces $F$~and~$A$ are
equal, because they are in equilibrium; the forces
$A$~and~$R$ are equal by virtue of the principle
of action and reaction; and finally, the force~$R$
and the weight~$P$ are equal because they
are in equilibrium. From these three equalities
\PageSep{100}
we deduce the equality of the weight~$P$ and the
force~$F$.

Thus we are compelled to bring into our definition
of the equality of two forces the principle
of the equality of action and reaction; \emph{hence this
principle can no longer be regarded as an experimental
law but only as a definition}.

To recognise the equality of two forces we are
then in possession of two rules: the equality of
two forces in equilibrium and the equality of action
and reaction. But, as we have seen, these are not
sufficient, and we are compelled to have recourse
to a third rule, and to admit that certain forces---the
weight of a body, for instance---are constant in
magnitude and direction. But this third rule is
an experimental law. It is only approximately
true: \emph{it is a bad definition}. We are therefore
reduced to Kirchoff's definition: force is the product
of the mass and the acceleration. This law
of Newton in its turn ceases to be regarded as an
experimental law, it is now only a definition. But
as a definition it is insufficient, for we do not
know what mass is. It enables us, no doubt, to
calculate the ratio of two forces applied at
different times to the same body, but it tells us
nothing about the ratio of two forces applied to
two different bodies. To fill up the gap we must
have recourse to Newton's third law, the equality
of action and reaction, still regarded not as
an experimental law but as a definition. Two
bodies, $A$~and~$B$, act on each other; the acceleration
\PageSep{101}
of~$A$, multiplied by the mass of~$A$, is equal to
the action of~$B$ on~$A$; in the same way the
acceleration of~$B$, multiplied by the mass of~$B$ is
equal to the reaction of~$A$ on~$B$. As, by definition,
the action and the reaction are equal, the masses
of $A$~and~$B$ arc respectively in the inverse ratio of
their masses. Thus is the ratio of the two masses
defined, and it is for experiment to verify that the
ratio is constant.

This would do very well if the two bodies were
alone and could be abstracted from the action of
the rest of the world; but this is by no means
the case. The acceleration of~$A$ is not solely due
to the action of~$B$, but to that of a multitude of
other bodies, $C$,~$D$,~\ldots. To apply the preceding
rule we must decompose the acceleration of~$A$ into
many components, and find out which of these
components is due to the action of~$B$. The
decomposition would still be possible if we
suppose that the action of~$C$ on~$A$ is simply added
to that of~$B$ on~$A$, and that the presence of the
body~$C$ does not in any way modify the action of~$B$
on~$A$, or that the presence of~$B$ does not modify
the action of~$C$ on~$A$; that is, if we admit that
any two bodies attract each other, that their
mutual action is along their join, and is only dependent
on their distance apart; if, in a word, we
admit the \emph{hypothesis of central forces}.

We know that to determine the masses of the
heavenly bodies we adopt quite a different principle.
The law of gravitation teaches us that the
\PageSep{102}
attraction of two bodies is proportional to their
masses; if $r$~is their distance apart, $m$~and~$m'$ their
masses, $k$~a constant, then their attraction will be~$kmm'/r^{2}$.
What we are measuring is therefore not
mass, the ratio of the force to the acceleration, but
the attracting mass; not the inertia of the body,
but its attracting power. It is an indirect process,
the use of which is not indispensable theoretically.
We might have said that the attraction is inversely
proportional to the square of the distance,
without being proportional to the product of the
%[** TN: "mais sans que l'on eût f = kmm'"]
masses, that it is equal to~$f/r^{2}$ \Reword{and not to~$kmm'$}{but without having $f = kmm'$}.
If it were so, we should nevertheless, by observing
the \emph{relative} motion of the celestial bodies, be able
to calculate the masses of these bodies.

But have we any right to admit the hypothesis
of central forces? Is this hypothesis rigorously
accurate? Is it certain that it will never be
falsified by experiment? Who will venture to
make such an assertion? And if we must abandon
this hypothesis, the building which has been so
laboriously erected must fall to the ground.

We have no longer any right to speak of the
component of the acceleration of~$A$ which is
due to the action of~$B$. We have no means of
distinguishing it from that which is due to the
action of~$C$ or of any other body. The rule
becomes inapplicable in the measurement of
masses. What then is left of the principle of
the equality of action and reaction? If we
reject the hypothesis of central forces this principle
\PageSep{103}
must go too; the geometrical resultant of
all the forces applied to the different bodies of a
system abstracted from all external action will be
zero. In other words, \emph{the motion of the centre of
gravity of this system will be uniform and in a
straight line}. Here would seem to be a means of
defining mass. The position of the centre of
gravity evidently depends on the values given to
the masses; we must select these values so that
the motion of the centre of gravity is uniform
and rectilinear. This will always be possible if
Newton's third law holds good, and it will be in
general possible only in one way. But no system
exists which is abstracted from all external action;
every part of the universe is subject, more or less,
to the action of the other parts. \emph{The law of the
motion of the centre of gravity is only rigorously true
when applied to the whole universe.}

But then, to obtain the values of the masses
we must find the motion of the centre of gravity
of the universe. The absurdity of this conclusion
is obvious; the motion of the centre of gravity
of the universe will be for ever to us unknown.
Nothing, therefore, is left, and our efforts are
fruitless. There is no escape from the following
definition, which is only a confession of failure:
\emph{Masses are co-efficients which it is found convenient to
introduce into calculations.}

We could reconstruct our mechanics by giving
to our masses different values. The new mechanics
would be in contradiction neither with
\PageSep{104}
experiment nor with the general principles of
dynamics (the principle of inertia, proportionality
of masses and accelerations, equality of
action and reaction, uniform motion of the centre
of gravity in a straight line, and areas). But the
equations of this mechanics \emph{would not be so simple}.
Let us clearly understand this. It would be only
the first terms which would be less simple---\ie,
those we already know through experiment;
perhaps the small masses could be slightly altered
without the \emph{complete} equations gaining or losing
in simplicity.

Hertz has inquired if the principles of mechanics
are rigorously true. ``In the opinion of many
physicists it seems inconceivable that experiment
will ever alter the impregnable principles of
mechanics; and yet, what is due to experiment
may always be rectified by experiment.'' From
what we have just seen these fears would appear
to be groundless. The principles of dynamics
appeared to us first as experimental truths, but
we have been compelled to use them as definitions.
It is \emph{by definition} that force is equal to
the product of the mass and the acceleration;
this is a principle which is henceforth beyond
the reach of any future experiment. Thus
it is by definition that action and reaction are
equal and opposite. But then it will be said,
these unverifiable principles are absolutely devoid
of any significance. They cannot be disproved by
experiment, but we can learn from them nothing
\PageSep{105}
of any use to us; what then is the use of studying
dynamics? This somewhat rapid condemnation
would be rather unfair. There is not in Nature any
system \emph{perfectly} isolated, perfectly abstracted from
all external action; but there are systems which
are \emph{nearly} isolated. If we observe such a system,
we can study not only the relative motion of its
different parts with respect to each other, but the
motion of its centre of gravity with respect to the
other parts of the universe. We then find that
the motion of its centre of gravity is \emph{nearly} uniform
and rectilinear in conformity with Newton's Third
Law. This is an experimental fact, which cannot
be invalidated by a more accurate experiment.
What, in fact, would a more accurate experiment
teach us? It would teach us that the law is only
approximately true, and we know that already.
\emph{Thus is explained how experiment may serve as a basis
for the principles of mechanics, and yet will never
invalidate them.}

\Par{Anthropomorphic Mechanics.}---It will be said that
Kirchoff has only followed the general tendency of
mathematicians towards nominalism; from this his
skill as a physicist has not saved him. He wanted
a definition of a force, and he took the first that
came handy; but we do not require a definition
of force; the idea of force is primitive, irreducible,
indefinable; we all know what it is; of it we have
direct intuition. This direct intuition arises from
the idea of effort which is familiar to us from
childhood. But in the first place, even if this
\PageSep{106}
direct intuition made known to us the real nature
of force in itself, it would prove to be an insufficient
basis for mechanics; it would, moreover, be quite
useless. The important thing is not to know
what force is, but how to measure it. Everything
which does not teach us how to measure it is as
useless to the mechanician as, for instance, the
subjective idea of heat and cold to the student of
heat. This subjective idea cannot be translated
into numbers, and is therefore useless; a scientist
whose skin is an absolutely bad conductor of heat,
and who, therefore, has never felt the sensation
of heat or cold, would read a thermometer in just
the same way as any one else, and would have
enough material to construct the whole of the
theory of heat.

Now this immediate notion of effort is of no use
to us in the measurement of force. It is clear, for
example, that I shall experience more fatigue in
lifting a weight of $100$~lb.\ than a man who is
accustomed to lifting heavy burdens. But there
is more than this. This notion of effort does not
teach us the nature of force; it is definitively reduced
to a recollection of muscular sensations, and
no one will maintain that the sun experiences
a muscular sensation when it attracts the earth.
All that we can expect to find from it is a symbol,
less precise and less convenient than the arrows
(to denote direction) used by geometers, and quite
as remote from reality.

Anthropomorphism plays a considerable historic
\PageSep{107}
rôle in the genesis of mechanics; perhaps it may
yet furnish us with a symbol which some minds
may find convenient; but it can be the foundation
of nothing of a really scientific or philosophical
character.

\Par{The Thread School.}---M.~Andrade, in his \Title{Leçons
de \Typo{Mecanique}{Mécanique} physique}, has modernised anthropomorphic
mechanics. To the school of mechanics
with which Kirchoff is identified, he opposes a
school which is quaintly called the ``Thread
School.''

This school tries to reduce everything to the consideration
of certain material systems of negligible
mass, regarded in a state of tension and capable
of transmitting considerable effort to distant
bodies---systems of which the ideal type is the
fine string, wire, or \emph{thread}. A thread which
transmits any force is slightly lengthened in the
direction of that force; the direction of the thread
tells us the direction of the force, and the magnitude
of the force is measured by the lengthening of
the thread.

%[** TN: "A" variously italicized and not in the original]
{\Loosen We may imagine such an experiment as the
following:}---A body~$A$ is attached to a thread;
at the other extremity of the thread acts a force
which is made to vary until the length of the
thread is increased by~$\alpha$, and the acceleration
of the body~$A$ is recorded. $A$~is then detached,
and a body~$B$ is attached to the same thread, and
the same or another force is made to act until
the increment of length again is~$\alpha$, and the
\PageSep{108}
acceleration of~$B$ is noted. The experiment is
then renewed with both $A$~and~$B$ until the increment
of length is~$\beta$. The four accelerations
observed should be proportional. Here we have
an experimental verification of the law of acceleration
enunciated above. Again, we may consider
a body under the action of several threads in
equal tension, and by experiment we determine
the direction of those threads when the body
is in equilibrium. This is an experimental
verification of the law of the composition of
forces. But, as a matter of fact, what have we
done? We have defined the force acting on the
string by the deformation of the thread, which is
reasonable enough; we have then assumed that if
a body is attached to this thread, the effort which
is transmitted to it by the thread is equal to the
action exercised by the body on the thread; in
fact, we have used the principle of action and
reaction by considering it, not as an experimental
truth, but as the very definition of force. This
definition is quite as conventional as that of
Kirchoff, but it is much less general.

All the forces are not transmitted by the thread
(and to compare them they would all have to be
transmitted by identical threads). If we even
admitted that the earth is attached to the sun by
an invisible thread, at any rate it will be agreed
that we have no means of measuring the increment
of the thread. Nine times out of ten, in consequence,
our definition will be in default; no
\PageSep{109}
sense of any kind can be attached to it, and we
must fall back on that of Kirchoff. Why then go
on in this roundabout way? You admit a certain
definition of force which has a meaning only in
certain particular cases. In those cases you verify
by experiment that it leads to the law of acceleration.
On the strength of these experiments 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 that law, but as verifications of the
principle of action and reaction, or as proving
the deformations of an elastic body depend only
on the forces acting on that body? Without
taking into account the fact that the conditions
in which your definition could be accepted can
only be very imperfectly fulfilled, that a thread is
never without mass, that it is never isolated from
all other forces than the reaction of the bodies
attached to its extremities.

The ideas expounded by M.~Andrade are none
the less very interesting. If they do not satisfy our
logical requirements, they give us a better view of
the historical genesis of the fundamental ideas of
mechanics. The reflections they suggest show us
how the human mind passed from a naïve
anthropomorphism to the present conception of
science.

We see that we end with an experiment which
\PageSep{110}
is very particular, and as a matter of fact very
crude, and we start with a perfectly general law,
perfectly precise, the truth of which we regard as
absolute. We have, so to speak, freely conferred
this certainty on it by looking upon it as a convention.

Are the laws of acceleration and of the composition
of forces only arbitrary conventions?
Conventions, yes; arbitrary, no---they would be
so if we lost sight of the experiments which led the
founders of the science to adopt them, and which,
imperfect as they were, were sufficient to justify
their adoption. It is well from time to time to let
our attention dwell on the experimental origin of
these conventions.
\PageSep{111}


\Chapter{VII.}{Relative and Absolute Motion.}

\Par{The Principle of Relative Motion.}---Sometimes
endeavours have been made to connect the law of
acceleration with a more general principle. The
movement of any system whatever ought to
obey the same laws, whether it is referred to fixed
axes or to the movable axes which are implied
in uniform motion in a straight line. This is
the principle of relative motion; it is imposed
upon us for two reasons: the commonest experiment
confirms it; the consideration of the contrary
hypothesis is singularly repugnant to the mind.

Let us admit it then, and consider a body under
the action of a force. The relative motion of this
body with respect to an observer moving with a
uniform velocity equal to the initial velocity of the
body, should be identical with what would be its
absolute motion if it started from rest. We conclude
that its acceleration must not depend upon
its absolute velocity, and from that we attempt to
deduce the complete law of acceleration.

For a long time there have been traces of this
proof in the regulations for the degree of B.~ès~Sc.
\PageSep{112}
It is clear that the attempt has failed. The
obstacle which prevented us from proving the
law of acceleration is that we have no definition
of force. This obstacle subsists in its entirety,
since the principle invoked has not furnished us
with the missing definition. The principle of
relative motion is none the less very interesting,
and deserves to be considered for its own sake.
Let us try to enunciate it in an accurate manner.
We have said above that the accelerations of the
different bodies which form part of an isolated
system only depend on their velocities and their
relative positions, and not on their velocities and
their absolute positions, provided that the movable
axes to which the relative motion is referred
move uniformly in a straight line; or, if it is preferred,
their accelerations depend only on the
differences of their velocities and the differences of
their co-ordinates, and not on the absolute values
of these velocities and co-ordinates. If this principle
is true for relative accelerations, or rather
for differences of acceleration, by combining it
with the law of reaction we shall deduce that it is
true for absolute accelerations. It remains to be
seen how we can prove that differences of acceleration
depend only on differences of velocities
and co-ordinates; or, to speak in mathematical
language, that these differences of co-ordinates
satisfy differential equations of the second order.
Can this proof be deduced from experiment or
from \Foreign{à~priori} conditions? Remembering what we
\PageSep{113}
have said before, the reader will give his own
answer. Thus enunciated, in fact, the principle of
relative motion curiously resembles what I called
above the generalised principle of inertia; it is not
quite the same thing, since it is a question of
differences of co-ordinates, and not of the co-ordinates
themselves. The new principle teaches
us something more than the old, but the same
discussion applies to it, and would lead to the
same conclusions. We need not recur to it.

\Par{Newton's Argument.}---Here we find a very important
and even slightly disturbing question. I
have said that the principle of relative motion
was not for us simply a result of experiment; and
that \Foreign{à~priori} every contrary hypothesis would be
repugnant to the mind. But, then, why is the
principle only true if the motion of the movable
axes is uniform and in a straight line? It seems
that it should be imposed upon us with the same
force if the motion is accelerated, or at any rate
if it reduces to a uniform rotation. In these two
cases, in fact, the principle is not true. I need not
dwell on the case in which the motion of the
axes is in a straight line and not uniform. The
paradox does not bear a moment's examination.
If I am in a railway carriage, and if the train,
striking against any obstacle whatever, is suddenly
stopped, I shall be projected on to the opposite
side, although I have not been directly acted upon
by any force. There is nothing mysterious in
that, and if I have not been subject to the action
\PageSep{114}
of any external force, the train 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. Nor need I dwell
on the case of relative motion referring to axes
which rotate uniformly. If the sky were for ever
covered with clouds, and if we had no means of
observing the stars, we might, nevertheless, conclude
that the earth turns round. We should be
warned of this fact by the flattening at the poles,
or by the experiment of Foucault's pendulum.
And yet, would there in this case be any meaning
in saying that the earth turns round? If there is
no absolute space, can a thing turn without turning
with respect to something; and, on the other
hand, how can we admit Newton's conclusion and
believe in absolute space? But it is not sufficient
to state that all possible solutions are equally
unpleasant to us. We must analyse in each case
the reason of our dislike, in order to make our
choice with the knowledge of the cause. The
long discussion which follows must, therefore, be
excused.

Let us resume our imaginary story. Thick
clouds hide the stars from men who cannot observe
them, and even are ignorant of their existence.
How will those men know that the earth turns
round? No doubt, for a longer period than did
our ancestors, they will regard the soil on which
they stand as fixed and immovable! They will
\PageSep{115}
wait a much longer time than we did for the
coming of a Copernicus; but this Copernicus will
come at last. How will he come? In the first
place, the mechanical school of this world would
not run their heads against an absolute contradiction.
In the theory of relative motion we observe,
besides real forces, two imaginary forces, which
we call ordinary centrifugal force and compounded
centrifugal force. Our imaginary scientists can
thus explain everything by looking upon these two
forces as real, and they would not see in this a
contradiction of the generalised principle of inertia,
for these forces would depend, the one on the
relative positions of the different parts of the
system, such as real attractions, and the other on
their relative velocities, as in the case of real
frictions. Many difficulties, however, would before
long awaken their attention. If they succeeded in
realising an isolated system, the centre of gravity
of this system would not have an approximately
rectilinear path. They could invoke, to explain
this fact, the centrifugal forces which they would
regard as real, and which, no doubt, they would
attribute to the mutual actions of the bodies---only
they would not see these forces vanish at great
distances---that is to say, in proportion as the
isolation is better realised. Far from it. Centrifugal
force increases indefinitely with distance.
Already this difficulty would seem to them sufficiently
serious, but it would not detain them for
long. They would soon imagine some very subtle
\PageSep{116}
medium analogous to our ether, in which all
bodies would be bathed, and which would exercise
on them a repulsive action. But that is not
all. Space is symmetrical---yet the laws of
motion would present no symmetry. They should
be able to distinguish between right and left.
They would see, for instance, that cyclones always
turn in the same direction, while for reasons of
symmetry they should turn indifferently in any
direction. If our scientists were able by dint of
much hard work to make their universe perfectly
symmetrical, this symmetry would not subsist,
although there is no apparent reason why it
should be disturbed in one direction more than
in another. They would extract this from the
situation no doubt---they would invent something
which would not be more extraordinary than the
glass spheres of Ptolemy, and would thus go on
accumulating complications until the long-expected
Copernicus would sweep them all away
with a single blow, saying it is much more simple
to admit that the earth turns round. Just as
our Copernicus said to us: ``It is more convenient
to suppose that the earth turns round, because the
laws of astronomy are thus expressed in a more
simple language,'' so he would say to them: ``It
is more convenient to suppose that the earth turns
round, because the laws of mechanics are thus
expressed in much more simple language.\Add{''} That
does not prevent absolute space---that is to say,
the point to which we must refer the earth to
\PageSep{117}
know if it really does turn round---from having
no objective existence. And hence this affirmation:
``the earth turns round,'' has no meaning,
since it cannot be verified by experiment; since
such an experiment not only cannot be realised or
even dreamed of by the most daring Jules Verne,
but cannot even be conceived of without contradiction;
or, in other words, these two propositions,
``the earth turns round,'' and, ``it is more
convenient to suppose that the earth turns round,''
have one and the same meaning. There is nothing
more in one than in the other. Perhaps they will
not be content with this, and may find it surprising
that among all the hypotheses, or rather all
the conventions, that can be made on this subject
there is one which is more convenient than the
rest? But if we have admitted it without difficulty
when it is a question of the laws of
astronomy, why should we object when it is a
question of the laws of mechanics? We have
seen that the co-ordinates of bodies are determined
by differential equations of the second
order, and that so are the differences of these
co-ordinates. This is what we have called the
generalised principle of inertia, and the principle
of relative motion. If the distances of these
bodies were determined in the same way by
equations of the second order, it seems that the
mind should be entirely satisfied. How far does
the mind receive this satisfaction, and why is it
not content with it? To explain this we had
\PageSep{118}
better take a simple example. I assume a system
analogous to our solar system, but in which fixed
stars foreign to this system cannot be perceived,
so that astronomers can only observe the mutual
distances of 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, outside Newton's law, we knew the
initial values of these distances and of their derivatives
with respect to time---that would not be
sufficient to determine the values of these same
distances at an ulterior moment. A datum would
be still lacking, and this datum might be, for
example, what astronomers call the area-constant.
But here we may look at it from two different
points of view. We may consider two kinds of
constants. In the eyes of the physicist the world
reduces to a series of phenomena depending, on the
one hand, solely on initial phenomena, and, on the
other hand, on the laws connecting consequence
and antecedent. If observation then teaches us
that a certain quantity is a constant, we shall have
a choice of two ways of looking at it. So let us
admit that there is a law which requires that this
quantity shall not vary, but that by chance it has
been found to have had in the beginning of time
this value rather than that, a value that it has
kept ever since. This quantity might then be
called an \emph{accidental} constant. Or again, let us
\PageSep{119}
admit on the contrary that there is a law of nature
which imposes on this quantity this value and not
that. We shall then have what may be called an
\emph{essential} constant. For example, in virtue of the
laws of Newton the duration of the revolution of
the earth must be constant. But if it is $366$~and
something sidereal days, and not $300$~or~$400$, it is
because of some initial chance or other. It is an
\emph{accidental} constant. If, on the other hand, the
exponent of the distance which figures in the
expression of the attractive force is equal to~$-2$
and not to~$-3$, it is not by chance, but because it
is required by Newton's law. It is an \emph{essential}
constant. I do not know if this manner of giving
to chance its share is legitimate in itself, and if
there is not some artificiality about this distinction;
but it is certain at least that in proportion
as Nature has secrets, she will be strictly arbitrary
and always uncertain in their application. As far
as the area-constant is concerned, we are accustomed
to look upon it as accidental. Is it certain
that our imaginary astronomers would do the
same? If they were able to compare two different
solar systems, they would get the idea that this
constant may assume several different values. But
I supposed at the outset, as I was entitled to do,
that their system would appear isolated, and that
they would see no star which was foreign to their
system. Under these conditions they could only
detect a single constant, which would have an
absolutely invariable, unique value. They would
\PageSep{120}
be led no doubt to look upon it as an essential
constant.

One word in passing to forestall an objection.
The inhabitants of this imaginary world could
neither observe nor define the area-constant as we
do, because absolute longitudes escape their notice;
but that would not prevent them from being
rapidly led to remark a certain constant which
would be naturally introduced into their equations,
and which would be nothing but what we call the
area-constant. But then what would happen?
If the area-constant is regarded as essential, as
dependent upon a law of nature, then in order to
calculate the distances of the planets at any given
moment it would be sufficient to know the initial
values of these distances and those of their first
derivatives. From this new point of view, distances
will be determined by differential equations
of the second order. Would this completely
satisfy the minds of these astronomers? I think
not. In the first place, they would very soon see
that in differentiating their equations so as to
raise them to a higher order, these equations
would become much more simple, and they would
be especially struck by the difficulty which arises
from symmetry. They would have to admit
different laws, according as the aggregate of the
planets presented the figure of a certain polyhedron
or rather of a regular polyhedron, and these consequences
can only be escaped by regarding the area-constant
as accidental. I have taken this particular
\PageSep{121}
example, because I have imagined astronomers
who would not be in the least concerned with
terrestrial mechanics and whose vision would be
bounded by the solar system. But our conclusions
apply in all cases. Our universe is more
extended than theirs, since we have fixed stars;
but it, too, is very limited, so we might reason on
the whole of our universe just as these astronomers
do on their solar system. We thus see that we
should be definitively led to conclude that the
equations which define distances are of an order
higher than the second. Why should this alarm
us---why do we find it perfectly natural that the
sequence of phenomena depends on 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? It can
only be because of mental habits created in us by
the constant study of the generalised principle of
inertia and of its consequences. The values of the
distances at any given moment depend upon their
initial values, on that of their first derivatives, and
something else. What is that \emph{something else}? If
we do not want it to be merely one of the second
derivatives, we have only the choice of hypotheses.
Suppose, as is usually done, that this something
else is the absolute orientation of the universe in
space, or the rapidity with which this orientation
varies; this may be, it certainly is, the most convenient
solution for the geometer. But it is not
the most satisfactory for the philosopher, because
\PageSep{122}
this orientation does not exist. We may assume
that this something else is the position or the
velocity of some invisible body, and this is what is
done by certain persons, who have even called the
body Alpha, although we are destined to never
know anything about this body except its name.
This is an artifice entirely analogous to that of
which I spoke at the end of the paragraph containing
my reflections on the principle of inertia.
But as a matter of fact the difficulty is artificial.
Provided that the future indications of our instruments
can only depend on the indications which
they have given us, or that they might have
formerly given us, such is all we want, and with
these conditions we may rest satisfied.
\PageSep{123}


\Chapter{VIII.}{Energy and Thermo-dynamics.}

\Par{Energetics.}---The difficulties raised by the classical
mechanics have led certain minds to prefer a
new system which they call Energetics. Energetics
took its rise in consequence of the discovery of the
principle of the conservation of energy. Helmholtz
gave it its definite form. We begin by defining
two quantities which play a fundamental
part in this theory. They are \emph{kinetic energy}, or
\Foreign{vis~viva}, and \emph{potential energy}. Every change
that the bodies of nature can undergo is regulated
by two experimental laws. First, the sum of the
kinetic and potential energies is constant. This
is the principle of the conservation of energy.
Second, if a system of bodies is at~$A$ at the time~$t_{0}$,
and at~$B$ at the time~$t_{1}$, it always passes from the
first position to the second by such a path that
the \emph{mean} value of the difference between the two
kinds of energy in the interval of time which
separates the two epochs $t_{0}$~and~$t_{1}$ is a minimum.
This is Hamilton's principle, and is one of the
forms of the principle of least action. The
energetic theory has the following advantages
\PageSep{124}
over the classical. First, it is less incomplete---that
is to say, the principles of the conservation of
energy and of Hamilton teach us more than the
fundamental principles of the classical theory, and
exclude certain motions which do not occur in
nature and which would be compatible with the
classical theory. Second, it frees us from the
hypothesis of atoms, which it was almost impossible
to avoid with the classical theory. But in
its turn it raises fresh difficulties. The definitions
of the two kinds of energy would raise difficulties
almost as great as those of force and mass in the
first system. However, we can get out of these
difficulties more easily, at any rate in the simplest
cases. Assume an isolated system formed of a
certain number of material points. Assume that
these points are acted upon by forces depending
only on their relative position and their distances
apart, and independent of their velocities.
In virtue of the principle of the conservation of
energy there must be a function of forces. In this
simple case the enunciation of the principle of the
conservation of energy is of extreme simplicity.
A certain quantity, which may be determined by
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 squares of these velocities. This
decomposition can only take place in one way.
The first of these terms, which I shall call~$U$, will
\PageSep{125}
be potential energy; the second, which I shall call~$T$,
will be kinetic energy. It is true that if $T + U$
is constant, so is any function of~$T + U$, $\phi(T + U)$.
But this function $\phi(T + U)$ will not be the sum of
two terms, the one independent of the velocities,
and the other proportional to the square of the
velocities. Among the functions which remain
constant there is only one which enjoys this property.
It is~$T + U$ (or a linear function of~$T + U$\Typo{)}{},
it matters not which, since this linear function may
always be reduced to~$T + U$ by a change of unit
and of origin\Typo{}{)}. This, then, is what we call energy.
The first term we shall call potential energy, and
the second kinetic energy. The definition of the
two kinds of energy may therefore be carried
through without any ambiguity.

So it is with the definition of mass. Kinetic
energy, or \Foreign{vis~viva}, is expressed very simply by the
aid of the masses, and of the relative velocities of all
the material points with reference to one of them.
These relative velocities may be observed, and
when we have the expression of the kinetic energy
as a function of these relative velocities, the co-efficients
of this expression will give us the masses.
So in this simple case the fundamental ideas can
be defined without difficulty. But the difficulties
reappear in the more complicated cases if the
forces, instead of depending solely 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
\PageSep{126}
distance but on their velocity and on their acceleration.
If material points attracted each other
according to an analogous law, $U$~would depend
on the velocity, and it might contain a term
proportional to the square of the velocity. How
can we detect among such terms those that arise
from $T$~or~$U$? and how, therefore, can we distinguish
the two parts of the energy? But there
is more than this. How can we define energy
itself? We have no more reason to take as our
definition $T + U$ rather than any other function of~$T + U$,
when the property which characterised
$T + U$ has disappeared---namely, that of being the
sum of two terms of a particular form. But that
is not all. We must take account, not only of
mechanical energy properly so called, but of the
other forms of energy---heat, chemical energy,
electrical energy,~etc. The principle of the conservation
of energy must be written $T + U + Q =$
a constant, where $T$~is 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, chemical, or
electrical form. This would be all right if the
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 depending only on
their internal state. The expression for the energy
could be decomposed in one way only into three
\PageSep{127}
terms of this form. But this is not the case. Let
us consider electrified bodies. The electro-static
energy due to their mutual action will evidently
depend on their charge---\ie, on their state;
but it will equally depend on their position.
If these bodies are in motion, they will act
electro-dynamically on one another, and the
electro-dynamic energy will depend not only on
their state and their position but on their velocities.
We have therefore no means of making the selection
of the terms which should form part of~$T$,
and~$U$, and~$Q$, and of separating the three parts of
the energy. If $T + U + Q$ is constant, the same is
true of any function whatever, $\phi(T + U + Q)$.

If $T + U + Q$ were of the particular form that I
have suggested above, no ambiguity would ensue.
Among the functions $\phi(T + U + Q)$ which remain
constant, there is only one that would be of this
particular form, namely the one which I would
agree to call energy. But I have said this is not
rigorously the case. Among the functions that
remain constant there is not one which can
rigorously be placed in this particular form. How
then can we choose from among them that which
should be called energy? We have no longer
any guide in our choice.

Of the principle of the conservation of energy
there is nothing left then but an enunciation:---\emph{There
is something which remains constant.} In this
form it, in its turn, is outside the bounds of experiment
and reduced to a kind of tautology. It
\PageSep{128}
is clear that if the world is governed by laws
there will be quantities which remain constant.
Like Newton's laws, and for an analogous reason,
the principle of the conservation of energy being
based on experiment, can no longer be invalidated
by it.

This discussion shows that, in passing from the
classical system to the energetic, an advance has
been made; but it shows, at the same time, that
we have not advanced far enough.

Another objection seems to be still more serious.
The principle of least action is applicable to reversible
phenomena, but it is by no means satisfactory
as far as irreversible phenomena are concerned.
Helmholtz attempted to extend it to this class
of phenomena, but he did not and could not
succeed. So far as this is concerned all has yet to
be done. The very enunciation of the principle of
least action is objectionable. To move from one
point to another, a material molecule, acted upon
by no force, but compelled to move on a surface,
will take as its path the geodesic line---\ie, the
shortest path. This molecule seems to know the
point to which we want to take it, to foresee
the time that it will take it to reach it by such
a path, and then to know how to choose the most
convenient path. The enunciation of the principle
presents it to us, so to speak, as a living
and free entity. It is clear that it would be better
to replace it by a less objectionable enunciation,
one in which, as philosophers would say, final
\PageSep{129}
effects do not seem to be substituted for acting
causes.

\Par{Thermo-dynamics.}---The rôle of the two fundamental
principles of thermo-dynamics becomes
daily more important in all branches of natural
philosophy. Abandoning the ambitious theories
of forty years ago, encumbered as they were with
molecular hypotheses, we now try to rest on
thermo-dynamics alone the entire edifice of
mathematical physics. Will the two principles
of Mayer and of Clausius assure to it foundations
solid enough to last for some time? We
all feel it, but whence does our confidence
arise? An eminent physicist said to me one day,
\Foreign{àpropos} of the law of errors:---every one stoutly
believes it, because mathematicians imagine that
it is an effect of observation, and observers imagine
that it is a mathematical theorem. And this was
for a long time the case with the principle of the
conservation of energy. It is no longer the same
now. There is no one who does not know that it
is an experimental fact. But then who gives us
the right of attributing to the principle itself more
generality and more precision than to the experiments
which have served to demonstrate it? This
is asking, if it is legitimate to generalise, as we do
every day, empiric data, and I shall not be so
foolhardy as to discuss this question, after so many
philosophers have vainly tried to solve it. One
thing alone is certain. If this permission were
refused to us, science could not exist; or at least
\PageSep{130}
would be reduced to a kind of inventory, to the
ascertaining of isolated facts. It would not longer
be to us of any value, since it could not satisfy our
need of order and harmony, and because it would
be at the same time incapable of prediction. As
the circumstances which have preceded any fact
whatever will never again, in all probability, be
simultaneously reproduced, we already require a
first generalisation to predict whether the fact will
be renewed as soon as the least of these circumstances
is changed. But every proposition may
be generalised in an infinite number of ways.
Among all possible generalisations we must
choose, and we cannot but choose the simplest.
We are therefore led to adopt the same course
as if a simple law were, other things being equal,
more probable than a complex law. A century
ago it was frankly confessed and proclaimed
abroad that Nature loves simplicity; but Nature
has proved the contrary since then on more than
one occasion. We no longer confess this tendency,
and we only keep of it what is indispensable, so
that science may not become impossible. In
formulating a general, simple, and formal law,
based on a comparatively small number of not altogether
consistent experiments, we have only obeyed
a necessity from which the human mind cannot
free itself. But there is something more, and that
is why I dwell on this topic. No one doubts that
Mayer's principle is not called upon to survive all
the particular laws from which it was deduced, in
\PageSep{131}
the same way that Newton's law has survived the
laws of Kepler from which it was derived, and
which are no longer anything but approximations,
if we take perturbations into account. Now why
does this principle thus occupy a kind of privileged
position among physical laws? There are many
reasons for that. At the outset we think that we
cannot reject it, or even doubt its absolute rigour,
without admitting the possibility of perpetual
motion; we certainly feel distrust at such a
prospect, and we believe ourselves less rash in
affirming it than in denying it. That perhaps is
not quite accurate. The impossibility of perpetual
motion only implies the conservation of energy for
reversible phenomena. The imposing simplicity
of Mayer's principle equally contributes to
strengthen our faith. In a law immediately deduced
from experiments, such as Mariotte's law,
this simplicity would rather appear to us a reason
for distrust; but here this is no longer the case.
We take elements which at the first glance are
unconnected; these arrange themselves in an unexpected
order, and form a harmonious whole.
We cannot believe that this unexpected harmony
is a mere result of chance. Our conquest
appears to be valuable to us in proportion to the
efforts it has cost, and we feel the more certain of
having snatched its true secret from Nature in proportion
as Nature has appeared more jealous of our
attempts to discover it. But these are only small
reasons. Before we raise Mayer's law to the
\PageSep{132}
dignity of an absolute principle, a deeper discussion
is necessary. But if we embark on this discussion
we see that this absolute principle is not even easy
to enunciate. In every particular case we clearly
see what energy is, and we can give it at least a
provisory definition; but it is impossible to find
a general definition of it. If we wish 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---\emph{there is something which
remains constant}. But has this a meaning? In
the determinist hypothesis the state of the universe
is determined by an extremely large number~$n$
of parameters, which I shall call $x_{1}$,~$x_{2}$, $x_{3}\Add{,}~\ldots\Add{,},~x_{n}$.
As soon as we know at a given moment the values of
these $n$~parameters, we also know their derivatives
with respect to time, and we can therefore calculate
the values of these same parameters at an
anterior or ulterior moment. In other words,
these $n$~parameters specify $n$~differential equations
of the first order. These equations have $n - 1$
integrals, and therefore there are $n - 1$ functions of
$x_{1}$,~$x_{2}$, $x_{3}\Add{,}~\ldots\Add{,}~x_{n}$, which remain constant. If we
say then, \emph{there is something which remains constant},
we are only enunciating a tautology. We would
be even embarrassed to decide which among all
our integrals is that which should retain the name
of energy. Besides, it is not in this sense that
Mayer's principle is understood when it is applied
to a limited system. We admit, then, that $p$~of
our $n$~parameters vary independently so that we
\PageSep{133}
have only $n - p$ relations, generally linear, between
our $n$~parameters and their derivatives. Suppose,
for the sake of simplicity, that the sum of the
work done by the external forces is zero, as well
as that of all the quantities of heat given off from
the interior: what will then be the meaning of
our principle? \emph{There is a combination of these $n - p$
relations, of which the first member is an exact
differential}; and then this differential vanishing
in virtue of our $n - p$ relations, its integral is a
constant, and it is this integral which we call
energy. But how can it be that there are several
parameters whose variations are independent?
That can only take place in the case of external
forces (although we have supposed, for the sake
of simplicity, that the algebraical sum of all the
work done by these forces has vanished). If,
in fact, the system were completely isolated from
all external action, the values of our $n$~parameters
at a given moment would suffice to determine
the state of the system at any ulterior moment
whatever, provided that we still clung to the determinist
hypothesis. We should therefore fall back
on the same difficulty as before. If the future
state of the system is not entirely determined
by its present state, it is because it further depends
on the state of bodies external to the system.
But then, is it likely that there exist among the
parameters~$x$ which define the state of the system of
equations independent of this state of the external
bodies? and if in certain cases we think we can
\PageSep{134}
find them, is it not only because of our ignorance,
and because the influence of these bodies is too
weak for our experiment to be able 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 upon
the state of the external bodies. Again, I have
supposed above that the sum of all the external
work is zero, and if we wish to be free from
this rather artificial restriction the enunciation
becomes still more difficult. To formulate
Mayer's principle by giving it an absolute
meaning, we must extend it to the whole
universe, and then we find ourselves face to
face with the very difficulty we have endeavoured
to avoid. To sum up, and to use ordinary
language, the law of the conservation of energy
can have only one significance, because there is
in it a property common to all possible properties;
but in the determinist hypothesis there is only one
possible, and then the law has no meaning. In
the indeterminist hypothesis, on the other hand,
it would have a meaning even if we wished to
regard it in an absolute sense. It would appear
as a limitation imposed on freedom.

But this word warns me that I am wandering
from the subject, and that I am leaving the
domain of mathematics and physics. I check
myself, therefore, and I wish to retain only one
impression of the whole of this discussion, and
that is, that Mayer's law is a form subtle enough
\PageSep{135}
for us to be able to put into it almost anything we
like. I do not mean by that that it corresponds
to no objective reality, nor that it is reduced to
mere tautology; since, in each particular case, and
provided we do not wish to extend it to the
absolute, it has a perfectly clear meaning. This
subtlety is a reason for believing that it will last
long; and as, on the other hand, it will only
disappear to be blended in a higher harmony,
we may work with confidence and utilise it,
certain beforehand that our work will not be
lost.

Almost everything that I have just said
applies to the principle of Clausius. What
distinguishes it is, that it is expressed by an
inequality. It will be said perhaps that 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 we hope to replace
them little by little by more exact laws. 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.

\Par{General Conclusions on Part~III.}---The principles
of mechanics are therefore presented to us
under two different aspects. On the one hand,
there are truths founded on experiment, and
verified approximately as far as almost isolated
systems are concerned; on the other hand,
\PageSep{136}
there are postulates applicable to the whole of
the universe and regarded as rigorously true.
If these postulates possess a generality and a
certainty which falsify the experimental truths
from which they were deduced, it is because
they reduce in final analysis to a simple convention
that we have a right to make, because
we are certain beforehand that no experiment
can contradict it. This convention, however, is
not absolutely arbitrary; it is not the child
of our caprice. We admit it because certain
experiments have shown us that it will be convenient,
and thus is explained how experiment
has built up the principles of mechanics, and
why, moreover, it cannot reverse them. Take a
comparison with geometry. The fundamental
propositions of geometry, for instance, Euclid's
postulate, are only conventions, and it is quite
as unreasonable to ask if they are true or false
as to ask if the metric system is true or false.
Only, these conventions are convenient, and there
are certain experiments which prove it to us. At
the first glance, the analogy is complete, the rôle
of experiment seems the same. We shall therefore
be tempted to say, either mechanics must
be looked upon as experimental science and then
it should be the same with geometry; or, on the
contrary, geometry is a deductive science, and
then we can say the same of mechanics. Such
a conclusion would be illegitimate. The experiments
which have led us to adopt as more
\PageSep{137}
convenient the fundamental conventions of
geometry refer to bodies which have nothing
in common with those that are studied by
geometry. They refer to the properties of solid
bodies and to the propagation of light in a straight
line. These are mechanical, optical experiments.
In no way can they be regarded as geometrical
experiments. And even the probable reason why
our geometry seems convenient to us is, that our
bodies, our hands, and our limbs enjoy the properties
of solid bodies. Our fundamental experiments are
pre-eminently physiological experiments which
refer, not to the space which is the object that
geometry must study, but to our body---that is to
say, to the instrument which we use for that
study. On the other hand, the fundamental
conventions of mechanics and the experiments
which prove to us that they are convenient,
certainly refer to the same objects or to analogous
objects. Conventional and general principles are
the natural and direct generalisations of experimental
and particular principles. Let it not be
said that I am thus tracing artificial frontiers
between the sciences; that I am separating by
a barrier geometry properly so called from the
study of solid bodies. I might just as well
raise a barrier between experimental mechanics
and the conventional mechanics of general
principles. Who does not see, in fact, that
by separating these two sciences we mutilate
both, and that what will remain of the conventional
\PageSep{138}
mechanics when it is isolated will be but
very little, and can in no way be compared with
that grand body of doctrine which is called
geometry.

We now understand why the teaching of
mechanics should remain experimental. Thus
only can we be made to understand the genesis
of the science, and that is indispensable for
a complete knowledge of the science itself.
Besides, if we study mechanics, it is in order
to apply it; and we can only apply it if it remains
objective. Now, as we have seen, when principles
gain in generality and certainty they lose in
objectivity. It is therefore especially with the
objective side of principles that we must be
early familiarised, and this can only be by
passing from the particular to the general, instead
of from the general to the particular.

Principles are conventions and definitions in
disguise. They are, however, deduced from
experimental laws, and these laws have, so to
speak, been erected into principles to which
our mind attributes an absolute value. Some
philosophers have generalised far too much.
They have thought that the principles were
the whole of science, and therefore that the
whole of science was conventional. This paradoxical
doctrine, which is called Nominalism,
cannot stand examination. How can a law
become a principle? It expressed a relation
between two real terms, $A$~and~$B$; but it was
\PageSep{139}
not rigorously true, it was only approximate.
We introduce arbitrarily an intermediate term,~$C$,
more or less imaginary, and $C$~is \emph{by definition} that
which has with~$A$ \emph{exactly} the relation expressed
by the law. So our law is decomposed into an
absolute and rigorous principle which expresses
the relation of~$A$ to~$C$, and an approximate experimental
and revisable law which expresses the
relation of~$C$ to~$B$. But it is clear that however
far this decomposition may be carried, laws will
always remain. We shall now enter into the
domain of laws properly so called.
\PageSep{140}


\Part{IV.}{Nature.}

\Chapter{IX.}{Hypotheses in Physics.}

\Par{The Rôle of Experiment and Generalisation.}---Exper\-iment
is the sole source of truth. It alone
can teach us something new; it alone can give
us certainty. These are two points that cannot
be questioned. But then, if experiment is everything,
what place is left for mathematical physics?
What can experimental physics do with such an
auxiliary---an auxiliary, moreover, which seems
useless, and even may be dangerous?

However, mathematical physics exists. It has
rendered undeniable service, and that is a fact
which has to be explained. It is not sufficient
merely to observe; we must use our observations,
and for that purpose we must generalise. This
is what has always been done, only as the recollection
of past errors has made man more and more
circumspect, he has observed more and more and
generalised less and less. Every age has scoffed
at its predecessor, accusing it of having generalised
\PageSep{141}
too boldly and too naïvely. Descartes used to
commiserate the Ionians. Descartes in his turn
makes us smile, and no doubt some day our
children will laugh at us. Is there no way of
getting at once to the gist of the matter, and
thereby escaping the raillery which we foresee?
Cannot we be content with experiment alone?
No, that is impossible; that would be a complete
misunderstanding of the true character of science.
The man of science must work with method.
Science is built up of facts, as a house is built of
stones; but an accumulation of facts is no more a
science than a heap of stones is a house. Most
important of all, the man of science must exhibit
foresight. Carlyle has written somewhere something
after this fashion. ``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.''\footnote
  {V. \Title{Past and Present}, end of Chapter~I., Book~II.\Transl}
Carlyle was a compatriot of Bacon,
and, like him, he wished to proclaim his worship
of \emph{the God of Things as they are}.

But Bacon would not have said that. That is
the language of the historian. The physicist
would most likely have said: ``John Lackland
passed by here. It is all the same to me, for he
will not pass this way again.''

We all know that there are good and bad
experiments. The latter accumulate in vain.
Whether there are a hundred or a thousand,
\PageSep{142}
one single piece of work by a real master---by a
Pasteur, for example---will be sufficient to sweep
them into oblivion. Bacon would have thoroughly
understood that, for he invented the phrase \Foreign{experimentum
crucis}; but Carlyle would not have understood
it. A fact is a fact. A student has read
such and such a number on his thermometer.
He has taken no precautions. It does not matter;
he has read it, and if it is only the fact which
counts, this is a reality that is as much entitled
to be called a reality as the peregrinations of King
John Lackland. What, then, is a good experiment?
It is that which teaches us something more than
an isolated fact. It is that which enables us to
predict, and to generalise. Without generalisation,
prediction is impossible. The circumstances
under which one has operated will never again
be reproduced simultaneously. The fact observed
will never be repeated. All that can be affirmed
is that under analogous circumstances an analogous
fact will be produced. To predict it, we must
therefore invoke the aid of analogy---that is to say,
even at this stage, we must generalise. However
timid we may be, there must be interpolation.
Experiment only gives us a certain number of
isolated points. They must be connected by a
continuous line, and this is a true generalisation.
But more is done. The curve thus traced will
pass between and near the points observed; it
will not pass through the points themselves.
Thus we are not restricted to generalising our
\PageSep{143}
experiment, we correct it; and the physicist who
would abstain from these corrections, and really
content himself with experiment pure and simple,
would be compelled to enunciate very extraordinary
laws indeed. Detached facts cannot
therefore satisfy us, and that is why our science
must be ordered, or, better still, generalised.

It is often said that experiments should be made
without preconceived ideas. That is impossible.
Not only would it make every experiment fruitless,
but even if we wished to do so, it could not be
done. Every man has his own conception of the
world, and this he cannot so easily lay aside. We
must, for example, use language, and our language
is necessarily steeped in preconceived ideas. Only
they are unconscious preconceived ideas, which
are a thousand times the most dangerous of all.
Shall we say, that if we cause others to intervene of
which we are fully conscious, that we shall only
aggravate the evil? I do not think so. I am
inclined to think that they will serve as ample
counterpoises---I was almost going to say antidotes.
They will generally disagree, they will enter into
conflict one with another, and \Foreign{ipso~facto}, they will
force us to look at things under different aspects.
This is enough to free us. He is no longer a slave
who can choose his master.

Thus, by generalisation, every fact observed
enables us to predict a large number of others;
only, we ought not to forget that the first alone
is certain, and that all the others are merely
\PageSep{144}
probable. However solidly founded a prediction
may appear to us, we are never \emph{absolutely} sure that
experiment will not prove it to be baseless if we
set to work to verify it. But the probability of its
accuracy is often so great that practically we may
be content with it. It is far better to predict
without certainty, than never to have predicted
at all. We should never, therefore, disdain to
verify when the opportunity presents itself. But
every experiment is long and difficult, and the
labourers are few, and the number of facts which
we require to predict is enormous; and besides
this mass, the number of direct verifications that
we can make will never be more than a negligible
quantity. Of this little that we can directly attain
we must choose the best. Every experiment must
enable us to make a maximum number of predictions
having the highest possible degree of probability.
The problem is, so to speak, to increase
the output of the scientific machine. I may be
permitted to compare science to a library which
must go on increasing indefinitely; the librarian
has limited funds for his purchases, and he must,
therefore, strain every nerve not to waste them.
Experimental physics has to make the purchases,
and experimental physics alone can enrich the
library. As for mathematical physics, her duty
is to draw up the catalogue. If the catalogue is
well done the library is none the richer for it; but
the reader will be enabled to utilise its riches;
and also by showing the librarian the gaps in his
\PageSep{145}
collection, it will help him to make a judicious
use of his funds, which is all the more important,
inasmuch as those funds are entirely inadequate.
That is the rôle of mathematical physics. It
must direct generalisation, so as to increase what
I called just now the output of science. By what
means it does this, and how it may do it without
danger, is what we have now to examine.

\Par{The Unity of Nature.}---Let us first of all observe
that every generalisation supposes in a certain
measure a belief in the unity and simplicity of
Nature. As far as the unity is concerned, there
can be no difficulty. If the different parts of the
universe were not as the organs of the same body,
they would not \Chg{re-act}{react} one upon the other; they
would mutually ignore each other, and we in
particular should only know one part. We need
not, therefore, ask if Nature is one, but how she
is one.

As for the second point, that is not so clear. It
is not certain that Nature is simple. Can we
without danger act as if she were?

There was a time when the simplicity of
Mariotte's law was an argument in favour of its
accuracy: when Fresnel himself, after having said
in a conversation with Laplace that Nature cares
naught for analytical difficulties, was compelled
to explain his words so as not to give offence to
current opinion. Nowadays, ideas have changed
considerably; but those who do not believe that
natural laws must be simple, are still often obliged
\PageSep{146}
to act as if they did believe it. They cannot
entirely dispense with this necessity without
making all generalisation, and therefore all science,
impossible. It is clear that any fact can be
generalised in an infinite number of ways, and
it is a question of choice. The choice can only
be guided by considerations of simplicity. Let
us take the most ordinary case, that of interpolation.
We draw a continuous line as regularly as
possible between the points given by observation.
Why do we avoid angular points and inflexions
that are too sharp? Why do we not make our
curve describe the most capricious zigzags? It
is because we know beforehand, or think we know,
that the law we have to express cannot be so
complicated as all that. The mass of Jupiter
may be deduced either from the movements of
his satellites, or from the perturbations of the
major planets, or from those of the minor planets.
If we take the mean of the determinations obtained
by these three methods, we find three numbers
very close together, but not quite identical. This
result might be interpreted by supposing that the
gravitation constant is not the same in the three
cases; the observations would be certainly much
better represented. Why do we reject this interpretation?
Not because it is absurd, but because
it is uselessly complicated. We shall only accept
it when we are forced to, and it is not imposed
upon us yet. To sum up, in most cases every law
is held to be simple until the contrary is proved.
\PageSep{147}

This custom is imposed upon physicists by the
reasons that I have indicated, but how can it be
justified in the presence of discoveries which daily
show us fresh details, richer and more complex?
How can we even reconcile it with the unity of
nature? For if all things are interdependent,
the relations in which so many different objects
intervene can no longer be simple.

If we study the history of science we see produced
two phenomena which are, so to speak,
each the inverse of the other. Sometimes it is
simplicity which is hidden under what is
apparently complex; sometimes, on the contrary,
it is simplicity which is apparent, and which
conceals extremely complex realities. What is
there more complicated than the disturbed
motions of the planets, and what more simple
than Newton's law? There, as Fresnel said,
Nature playing with analytical difficulties, only
uses simple means, and creates by their combination
I know not what tangled skein. Here it is
the hidden simplicity which must be disentangled.
Examples to the contrary abound. In the kinetic
theory of gases, molecules of tremendous velocity
are discussed, whose paths, deformed by incessant
impacts, have the most capricious shapes, and
plough their way through space in every direction.
The result observable is Mariotte's simple law.
Each individual fact was complicated. The law
of great numbers has re-established simplicity in
the mean. Here the simplicity is only apparent,
\PageSep{148}
and the coarseness of our senses alone prevents us
from seeing the complexity.

Many phenomena obey a law of proportionality.
But why? Because in these phenomena
there is something which is very small. The
simple law observed is only the translation of
the general analytical rule by which 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 only
very small, the law of proportionality is only
approximate, and simplicity is only apparent.
What I have just said applies to the law of the
superposition of small movements, which is so
fruitful in its applications and which is the foundation
of optics.

And Newton's law itself? Its simplicity, so
long undetected, is perhaps only apparent. Who
knows if it be not due to some complicated
mechanism, to the impact of some subtle matter
animated by irregular movements, and if it has
not become simple merely through the play of
averages and large numbers? In any case, it
is difficult not to suppose that the true law contains
complementary terms which may become
sensible at small distances. If in astronomy they
are negligible, and if the law thus regains its
simplicity, it is solely on account of the enormous
distances of the celestial bodies. No doubt, if our
means of investigation became more and more
penetrating, we should discover the simple beneath
\PageSep{149}
the complex, and then the complex from the
simple, and then again the simple beneath the
complex, and so on, without ever being able to
predict what the last term will be. We must stop
somewhere, and for science to be possible we must
stop where we have found simplicity. That is the
only ground on which we can erect the edifice of
our generalisations. But, this simplicity being
only apparent, will the ground be solid enough?
That is what we have now to discover.

For this purpose let us see what part is played
in our generalisations by the belief in simplicity.
We have verified a simple law in a considerable
number of particular cases. We refuse to admit
that this coincidence, so often repeated, is a result
of mere chance, and we conclude that the law
must be true in the general case.

Kepler remarks that the positions of a planet
observed by Tycho are all on the same ellipse.
Not for one moment does he think that, by a
singular freak of chance, Tycho had never looked
at the heavens except at the very moment when
the path of the planet happened to cut that
ellipse. What does it matter then if the simplicity
be real or if it hide a complex truth? Whether it
be due to the influence of great numbers which
reduces individual differences to a level, or to the
greatness or the smallness of certain quantities
which allow of certain terms to be neglected---in
no case is it due to chance. This simplicity, real
or apparent, has always a cause. We shall therefore
\PageSep{150}
always be able to reason in the same fashion,
and if a simple law has been observed in several
particular cases, we may legitimately suppose that
it still will be true in analogous cases. To refuse
to admit this would be to attribute an inadmissible
rôle to chance. However, there is a
difference. If the simplicity were real and profound
it would bear the test of the increasing
precision of our methods of measurement. If,
then, we believe Nature to be profoundly simple,
we must conclude that it is an approximate and
not a rigorous simplicity. This is what was
formerly done, but it is what we have no longer
the right to do. The simplicity of Kepler's laws,
for instance, is only apparent; but that does not
prevent them from being applied to almost all
systems analogous to the solar system, though
that prevents them from being rigorously exact.

\Par{Rôle of Hypothesis.}---Every generalisation is a
hypothesis. Hypothesis therefore plays a necessary
rôle, which no one has ever contested. Only,
it should always be as soon as possible submitted
to verification. It goes without saying that, if it
cannot stand this test, it must be abandoned
without any hesitation. This is, indeed, what
is generally done; but sometimes with a certain
impatience. Ah well!\ this impatience is not
justified. The physicist who has just given up
one of his hypotheses should, on the contrary,
rejoice, for he found an unexpected opportunity of
discovery. His hypothesis, I imagine, had not
\PageSep{151}
been lightly adopted, It took into account all the
known factors which seem capable of intervention
in the phenomenon. If it is not verified, it is
because there is something unexpected and extraordinary
about it, because we are on the point
of finding something unknown and new. Has
the hypothesis thus rejected been sterile? Far
from it. It may be even said that it has rendered
more service than a true hypothesis. Not only
has it been the occasion of a decisive experiment,
but if this experiment had been made by chance,
without the hypothesis, no conclusion could have
been drawn; nothing extraordinary would have
been seen; and only one fact the more would have
been catalogued, without deducing from it the
remotest consequence.

Now, under what conditions is the use of
hypothesis without danger? The proposal to
submit all to experiment is not sufficient. Some
hypotheses are dangerous,---first and foremost
those which are tacit and unconscious. And
since we make them without knowing them,
we cannot get rid of them. Here again, there
is a service that mathematical physics may
render us. By the precision which is its characteristic,
we are compelled to formulate all the
hypotheses that we would unhesitatingly make
without its aid. Let us also notice that it is
important not to multiply hypotheses indefinitely.
If we construct a theory based upon multiple hypotheses,
and if experiment condemns it, which of
\PageSep{152}
the premisses must be changed? It is impossible
to tell. Conversely, if the experiment succeeds,
must we suppose that it has verified all these
hypotheses at once? Can several unknowns be
determined from a single equation?

We must also take care to distinguish between
the different kinds of hypotheses. First of all,
there are those which are quite natural and
necessary. It is difficult not to suppose that the
influence of very distant bodies is quite negligible,
that small movements obey a linear law, and that
effect is a continuous function of its cause. I will
say as much for the conditions imposed by
symmetry. All these hypotheses affirm, so to
speak, the common basis of all the theories of
mathematical physics. They are the last that
should be abandoned. There is a second category
of hypotheses which I shall qualify as indifferent.
In most questions the analyst assumes, at the
beginning of his calculations, either that matter is
continuous, or the reverse, that it is formed of
atoms. In either case, his results would have
been the same. On the atomic supposition he has
a little more difficulty in obtaining them---that is
all. If, then, experiment confirms his conclusions,
will he suppose that he has proved, for example,
the real existence of atoms?

In optical theories two vectors are introduced,
one of which we consider as a velocity and the
other as a vortex. This again is an indifferent
hypothesis, since we should have arrived at the
\PageSep{153}
same conclusions by assuming the former to be
a vortex and the latter to be a velocity. The
success of the experiment cannot prove, therefore,
that the first vector is really a velocity. It only
proves one thing---namely, that it is a vector;
and that is the only hypothesis that has really
been introduced into the premisses. To give it
the concrete appearance that the fallibility of our
minds demands, it was necessary to consider it
either as a velocity or as a vortex. In the same
way, it was necessary to represent it by an~$x$ or a~$y$,
but the result will not prove that we were right
or wrong in regarding it as a velocity; nor will it
prove we are right or wrong in calling it~$x$ and
not~$y$.

These indifferent hypotheses are never dangerous
provided their characters are not misunderstood.
They may be useful, either as artifices for
calculation, or to assist our understanding by
concrete images, to fix the ideas, as we say. They
need not therefore be rejected. The hypotheses
of the third category are real generalisations.
They must be confirmed or invalidated by experiment.
Whether verified or condemned, they will
always be fruitful; but, for the reasons I have
given, they will only be so if they are not too
numerous.

\Par{Origin of Mathematical Physics.}---Let us go
further and study more closely the conditions
which have assisted the development of mathematical
physics. We recognise at the outset that
\PageSep{154}
the efforts of men of science have always tended
to resolve the complex phenomenon given directly
by experiment into a very large number of elementary
phenomena, and that in three different
ways.

First, with respect to time. Instead of embracing
in its entirety the progressive development of a
phenomenon, we simply try to connect each
moment with the one immediately preceding.
We admit that the present state of the world
only depends on the immediate past, without
being directly influenced, so to speak, by the
recollection of a more distant past. Thanks to
this postulate, instead of studying directly the
whole succession of phenomena, we may confine
ourselves to writing down its \emph{differential equation};
for the laws of Kepler we substitute the law of
Newton.

Next, we try to decompose the phenomena in
space. What experiment gives us is a confused
aggregate of facts spread over a scene of considerable
extent. We must try to deduce the elementary
phenomenon, which will still be localised in a
very small region of space.

A few examples perhaps will make my meaning
clearer. If we wished to study in all its complexity
the distribution of temperature in a cooling
solid, we could never do so. This is simply because,
if we only reflect that a point in the solid
can directly impart some of its heat to a neighbouring
point, it will immediately impart that
\PageSep{155}
heat only to the nearest points, and it is but
gradually that the flow of heat will reach other
portions of the solid. The elementary phenomenon
is the interchange of heat between two
contiguous points. It is strictly localised and
relatively simple if, as is natural, we admit that
it is not influenced by the temperature of the
molecules whose distance apart is small.

I bend a rod: it takes a very complicated form,
the direct investigation of which would be impossible.
But I can attack the problem, however,
if I notice that its flexure is only the resultant of
the deformations of the very small elements of the
rod, and that the deformation of each of these
elements only depends on the forces which are
directly applied to it, and not in the least on
those which may be acting on the other elements.

In all these examples, which may be increased
without difficulty, it is admitted that there is no
action at a distance or at great distances. That
is an hypothesis. It is not always true, as the law
of gravitation proves. It must therefore be verified.
If it is confirmed, even approximately, it is valuable,
for it helps us to use mathematical physics,
at any rate by successive approximations. If it
does not stand the test, we must seek something
else that is analogous, for there are other means
of arriving at the elementary phenomenon. If
several bodies act simultaneously, it may happen
that their actions are independent, and may be
added one to the other, either as vectors or as scalar
\PageSep{156}
quantities. The elementary phenomenon is then
the action of an isolated body. Or suppose, again,
it is a question of small movements, or more
generally of small variations which obey the well-known
law of mutual or relative independence.
The movement observed will then be decomposed
into simple movements---for example, sound into
its harmonics, and white light into its monochromatic
components. When we have discovered in
which direction to seek for the elementary phenomena,
by what means may we reach it? First, it
will often happen that in order to predict it, or rather
in order to predict what is useful to us, it will not
be necessary to know its mechanism. The law of
great numbers will suffice. Take for example the
propagation of heat. Each molecule radiates towards
its neighbour---we need not inquire according
to what law; and if we make any supposition
in this respect, it will be an indifferent hypothesis,
and therefore useless and unverifiable. In fact,
by the action of averages and thanks to the
symmetry of the medium, all differences are
levelled, and, whatever the hypothesis may be, the
result is always the same.

The same feature is presented in the theory of
elasticity, and in that of capillarity. The neighbouring
molecules attract and repel each other, we
need not inquire by what law. It is enough for us
that this attraction is sensible at small distances
only, and that the molecules are very numerous,
that the medium is symmetrical, and we have
\PageSep{157}
only to let the law of great numbers come into
play.

Here again the simplicity of the elementary
phenomenon is hidden beneath the complexity of
the observable resultant phenomenon; but in its
turn this simplicity was only apparent and disguised
a very complex mechanism. Evidently the
best means of reaching the elementary phenomenon
would be experiment. It would be necessary
by experimental artifices to dissociate the
complex system which nature offers for our investigations
and carefully to study the elements as
dissociated as possible; for example, natural white
light would be decomposed into monochromatic
lights by the aid of the prism, and into polarised
lights by the aid of the polariser. Unfortunately,
that is neither always possible nor always sufficient,
and sometimes the mind must run ahead of
experiment. I shall only give one example which
has always struck me rather forcibly. If I decompose
white light, I shall be able to isolate a
portion of the spectrum, but however small it may
be, it will always be a certain width. In the same
way the natural lights which are called \emph{monochromatic}
%[** TN: "nous donnent une raie très fine, mais qui n'est pas cependant infiniment fine"]
give us a very fine \Reword{array, but a y}{ray, but one} which
is not, however, infinitely fine. It might be
supposed that in the experimental study of the
properties of these natural lights, by operating
with finer and finer rays, and passing on at last
to the limit, so to speak, we should eventually
obtain the properties of a rigorously monochromatic
\PageSep{158}
light. That would not be accurate.
I assume that two rays emanate from the same
source, that they are first polarised in planes at
right angles, that they are then brought back
again to the same plane of polarisation, and that
we try to obtain interference. If the light were
\emph{rigorously} monochromatic, there would be interference;
but with our nearly monochromatic
lights, there will be no interference, and that,
however narrow the ray may be. For it to be
otherwise, the ray would have to be several million
times finer than the finest known rays.

Here then we should be led astray by proceeding
to the limit. The mind has to run ahead of 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 state the problem in
the form of an equation. It only remains to deduce
from it by combination the observable and
verifiable complex fact. That is what we call
\emph{integration}, and it is the province of the mathematician.
It might be asked, why in physical
science generalisation so readily takes the
mathematical form. The reason is now easy to
see. It is not only because we have to express
numerical laws; it is because the observable
phenomenon is due to the superposition of a large
number of elementary phenomena which are \emph{all
similar to each other}; and in this way differential
equations are quite naturally introduced. It is
\PageSep{159}
not enough that each elementary phenomenon
should obey simple laws: all those that we have
to combine must obey the same law; then only
is the intervention of mathematics of any use.
Mathematics teaches us, in fact, to combine like
with like. Its object is to divine the result of a
combination without having to reconstruct that
combination element by element. If we have to
repeat the same operation several times, mathematics
enables us to avoid this repetition by telling
the result beforehand by a kind of induction.
This I have explained before in the \hyperref[chapref:I]{chapter on
mathematical reasoning}. But for that purpose
all these operations must be similar; in the contrary
case we must evidently make up our minds
to working them out in full one after the other,
and mathematics will be useless. It is therefore,
thanks to the approximate homogeneity of the
matter studied by physicists, that mathematical
physics came into existence. In the natural
sciences the following conditions are no longer to
be found:---homogeneity, relative independence of
remote parts, simplicity of the elementary fact;
and that is why the student of natural science is
compelled to have recourse to other modes of
generalisation.
\PageSep{160}


\Chapter{X.}{The Theories of Modern Physics.}

\Par{Significance of Physical Theories.}---The ephemeral
nature of scientific theories takes by surprise the
man of the world. Their brief period of prosperity
ended, he sees them abandoned one after another;
he sees ruins piled upon ruins; he predicts that
the theories in fashion to-day will in a short time
succumb in their turn, and he concludes that they
are absolutely in vain. This is what he calls the
\emph{bankruptcy of science}.

His scepticism is superficial; he does not take
into account the object of scientific theories and
the part they play, or he would understand that
the ruins may be still good for something. No
theory seemed established on firmer ground than
Fresnel's, which attributed light to the movements
of the ether. Then if Maxwell's theory is
to-day preferred, does that mean that Fresnel's
work was in vain? No; for Fresnel's object was
not to know whether there really is an ether, if it
is or is not formed of atoms, if these atoms really
move in this way or that; his object was to
predict optical phenomena.

This Fresnel's theory enables us to do to-day
\PageSep{161}
as well as it did before Maxwell's time. The
differential equations are always true, they may
be always integrated by the same methods, and
the results of this integration still preserve their
value. It cannot be said that this is reducing
physical theories to simple practical recipes;
these equations express relations, and if the
equations remain true, it is because the relations
preserve their reality. They teach us now, as they
did then, that there is such and such a relation
between this thing and that; only, the something
which we then called \emph{motion}, we now call \emph{electric
current}. But these are merely names of the images
we substituted for the real objects which Nature
will hide for ever from our eyes. The true relations
between these real objects are the only reality we
can attain, and the sole condition is that the same
relations shall exist between these objects as between
the images we are forced to put in their place. If
the relations are known to us, what does it matter
if we think it convenient to replace one image by
another?

That a given periodic phenomenon (an electric
oscillation, for instance) is really due to the
vibration of a given atom, which, behaving like
a pendulum, is really displaced in this manner or
that, all this is neither certain nor essential.
But that there is between the electric oscillation,
the movement of the pendulum, and all periodic
phenomena an intimate relationship which corresponds
to a profound reality; that this relationship,
\PageSep{162}
this similarity, or rather this parallelism, is continued
in the details; that it is a consequence of
more general principles such as that of the conservation
of energy, and that of least action; this
we may affirm; this is the truth which will ever
remain the same in whatever garb we may see fit
to clothe it.

Many theories of dispersion have been proposed.
The first were imperfect, and contained but little
truth. Then came that of Helmholtz, and this
in its turn was modified in different ways; its
author himself conceived another theory, founded
on Maxwell's principles. But the remarkable
thing is, that all the scientists who followed
Helmholtz obtain the same equations, although
their starting-points were to all appearance widely
separated. I venture to say that these theories
are all simultaneously true; not merely because
they express a true relation---that between absorption
and abnormal dispersion. In the premisses
of these theories the part that is true is the part
common to all: it is the affirmation of this or
that relation between certain things, which some
call by one name and some by another.

The kinetic theory of gases has given rise to
many objections, to which it would be difficult
to find an answer were it claimed that the theory
is absolutely true. But all these objections do
not alter the fact that it has been useful,
particularly in revealing to us one true relation
which would otherwise have remained profoundly
\PageSep{163}
hidden---the relation between gaseous and osmotic
pressures. In this sense, then, it may be said to
be true.

When a physicist finds a contradiction between
two theories which are equally dear to him, he
sometimes says: ``Let us not be troubled, but let
us hold fast to the two ends of the chain, lest
we lose the intermediate links.'' This argument
of the embarrassed theologian would be ridiculous
if we were to attribute to physical theories the
interpretation given them by the man of the
world. In case of contradiction one of them at
least should be considered false. But this is no
longer the case if we only seek in them what
should be sought. It is quite possible that they
both express true relations, and that the contradictions
only exist in the images we have formed
to ourselves of reality. To those who feel that
we are going too far in our limitations of the
domain accessible to the scientist, I reply: These
questions which we forbid you to investigate,
and which you so regret, are not only insoluble,
they are illusory and devoid of meaning.

Such a philosopher claims that all physics can be
explained by the mutual impact of atoms. If he
simply means that the same relations obtain
between physical phenomena as between the
mutual impact of a large number of billiard
balls---well and good!\ this is verifiable, and
perhaps is true. But he means something more,
and we think we understand him, because we
\PageSep{164}
think we know what an impact is. Why? Simply
because we have often watched a game of billiards.
Are we to understand that God experiences the
same sensations in the contemplation of His
work that we do in watching a game of billiards?
If it is not our intention to give his assertion
this fantastic meaning, and if we do not wish
to give it the more restricted meaning I have
already mentioned, which is the sound meaning,
then it has no meaning at all. Hypotheses of
this kind have therefore only a metaphorical sense.
The scientist should no more banish them than a
poet banishes metaphor; but he ought to know
what they are worth. They may be useful to
give satisfaction to the mind, and they will do
no harm as long as they are only indifferent
hypotheses.

These considerations explain to us why certain
theories, that were thought to be abandoned and
definitively condemned by experiment, are suddenly
revived from their ashes and begin a new life.
It is because they expressed true relations, and
had not ceased to do so when for some reason or
other we felt it necessary to enunciate the same
relations in another language. Their life had been
latent, as it were.

Barely fifteen years ago, was there anything
more ridiculous, more quaintly old-fashioned, than
the fluids of Coulomb? And yet, here they are
re-appearing under the name of \emph{electrons}. In what
do these permanently electrified molecules differ
\PageSep{165}
from the electric molecules of Coulomb? It is
true that in the electrons the electricity is supported
by a little, a very little matter; in other
words, they have mass. Yet Coulomb did not
deny mass to his fluids, or if he did, it was with
reluctance. It would be rash to affirm that the
belief in electrons will not also undergo an eclipse,
but it was none the less curious to note this unexpected
renaissance.

But the most striking example is Carnot's
principle. Carnot established it, starting from
false hypotheses. When it was found that heat
was indestructible, and may be converted into
work, his ideas were completely abandoned;
later, Clausius returned to them, and to him is
due their definitive triumph. In its primitive
form, Carnot's theory expressed in addition to
true relations, other inexact relations, the \Foreign{débris}
of old ideas; but the presence of the latter did
not alter the reality of the others. Clausius had
only to separate them, just as one lops off dead
branches.

The result was the second fundamental law of
\Chg{thermodynamics}{thermo-dynamics}. The relations were always the
same, although they did not hold, at least to all
appearance, between the same objects. This was
sufficient for the principle to retain its value.
Nor have the reasonings of Carnot perished on
this account; they were applied to an imperfect
conception of matter, but their form---\ie, the
essential part of them, remained correct. What
\PageSep{166}
I have just said throws some light at the same
time on the rôle of general principles, such as
those of the principle of least action or of the
conservation of energy. These principles are of
very great value. They were obtained in the
search for what there was in common in the
enunciation of numerous physical laws; they
thus represent the quintessence of innumerable
observations. However, from their very generality
results a consequence to which I have called
attention in \ChapRef{VIII}.---namely, that they are
no longer capable of verification. As we cannot
give a general definition of energy, the principle
of the conservation of energy simply signifies that
there is a \emph{something} which remains constant.
\Pagelabel{166}%
Whatever fresh notions of the world may be
given us by future experiments, we are certain
beforehand that there is something which remains
constant, and which may be called \emph{energy}. Does
this mean that the principle has no meaning and
vanishes into a tautology? Not at all. It means
that the different things to which we give the
name of \emph{energy} are connected by a true relationship;
it affirms between them a real relation.
But then, if this principle has a meaning, it may
be false; it may be that we have no right to
extend indefinitely its applications, and yet it is
certain beforehand to be verified in the strict
sense of the word. How, then, shall we know
when it has been extended as far as is legitimate?
Simply when it ceases to be useful to us---\ie,
\PageSep{167}
when we can no longer use it to predict correctly
new phenomena. We shall be certain 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 nevertheless have condemned it.

\Par{Physics and Mechanism.}---Most theorists have a
constant predilection for explanations borrowed
from physics, mechanics, or dynamics. Some
would be satisfied if they could account for all
phenomena by the motion of molecules attracting
one another according to certain laws. Others
are more exact: they would suppress attractions
acting at a distance; their molecules would follow
rectilinear paths, from which they would only be
deviated by impacts. Others again, such as Hertz,
suppress the forces as well, but suppose their
molecules subjected to geometrical connections
analogous, for instance, to those of articulated
systems; thus, they wish to reduce dynamics to a
kind of kinematics. In a word, they all wish to
bend nature into a certain form, and unless they
can do this they cannot be satisfied. Is Nature
flexible enough for this?

We shall examine this question in \ChapRef{XII}.,
\Foreign{àpropos} of Maxwell's theory. Every time that the
principles of least action and energy are satisfied,
we shall see that not only is there always a
mechanical explanation possible, but that there
is an unlimited number of such explanations. By
means of a well-known theorem due to Königs,
\PageSep{168}
it may be shown that we can explain everything
in an unlimited number of ways, by connections
after the manner of Hertz, or, again, by central
forces. No doubt it may be just as easily demonstrated
that everything may be explained by
simple impacts. For this, let us bear in mind
that it is not enough to be content with the
ordinary matter of which we are aware by means
of our senses, and the movements of which we
observe directly. We may conceive of ordinary
matter as either composed of atoms, whose internal
movements escape us, our senses being able to
estimate only the displacement of the whole; or
we may imagine one of those subtle fluids, which
under the name of \emph{ether} or other names, have
from all time played so important a rôle in
physical theories. Often we go further, and regard
the ether as the only primitive, or even as the
only true matter. The more moderate consider
ordinary matter to be condensed ether, and
there is nothing startling in this conception; but
others only reduce its importance still further,
and see in matter nothing more than the geometrical
locus of singularities in the ether. Lord
Kelvin, for instance, holds what we call matter
to be only the locus of those points at which the
ether is animated by vortex motions. Riemann
believes it to be locus of those points at which
ether is constantly destroyed; to Wiechert or
Larmor, it is the locus of the points at which
the ether has undergone a kind of torsion of a
\PageSep{169}
very particular kind. Taking any one of these
points of view, I ask by what right do we apply
to the ether the mechanical properties observed
in ordinary matter, which is but false matter?
The ancient fluids, caloric, electricity,~etc., were
abandoned when it was seen that heat is not
indestructible. But they were also laid aside
for another reason, In materialising them, their
individuality was, so to speak, emphasised---gaps
were opened between them; and these gaps had
to be filled in when the sentiment of the unity of
Nature became stronger, and when the intimate
relations which connect all the parts were perceived.
In multiplying the fluids, not only did
the ancient physicists create unnecessary entities,
but they destroyed real ties. It is not enough for
a theory not to affirm false relations; it must not
conceal true relations.

Does our ether actually exist? We know the
origin of our belief in the ether. If light takes
several years to reach us from a distant star, it
is no longer on the star, nor is it on the earth.
It must be somewhere, and supported, so to speak,
by some material agency.

The same idea may be expressed in a more
mathematical and more abstract form. What we
note are the changes undergone by the material
molecules. We see, for instance, that the photographic
plate experiences the consequences of a
phenomenon of which the incandescent mass of
a star was the scene several years before. Now,
\PageSep{170}
in ordinary mechanics, the state of the system
under consideration depends only on its state at
the moment immediately preceding; the system
therefore satisfies certain differential equations.
On the other hand, if we did not believe in the
ether, the state of the material universe would
depend not only on the state immediately preceding,
but also on much older states; the system
would satisfy equations of finite differences. The
ether was invented to escape this breaking down
of the laws of general mechanics.

Still, this would only compel us to fill the
interplanetary space with ether, but not to
make it penetrate into the midst of the material
media. Fizeau's experiment goes further. By
the interference of rays which have passed
through the air or water in motion, it seems to
show us two different media penetrating each
other, and yet being displaced with respect to
each other. The ether is all but in our grasp.
Experiments can be conceived in which we come
closer still to it. Assume that Newton's principle
of the equality of action and \Chg{re-action}{reaction} is not true
if applied to matter \emph{alone}, and that this can be
proved. The geometrical sum of all the forces
applied to all the molecules would no longer be
zero. If we did not wish to change the whole of the
science of mechanics, we should have to introduce
the ether, in order that the action which matter
apparently undergoes should be counterbalanced
by the \Chg{re-action}{reaction} of matter on something.
\PageSep{171}

Or again, suppose we discover that optical and
electrical phenomena are influenced by the motion
of the earth. It would follow that those phenomena
might reveal to us not only the relative
motion of material bodies, but also what would
seem to be their absolute motion. Again, it would
be necessary to have an ether in order that these
so-called absolute movements should not be their
displacements with respect to empty space, but
with respect to something concrete.

Will this ever be accomplished? I do not
think so, and I shall explain why; and yet, it is
not absurd, for others have entertained this view.
For instance, if the theory of Lorentz, of which I
shall speak in more detail in \ChapRef{XIII}., were
true, Newton's principle would not apply to matter
\emph{alone}, and the difference would not be very far
from being within reach of experiment. On the
other hand, many experiments have been made
on the influence of the motion of the earth. The
results have always been negative. But if these
experiments have been undertaken, it is because
we have not been certain beforehand; and indeed,
according to current theories, the compensation
would be only approximate, and we might expect
to find accurate methods giving positive results.
I think that such a hope is illusory; it was none
the less interesting to show that a success of this
kind would, in a certain sense, open to us a new
world.

And now allow me to make a digression; I
\PageSep{172}
must explain why I do not believe, in spite of
Lorentz, that more exact observations will ever
make evident anything else but the relative displacements
of material bodies. Experiments have
been made that should have disclosed the terms
of the first order; the results were nugatory.
Could that have been by chance? No one has
admitted this; a general explanation was sought,
and Lorentz found it. He showed that the terms
of the first order should cancel each other, but
not the terms of the second order. Then more
exact experiments were made, which were also
negative; neither could this be the result of
chance. An explanation was necessary, and was
forthcoming; they always are; hypotheses are
what we lack the least. But this is not enough.
Who is there who does not think that this leaves
to chance far too important a rôle? Would it
not also be a chance that this singular concurrence
should cause a certain circumstance to destroy the
terms of the first order, and that a totally different
but very opportune circumstance should cause
those of the second order to vanish? No; the
same explanation must be found for the two
cases, and everything tends to show that this
explanation would serve equally well for the
terms of the higher order, and that the mutual
destruction of these terms will be rigorous and
absolute.

\Par{The Present State of Physics.}---Two opposite
tendencies may be distinguished in the history
\PageSep{173}
of the development of physics. On the one hand,
new relations are continually being discovered
between objects which seemed destined to remain
for ever unconnected; scattered facts cease to be
strangers to each other and tend to be marshalled
into an imposing synthesis. The march of science
is towards unity and simplicity.

On the other hand, new phenomena are continually
being revealed; it will be long before
they can be assigned their place---sometimes it
may happen that to find them a place a corner of
the edifice must be demolished. In the same way,
we are continually perceiving details ever more
varied in the phenomena we know, where our
crude senses used to be unable to detect any lack
of unity. What we thought to be simple becomes
complex, and the march of science seems to be
towards diversity and complication.

Here, then, are two opposing tendencies, each of
which seems to triumph in turn. Which will win?
If the first wins, science is possible; but nothing
proves this \Foreign{à~priori}, and it may be that after
unsuccessful efforts to bend Nature to our ideal of
unity in spite of herself, we shall be submerged by
the ever-rising flood of our new riches and compelled
to renounce all idea of classification---to
abandon our ideal, and to reduce science to the
mere recording of innumerable recipes.

In fact, we can give this question no answer.
All that we can do is to observe the science of
to-day, and compare it with that of yesterday.
\PageSep{174}
No doubt after this examination we shall be in a
position to offer a few conjectures.

Half-a-century ago hopes ran high indeed. The
unity of force had just been revealed to us by the
discovery of the conservation of energy and of its
transformation. This discovery also showed that
the phenomena of heat could be explained by
molecular movements. Although the nature of
these movements was not exactly known, no one
doubted but that they would be ascertained before
long. As for light, the work seemed entirely completed.
So far as electricity was concerned, there
was not so great an advance. Electricity had just
annexed magnetism. This was a considerable and
a definitive step towards unity. But how was
electricity in its turn to be brought into the
general unity, and how was it to be included in
the general universal mechanism? No one had
the slightest idea. As to the possibility of the inclusion,
all were agreed; they had faith. Finally,
as far as the molecular properties of material
bodies are concerned, the inclusion seemed easier,
but the details were very hazy. In a word, hopes
were vast and strong, but vague.

To-day, what do we see? In the first place, a
step in advance---immense progress. The relations
between light and electricity are now known; the
three domains of light, electricity, and magnetism,
formerly separated, are now one; and this annexation
seems definitive.

Nevertheless the conquest has caused us some
\PageSep{175}
sacrifices. Optical phenomena become particular
cases in electric phenomena; as long as the former
remained isolated, it was easy to explain them by
movements which were thought to be known in
all their details. That was easy enough; but any
explanation to be accepted must now cover the
whole domain of electricity. This cannot be done
without difficulty.

The most satisfactory theory is that of Lorentz;
it is unquestionably the theory that best explains
the known facts, the one that throws into relief
the greatest number of known relations, the one in
which we find most traces of definitive construction.
That it still possesses a serious fault I
have shown above. It is in contradiction with
Newton's law that action and \Chg{re-action}{reaction} are equal
and opposite---or rather, this principle according
to Lorentz cannot be applicable to matter alone;
if it be true, it must take into account the action
of the ether on matter, and the \Chg{re-action}{reaction} of the
matter on the ether. Now, in the new order, it is
very likely that things do not happen in this way.

However this may be, it is due to Lorentz that
the results of Fizeau on the optics of moving
bodies, the laws of normal and abnormal dispersion
and of absorption are connected with
each other and with the other properties of the
ether, by bonds which no doubt will not be
readily severed. Look at the ease with which the
new Zeeman phenomenon found its place, and
even aided the classification of Faraday's magnetic
\PageSep{176}
rotation, which had defied all Maxwell's efforts.
This facility proves that Lorentz's theory is not a
mere artificial combination which must eventually
find its solvent. It will probably have to be
modified, but not destroyed.

The only object of Lorentz was to include in a
single whole all the optics and electro-dynamics
of moving bodies; he did not claim to give a
mechanical explanation. Larmor goes further;
keeping the essential part of Lorentz's theory, he
grafts upon it, so to speak, MacCullagh's ideas on
the direction of the movement of the ether.
MacCullagh held that the velocity of the ether
is the same in magnitude and direction as the
magnetic force. Ingenious as is this attempt, the
fault in Lorentz's theory remains, and is even
aggravated. According to Lorentz, we do not
know what the movements of the ether are; and
because we do not know this, we may suppose
them to be movements compensating those of
matter, and re-affirming that action and \Chg{re-action}{reaction}
are equal and opposite. According to Larmor
we know the movements of the ether, and we
can prove that the compensation does not take
place.

If Larmor has failed, as in my opinion he has,
does it necessarily follow that a mechanical explanation
is impossible? Far from it. I said
above that as long as a phenomenon obeys the
two principles of energy and least action, so long
it allows of an unlimited number of mechanical
\PageSep{177}
explanations. And so with the phenomena of
optics and electricity.

But this is not enough. For a mechanical
explanation to be good it must be simple; to
choose it from among all the explanations that are
possible there must be other reasons than the
necessity of making a choice. Well, we have no
theory as yet which will satisfy this condition and
consequently be of any use. Are we then to
complain? That would be to forget the end we
seek, which is not the mechanism; the true and
only aim is unity.

We ought therefore to set some limits to
our ambition. Let us not seek to formulate a
mechanical explanation; let us be content to
show that we can always find one if we wish. In
this we have succeeded. The principle of the
conservation of energy has always been confirmed,
and now it has a fellow in the principle of least
action, stated in the form appropriate to physics.
This has also been verified, at least as far as
concerns the reversible phenomena which obey
Lagrange's equations---in other words, which obey
the most general laws of physics. The irreversible
phenomena are much more difficult to bring into
line; but they, too, are being co-ordinated and
tend to come into the unity. The light which
illuminates them comes from Carnot's principle.
For a long time thermo-dynamics was confined to
the study of the dilatations of bodies and of their
change of state. For some time past it has been
\PageSep{178}
growing bolder, and has considerably extended its
domain. We owe to it the theories of the voltaic
cell and of their thermo-electric phenomena; there
is not a corner in physics which it has not explored,
and it has even attacked chemistry itself.
The same laws hold good; everywhere, disguised
in some form or other, we find Carnot's principle;
everywhere also appears that eminently abstract
concept of entropy which is as universal as the
concept of energy, and like it, seems to conceal a
reality. It seemed that radiant heat must escape,
but recently that, too, has been brought under the
same laws.

In this way fresh analogies are revealed which
may be often pursued in detail; electric resistance
resembles the viscosity of fluids; hysteresis would
rather be like the friction of solids. In all cases
friction appears to be the type most imitated by
the most diverse irreversible phenomena, and this
relationship is real and profound.

A strictly mechanical explanation of these
phenomena has also been sought, but, owing to
their nature, it is hardly likely that it will be
found. To find it, it has been necessary to
suppose that the irreversibility is but apparent, that
the elementary phenomena are reversible and obey
the known laws of dynamics. But the elements
are extremely numerous, and become blended
more and more, so that to our crude sight all
appears to tend towards uniformity---\ie, all seems
to progress in the same direction, and that without
\PageSep{179}
hope of return. The apparent irreversibility is
therefore but an effect of the law of great numbers.
Only a being of infinitely subtle senses, such as
Maxwell's demon, could unravel this tangled skein
and turn back the course of the universe.

This conception, which is connected with the
kinetic theory of gases, has cost great effort and
has not, on the whole, been fruitful; it may
become so. This is not the place to examine if it
leads to contradictions, and if it is in conformity
with the true nature of things.

Let us notice, however, the original ideas of
M.~Gouy on the Brownian movement. According
to this scientist, this singular movement does not
obey Carnot's principle. The particles which it sets
moving would be smaller than the meshes of that
tightly drawn net; they would thus be ready to
separate them, and thereby to set back the course
of the universe. One can almost see Maxwell's
demon at work.\footnote
  {Clerk-Maxwell imagined some supernatural agency at work,
  sorting molecules in a gas of uniform temperature into (\textit{a})~those
  possessing kinetic energy above the average, (\textit{b})~those possessing
  kinetic energy below the average.\Transl}

To resume, phenomena long known are gradually
being better classified, but new phenomena come
to claim their place, and most of them, like the
Zeeman effect, find it at once. Then we have the
cathode rays, the X-rays, uranium and radium
rays; in fact, a whole world of which none had
suspected the existence. How many unexpected
\PageSep{180}
guests to find a place for! No one can yet predict
the place they will occupy, but I do not believe
they will destroy the general unity: I think that
they will rather complete it. On the one hand,
indeed, the new radiations seem to be connected
with the phenomena of luminosity; not only do
they excite fluorescence, but they sometimes come
into existence under the same conditions as that
property; neither are they unrelated to the cause
which produces the electric spark under the action
of ultra-violet light. Finally, and most important
of all, it is believed that in all these phenomena
there exist ions, animated, it is true, with velocities
far greater than those of electrolytes. All this is
very vague, but it will all become clearer.

Phosphorescence and the action of light on the
spark were regions rather isolated, and consequently
somewhat neglected by investigators. It is to be
hoped that a new path will now be made which
will facilitate their communications with the
rest of science. Not only do we discover new
phenomena, but those we think we know are
revealed in unlooked-for aspects. In the free ether
the laws preserve their majestic simplicity, but
matter properly so called seems more and more
complex; all we can say of it is but approximate,
and our formulæ are constantly requiring new
terms.

But the ranks are unbroken, the relations that
we have discovered between objects we thought
simple still hold good between the same objects
\PageSep{181}
when their complexity is recognised, and that
alone is the important thing. Our equations
become, it is true, more and more complicated, so
as to embrace more closely the complexity of
nature; but nothing is changed in the relations
which enable these equations to be derived from
each other. In a word, the form of these equations
persists. Take for instance the laws of reflection.
Fresnel established them by a simple and attractive
theory which experiment seemed to confirm. Subsequently,
more accurate researches have shown
that this verification was but approximate; traces
of elliptic polarisation were detected everywhere.
But it is owing to the first approximation that the
cause of these anomalies was found in the existence
of a transition layer, and all the essentials of
Fresnel's theory have remained. We cannot help
reflecting that all these relations would never have
been noted if there had been doubt in the first
place as to the complexity of the objects they
connect. Long ago it was said: If Tycho had had
instruments ten times as precise, we would never
have had a Kepler, or a Newton, or Astronomy.
It is a misfortune for a science to be born too late,
when the means of observation have become too
perfect. That is what is happening at this moment
with respect to physical chemistry; the founders
are hampered in their general grasp by third and
fourth decimal places; happily they are men of
robust faith. As we get to know the properties
of matter better we see that continuity reigns.
\PageSep{182}
From the work of Andrews and Van~der~Waals,
we see how the transition from the liquid to the
gaseous state is made, and that it is not abrupt.
Similarly, there is no gap between the liquid and
solid states, and in the proceedings of a recent
Congress we see memoirs on the rigidity of liquids
side by side with papers on the flow of solids.

With this tendency there is no doubt a loss of
simplicity. Such and such an effect was represented
by straight lines; it is now necessary to connect
these lines by more or less complicated curves.
On the other hand, unity is gained. Separate
categories quieted but did not satisfy the mind.

Finally, a new domain, that of chemistry, has
been invaded by the method of physics, and we see
the birth of physical chemistry. It is still quite
young, but already it has enabled us to connect
such phenomena as electrolysis, osmosis, and the
movements of ions.

From this cursory exposition what can we conclude?
Taking all things into account, we have
approached the realisation of unity. This has not
been done as quickly as was hoped fifty years ago,
and the path predicted has not always been
followed; but, on the whole, much ground has
been gained.
\PageSep{183}


\Chapter{XI.}{The Calculus of Probabilities.}

\First{No} doubt the reader will be astonished to find
reflections on the calculus of probabilities in such
a volume as this. What has that calculus to do
with physical science? The questions I shall raise---without,
however, giving them a solution---are
naturally raised by the philosopher who is examining
the problems of physics. So far is this the case,
that in the two preceding chapters I have several
times used the words ``probability'' and ``chance.''
``Predicted facts,'' as I said above, ``can only be
probable.'' However solidly founded a prediction
may appear to be, we are never absolutely
certain that experiment will not prove it false; but
the probability is often so great that practically
it may be accepted. And a little farther on I
added:---``See what a part the belief in simplicity
plays in our generalisations. We have verified a
simple law in a large number of particular cases,
and we refuse to admit that this so-often-repeated
coincidence is a mere effect of chance.'' Thus, in a
multitude of circumstances the physicist is often
in the same position as the gambler who reckons
up his chances. Every time that he reasons by
\PageSep{184}
induction, he more or less consciously requires the
calculus of probabilities, and that is why I am
obliged to open this chapter parenthetically, and to
interrupt our discussion of method in the physical
sciences in order to examine a little closer what this
calculus is worth, and what dependence we may
place upon it. The very name of the calculus of
probabilities is a paradox. Probability as opposed
to certainty is what one does not know, and how
can we calculate the unknown? Yet many eminent
scientists have devoted themselves to this calculus,
and it cannot 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 cannot,
how can we venture to reason upon it? The
definition, it will be said, is very simple. The
probability of an event is the ratio of the number
of cases favourable to the 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~6? Each can turn up in six
different ways; the number of possible cases is
$6 × 6 = 36$. The number of favourable cases is~$11$;
the probability is~$\dfrac{11}{36}$. That is the correct solution.
But why cannot we just as well proceed as follows?---The
points which turn up on the two dice form
$\dfrac{6 × 7}{2} = 21$ different combinations. Among these
combinations, six are favourable; the probability
\PageSep{185}
is~$\dfrac{6}{21}$. Now why is the first method of calculating
the number of possible cases more legitimate than
the second? In any case it is not the definition
that tells us. We are therefore bound to complete
the definition by saying, ``\ldots to the total number
of possible cases, provided the cases are equally
probable.'' So we are compelled to define the
probable by the probable. How can we know
that two possible cases are equally probable?
Will it be by a convention? If we insert at the
beginning of every problem an explicit convention,
well and good! We then have nothing to do but to
apply the rules of arithmetic and algebra, and we
complete our calculation, when our result cannot
be called in question. But if we wish to make the
slightest application of this result, we must prove
that our convention is legitimate, and we shall find
ourselves in the presence of the very difficulty we
thought we had avoided. It may be said that
common-sense is enough to show us the convention
that 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 seemed to be equally imperative in the eyes
of common-sense, and with one convention he finds~$\frac{1}{2}$,
and with the other~$\frac{1}{3}$. The conclusion which
seems to follow from this is that the calculus of
probabilities is a useless science, that the obscure
\PageSep{186}
instinct which we call common-sense, and to which
we appeal for the legitimisation of our conventions,
must be distrusted. But to this conclusion we can
no longer subscribe. We cannot do without that
obscure instinct. Without it, science would be
impossible, and without it we could neither discover
nor apply a law. Have we any right, for instance,
to enunciate Newton's law? No doubt numerous
observations are in agreement with it, but is not
that a simple fact of chance? and how do we know,
besides, that this law which has been true for so
many generations will not be untrue in the next?
To this objection the only answer you can give is:
It is very improbable. But grant the law. By
means of it I can calculate the position of Jupiter
in a year from now. Yet have I any right to say
this? Who can tell if a gigantic mass of enormous
velocity is not going to 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 only
be unconscious applications of the calculus of probabilities.
And if this calculus be condemned, then
the whole of the sciences must also be condemned.
I shall not dwell at length on 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 try
to discover the intermediary values. I may also
mention the celebrated theory of errors of observation,
\PageSep{187}
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 path, but in which, through
the effect of great numbers, the mean phenomena
which are all we observe obey the simple laws of
Mariotte and Gay-Lussac. All these theories are
based upon 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, they are sacrifices to which
we might readily be resigned. But I have said
above, it would not be 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 do not know,
and yet we must act. As for action, we have not
time to devote ourselves to an inquiry that will
suffice to dispel our ignorance. Besides, such an
inquiry would demand unlimited time. We must
therefore make up our minds without knowing.
This must be often done whatever may happen,
and we must follow the rules although we may
have but little confidence in them. What I know
is, not that 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 therefore science
itself, would be no longer of any practical value.

Unfortunately the difficulty does not thus disappear.
A gambler wants to try a \Foreign{coup}, and he
\PageSep{188}
asks my advice. If I give it him, I use the
calculus of probabilities; but I shall not guarantee
success. That is what I shall call \emph{subjective probability}.
In this case we might be content with the
explanation of which I have just given a sketch.
But assume that an observer is present at the play,
that he knows of the \Foreign{coup}, and that play goes
on for a long time, and that he makes a summary
of his notes. He will find that events have
taken place in conformity with the laws of the
calculus of probabilities. That is what I shall call
\emph{objective probability}, and it is this phenomenon
which has to be explained. There are numerous
Insurance Societies which apply the rules of the
calculus of probabilities, and they distribute to
their shareholders dividends, the objective reality
of which cannot be contested. In order to explain
them, we must do more than invoke our ignorance
and the necessity of action. Thus, absolute scepticism
is not admissible. We may distrust, but we
cannot condemn \Foreign{en~bloc}. Discussion is necessary.

\Par[I. ]{Classification of the Problems of Probability.}---In
order to classify the problems which are presented
to us with reference to probabilities, we must look at
them from different points of view, and first of all,
from that of \emph{generality}. I said above that probability
is the ratio of the number of favourable to
the number of possible cases. What for want of a
better term I call generality will increase with the
number of possible cases. This number may be
finite, as, for instance, if we take a throw of the
\PageSep{189}
dice in which the number of possible cases is~$36$.
That is the first degree of generality. But if we
ask, for instance, 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 infinite number.
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, which we reach, for instance,
when we try to find the most probable law after a
finite number of observations. Yet we may place
ourselves at a quite different point of view. If we
were not ignorant there would be no probability,
there could only be certainty. But our ignorance
cannot be absolute, for then there would be no
longer any probability at all. Thus the problems
of probability may be classed according to the
greater or less depth of this ignorance. In mathematics
we may set ourselves problems in 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
%[** TN: French edition uses a fraction]
that this probability is~\Reword{$1$-$10$th}{$\frac{1}{10}$}. Here we possess
all the data of the problem. We can calculate
our logarithm without having recourse to the
table, but we need not give ourselves the trouble.
This is the first degree of ignorance. In the
physical sciences our ignorance is already greater.
\PageSep{190}
The state of a system at a given moment 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 have a
simple mathematical problem to solve, and we
fall back upon our first degree of ignorance.
Then 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
paths and obey the laws of impact and
elastic bodies; yet as we know nothing of their
initial velocities, we know nothing of their present
velocities. The calculus of probabilities alone
enables us to predict the mean phenomena which
will result from a 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 discover 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
\PageSep{191}
from the effects. Now, these problems are classified
as \emph{probability of causes}, and are the most interesting
of all from their scientific applications. I play at
\Foreign{écarté} with a gentleman whom I know to be perfectly
honest. What is the chance that he turns
up the king? It is~$\frac{1}{8}$. 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 the king up six times. What
is the chance that he is a sharper? This is a
problem in the probability of causes. It may be
said that it 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 small divergencies are due to errors
of observation? This is the type of question that
we are 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 by discussing in succession
what I have called subjective and objective probability.

\Par[II. ]{Probability in Mathematics.}---The impossibility
of squaring the circle was shown in~1885, but
before that date all geometers considered this impossibility
as so ``probable'' that the Académie des
Sciences rejected without examination the, alas!\
\PageSep{192}
too numerous memoirs on this subject that a
few unhappy madmen sent in every year. Was
the Académie wrong? Evidently not, and it
knew perfectly well that by acting in this
manner it did not run the least risk of stifling
a discovery of moment. The Académie could
not have proved that it was right, but it knew
quite well that its instinct did not deceive it.
If you had asked the Academicians, they would
have answered: ``We have compared the probability
that an unknown scientist 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, and the latter has
appeared to us the greater.'' These are very
good reasons, but there is nothing mathematical
about them; they are purely psychological. If
you had pressed them further, they would have
added: ``Why do you expect a particular value of
a transcendental function to be an algebraical
number; if $\pi$~be the root of an algebraical equation,
why do you expect this root to be a period of
%[** TN: sin italicized in the original]
the function~$\sin 2x$, and why is it not the same
with the other roots of the same equation?'' To
sum up, they would have invoked the principle of
sufficient reason in its vaguest form. Yet what
information could they draw from it? At most a
rule of conduct for the employment of their time,
which would be more usefully spent at their
ordinary work than in reading a lucubration
that inspired in them a legitimate distrust. But
\PageSep{193}
what I called above objective probability has
nothing in common with this first problem. It is
otherwise with the second. Let us 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 say without
any hesitation that the probability is~$\frac{1}{2}$, and in
fact if you pick out in a table the third decimals
in these $10,000$ numbers you will find nearly as
many even digits as odd. Or, if you prefer it, let
us write $10,000$ numbers corresponding to our
$10,000$ logarithms, writing down for each of these
numbers $+1$~if the third decimal of the corresponding
logarithm is even, and $-1$~if odd; and then
let us take the mean of these $10,000$ numbers. I
do not hesitate to say that the mean of these
$10,000$ units is probably zero, and if I were to
calculate it practically, I would verify that it is
extremely small. But this verification is needless.
I might have rigorously proved that this mean is
smaller 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
may refer the reader to an article that I published
in the \Title{Revue générale des Sciences}, April~15th,
1899. The only point to which I wish to
draw attention is the following. In this calculation
I had occasion to rest my case on only two
facts---namely, that the first and second derivatives
of the logarithm remain, in the interval considered,
\PageSep{194}
between certain limits. Hence our first conclusion
is that the property is not only true 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 because I have often observed
analogous facts for other continuous functions; and
next, it is because I went through 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
ought to 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 that observation has confirmed my predictions,
and that the objective and subjective probabilities
are in agreement. As a third example I shall
choose the following:---The number~$u$ is taken at
random and $n$~is a given very large integer. What
is the mean value of~$\sin nu$? This problem has
no meaning by itself. To give it one, a convention
is required---namely, we agree that the probability
for the number~$u$ to lie between $a$~and~$a + da$ is
$\phi(a)\, da$; that it is therefore proportional to the
infinitely small interval~$da$, and is equal to this
multiplied by a function~$\phi(a)$, only depending
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~$2\pi$,
I may without loss of generality assume that
\PageSep{195}
$u$~lies between $0$~and~$2\pi$, and I shall thus be
led to suppose that $\phi(a)$~is a periodic function
whose period is~$2\pi$. The mean value that we
seek is readily expressed by a simple integral,
and it is easy to show that this integral is smaller
than
%[** TN: Expression displayed in the French edition]
\[
\frac{2\pi M_{K}}{n^{K}},
\]
$M_{K}$~being the maximum value of the
$K$th~derivative of~$\phi(u)$. We see then that if the
$K$th~derivative is finite, our mean value will
tend towards zero when $n$~increases indefinitely,
and that more rapidly than~$\dfrac{1}{n^{K+1}}$.

%[** TN: Paragraph break in the French edition]
The mean
value of~$\sin nu$ when $n$~is very large is therefore
zero. To define this value I required a convention,
but the result remains the same \emph{whatever
that convention may be}. I have imposed upon
myself but slight restrictions when I assumed that
the function~$\phi(a)$ 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.

\Par[III. ]{Probability in the Physical Sciences.}---We
now come to the problems which are connected
with what I have called the second degree of
\PageSep{196}
ignorance---namely, those in which we know the
law but do not know the initial state of the
system. I could multiply examples, but I shall
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 changing the nature of the problem,
suppose that their orbits are circular and situated
in the same plane, a plane which we are given.
On the other hand, we know absolutely nothing
about their initial distribution. However, we do
not hesitate to affirm that this 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 time---\ie, at the time~$t$
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 our
minor planet by a point in a plane---namely, the
point whose co-ordinates are $a$~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 the
points. Now what do we do when we apply the
calculus of probabilities to such a question as
this? 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
\PageSep{197}
compelled to make an arbitrary hypothesis. To
explain the nature of this hypothesis I may be
allowed to use, instead of a mathematical formula,
a crude but concrete image. Let us suppose
that over the surface of our plane has been
spread imaginary matter, the density of which is
variable, but varies continuously. We shall then
agree to say that the probable number of representative
points to be found on a certain portion
of the plane is proportional to the quantity of
this imaginary matter which is found there. If
there are, then, two regions of the plane of the
same extent, the probabilities that a representative
point of one of our minor planets is in one or
other of these regions will be as the mean densities
of the imaginary matter in one or other of the
regions. 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 imaginary continuous
matter. We know that the latter cannot be real,
but we are forced to adopt it through our ignorance.
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 may be nearly proportional
to the number of representative points,
or, if it is preferred, to the number of atoms which
are contained in that region. Even that is impossible,
\PageSep{198}
and our ignorance is so great that we are
forced to choose arbitrarily the function which
defines the density of our imaginary matter. We
shall be compelled to adopt 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 our
conclusion.

What is at the instant~$t$ the probable distribution
of the minor planets---or rather, what is the
mean value of the sine of the longitude at the
moment~$t$---\ie, of $\sin(at + b)$? We made at the
outset an arbitrary convention, but if we adopt it,
this probable value is entirely defined. Let us
decompose the plane into elements of surface.
Consider the value of $\sin(at + b)$ at the centre of
each of these elements. Multiply this value by the
surface of the element and by the corresponding
density of the imaginary matter. Let us then take
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~$\phi$ which defines the density of the imaginary
matter, and as this function~$\phi$ is arbitrary, we
can, according to the arbitrary choice which we
make, obtain a certain mean value. But this is
not the case. A simple calculation shows us that
our double integral decreases very rapidly as $t$~increases.
Thus, I cannot tell what hypothesis to
\PageSep{199}
make as to the probability of this or that initial
distribution, but when once the hypothesis is
made the result will be the same, and this gets
me out of my difficulty. Whatever the function~$\phi$
may be, the mean value tends towards zero
as $t$~increases, and as the minor planets have
certainly accomplished a very large number of
revolutions, I may assert that this mean value is
very small. I may give to~$\phi$ any value I choose,
with 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. What
reason could I have, for instance, for supposing
that the initial longitude might be exactly~$0°$, but
that it could not lie between $0°$~and~$1°$?

The difficulty reappears if we look at it from the
point of view of objective probability; if we pass
from our imaginary distribution in which the supposititious
matter was assumed to be continuous,
to the real distribution in which our representative
points are formed as discrete atoms. The mean
value of $\sin(at + b)$ will be represented quite
simply by
\[
\frac{1}{n} \sum \sin(at + b),
\]
$n$~being the number of minor planets. Instead of
a double integral referring to a continuous
function, we shall have a sum of discrete terms.
However, no one will seriously doubt that this
mean value is practically very small. Our representative
\PageSep{200}
points being very close together, our
discrete sum will in general differ very little from
an integral. An integral is the limit towards
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 the latter will still be true of
the sum itself. But there are exceptions. If, for
instance, for all the minor planets $b = \dfrac{\pi}{2} - at$, the
longitude of all the planets at the time~$t$ would be~$\dfrac{\pi}{2}$,
and the mean value in question would be
evidently unity. For this to be the case at the
time~$0$, the minor planets must have all been
lying on a kind of spiral of peculiar form, with
its spires very close together. All will admit that
such an initial distribution is extremely improbable
(and even if it were realised, the distribution
would not be uniform at the present time---for
example, on the 1st~January 1900; but it would
become so a few years later). Why, then, do we
think this initial distribution improbable? This
must be explained, for if we are wrong in rejecting
as improbable this absurd hypothesis, our inquiry
breaks down, and we can no longer affirm anything
on the subject of 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
\PageSep{201}
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 distribution at the present day would not
be uniform.

\Par[IV. ]{Rouge et Noir.}---The questions raised by
games of chance, such as roulette, are, fundamentally,
quite analogous to those we have just
%[** TN: "est partagé en un grand mombre de subdivisions égales"]
treated. For example, a wheel is divided into \Reword{thirty-seven}{a large number of}
equal compartments, alternately red and
black. A ball is spun round the wheel, and after
having moved round a number of times, it stops in
front of one of these sub-divisions. The probability
that the division is red is obviously~$\frac{1}{2}$. The needle
describes an angle~$\theta$, including several complete
revolutions. I do not know what is the probability
that the ball is spun with such a force that
this angle should lie between $\theta$~and~$\theta + d\theta$, but I
can make a convention. I can suppose that this
probability is~$\phi(\theta)\, d\theta$. As for the function~$\phi(\theta)$, I
can choose it in an entirely arbitrary manner. I
have nothing to guide me in my choice, but I am
naturally induced to suppose the function to be
continuous. Let $\epsilon$~be a length (measured on the
circumference of the circle of radius unity) of each
red and black compartment. We have to calculate
the integral of~$\phi(\theta)\, d\theta$, extending it on the one
hand to all the red, and on the other hand to all
\PageSep{202}
the black compartments, and to compare the
results. Consider an interval~$2\epsilon$ comprising two
consecutive red and black compartments. Let
$M$~and~$m$ be the maximum and minimum values of
the function~$\phi(\theta)$ in this interval. The integral
extended to the red compartments will be smaller
than~$\sum M\epsilon$; extended to the black it will be greater
than~$\sum m\epsilon$. The difference will therefore be
smaller than $\sum (M - m)\epsilon$. But if the function~$\phi$ is
supposed continuous, and if on the other hand the
interval~$\epsilon$ 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 be therefore very small, and the
probability will be very nearly~$\frac{1}{2}$. We see that
without knowing anything of the function~$\phi$ we
must act as if the probability were~$\frac{1}{2}$. And on
the other hand it explains why, from the
objective point of view, if I watch a certain
number of \Foreign{coups}, observation will give me almost
as many black \Foreign{coups} as red. All the players
know this objective law; but it leads them into a
remarkable error, which has often been exposed,
but into which they are always falling. When
the red has won, for example, six times running,
they bet on black, thinking that they are playing
an absolutely safe game, because they say it is
a very rare thing for the red to win seven times
running. In reality their probability of winning
is still~$\frac{1}{2}$. Observation shows, it is true, that
the series of seven consecutive reds is very rare,
\PageSep{203}
but series of six reds followed by a black are
also very 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.

\Par[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 almost on the same
visual ray, situated at very different distances
from the earth, and therefore very far indeed from
one another? or does the apparent correspond
to a real contiguity? This is a problem on the
probability of causes.

First of all, I recall that at the outset of all
problems of probability of effects that have
occupied our attention up to now, we have had
to use a convention which was more or less
justified; and if in most cases the result was to
a certain extent independent of this convention,
it was only the condition of certain hypotheses
which enabled us \Foreign{à~priori} to reject discontinuous
functions, for example, or certain absurd conventions.
We shall again find something
analogous to this 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
\PageSep{204}
that it is due to the cause~$a$. This is an \Foreign{à~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 \Foreign{à~priori}
probability for the cause~$a$ to come into play---I
mean the probability of this event to some one
who had not observed the effect. To make my
meaning clearer, I go back to the game of \Foreign{écarté}
mentioned before. My adversary deals for the
first time and turns up a king. What is the
probability that he is a sharper? The formulæ
ordinarily taught give~$\frac{8}{9}$, a result which is
obviously rather surprising. If we look at it
closer, we see that the conclusion is arrived at
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 certainly
not have played with him; and this explains the
absurdity of the conclusion. The function on
the \Foreign{à~priori} probability was unjustified, and that
is why the conclusion of the \Foreign{à~posteriori} probability
led me into an inadmissible result. The importance
of this preliminary convention is obvious.
I shall even add that if none were made, the
problem of the \Foreign{à~posteriori} probability would have
no meaning. It must be always made either
explicitly or tacitly.

Let us pass on to an example of a more
scientific character. I require to determine an
experimental law; this law, when discovered, can
\PageSep{205}
be represented by a curve. I make a certain
number of isolated observations, each of which
may be represented by a point. When I have
obtained these different points, I draw a curve
between them as carefully as possible, giving
my curve a regular form, avoiding sharp angles,
accentuated inflexions, and any sudden variation
of the radius of curvature. This curve will represent
to me the probable law, and not only will
it give me the values of the functions intermediary
to those which have been observed, but it also
gives me the observed values more accurately
than direct observation does; that is why I make
the curve pass near the points and not through
the points themselves.

Here, then, is a problem in the probability of
causes. The effects are the measurements I have
recorded; they depend on the combination of two
causes---the true law of the phenomenon and errors
of observation. Knowing the effects, we have to
find the probability that the phenomenon shall
obey this law or that, and that the observations
have been accompanied by this or that error.
The most probable law, therefore, corresponds to
the curve we have traced, and the most probable
error is represented by the distance of the corresponding
point from that curve. But the
problem has no meaning if before the observations
I had an \Foreign{à~priori} idea of the probability of
this law or that, or of the chances of error to
which I am exposed. If my instruments are
\PageSep{206}
good (and I knew whether this is so or not before
beginning the observations), I shall not draw the
curve far from the points which represent the
rough measurements. If they are inferior, I may
draw it a little farther from the points, so that I
may get a less sinuous curve; much will be sacrificed
to regularity.

Why, then, do I draw a curve without sinuosities?
Because I consider \Foreign{à~priori} a law
represented by a continuous function (or function
the derivatives of which to a high order are small),
as more probable than a law not satisfying those
conditions. But for this conviction the problem
would have no meaning; interpolation would be
impossible; no law could be deduced from a
finite number of observations; science would
cease to exist.

Fifty years ago physicists considered, other
things being equal, a simple law as more probable
than a complicated law. This principle was even
invoked in favour of Mariotte's law as against
that of Regnault. But this belief is now
repudiated; and yet, how many times are we
compelled to act as though we still held it!
However that may be, what remains of this
tendency is the belief in continuity, and as we
have just seen, if the belief in continuity were
to disappear, experimental science would become
impossible.

\Par[VI. ]{The Theory of Errors.}---We are thus brought
to consider the theory of errors which is directly
\PageSep{207}
connected with the problem of the probability
of causes. Here again we find \emph{effects}---to wit,
a certain number of irreconcilable observations,
and we try to find the \emph{causes} which are, on the
one hand, the true value of the quantity to be
measured, and, on the other, the error made in
each isolated observation. We must calculate
the probable \Foreign{à~posteriori} value of each error, and
therefore the probable value of the quantity to be
measured. But, as I have just explained, we
cannot undertake this calculation unless we admit
\Foreign{à~priori}---\ie, before any observations are made---that
there is a law of the probability of errors.
Is there a law of errors? The law to which
all calculators assent is Gauss's law, that is
represented by a certain transcendental curve
known as the ``bell.''

But it is first of all necessary to recall
the classic distinction between systematic and
accidental errors. If the metre with which we
measure a length is too long, the number we get
will be too small, and it will be no use to measure
several times---that is a systematic error. If we
measure with an accurate metre, we may make a
mistake, and find the length sometimes too large
and sometimes too small, and when we take the
mean of a large number of measurements,
the error will tend to grow small. These are
accidental errors.

It is clear that systematic errors do not satisfy
Gauss's law, but do accidental errors satisfy it?
\PageSep{208}
Numerous proofs have been attempted, almost all
of them crude paralogisms. But starting from
the following hypotheses we may prove Gauss's
law: the error is the result of a very large number
of partial and independent errors; each partial
error is very small and obeys any law of probability
whatever, provided the probability of a
positive error is the same as that of an equal
negative error. It is clear 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, physicists
are more distrustful of it than astronomers. This
is no doubt because the latter, apart from the
systematic errors to which they and the physicists
are subject alike, have to contend with an
extremely important source of error which is
entirely accidental---I mean atmospheric undulations.
So it is very curious to hear a discussion
between a physicist and an astronomer about a
method of observation. The physicist, persuaded
that one good measurement is worth more than
many bad ones, is pre-eminently concerned with
the elimination by means of every precaution of
the final systematic errors; the astronomer retorts:
``But you can only observe a small number of stars,
and accidental errors will not disappear.''

What conclusion must we draw? Must we
continue to use the method of least squares?
\PageSep{209}
We must distinguish. We have eliminated all
the systematic errors of which we have any
suspicion; we are quite certain that there are
others still, but we cannot detect them; and yet
we must make up our minds and adopt a definitive
value which will be regarded as the probable
value; and for that purpose it is clear that the
best thing we can do is to apply Gauss's law.
We have only applied a practical rule referring
to subjective probability. And there is no more
to be said.

Yet we want to go farther and say that not
only the probable value is so much, but that the
probable error in the result is so much. \emph{This
is absolutely invalid}: 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 law 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 more accurate than the first, because the
first is perhaps affected by a large systematic
error. All that we can say is, that the first series
is \emph{probably} better than the second because its
accidental error is smaller, and that we have no
reason for affirming that the systematic error is
greater for one of the series than for the other,
our ignorance on this point being absolute.

\Par[VII. ]{Conclusions.}---In the preceding lines I have
set several problems, and have given no solution.
\PageSep{210}
I do not regret this, for perhaps they will invite
the reader to reflect on these delicate questions.

However that may be, there are certain points
which seem to be well established. To undertake
the calculation of any probability, and even for
that calculation to have any meaning at all, we
must admit, as a point of departure, an 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
assume different forms. The form under which
we meet 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.
\PageSep{211}


\Chapter{XII.\protect\footnotemark}{Optics And Electricity.}
\footnotetext{This chapter is mainly taken from the prefaces of two of my
  books---\Title{Théorie Mathématique de la lumière} (Paris: Naud, 1889),
  and \Title{Électricité et Optique} (Paris: Naud, 1901).}

\Par{Fresnel's Theory.}---The best example that can be
chosen is the theory of light and its relations
to the theory of electricity. It is owing to Fresnel
that the science of optics is more advanced than
any other branch of physics. The theory called the
theory of undulations forms a complete whole,
which is satisfying to the mind; but we must
not ask from it what it cannot give us. The
object of mathematical theories is not to reveal
to us the real nature of things; that would be
an unreasonable claim. Their only object is to
co-ordinate the physical laws with which physical
experiment makes us acquainted, the enunciation
of which, without the aid of mathematics, we
should be unable to effect. Whether the ether
exists or not matters little---let us leave that to
the metaphysicians; what is essential for us is, that
everything happens as if it existed, and that this
hypothesis is found to be suitable for the explanation
of phenomena. After all, have we any other
\PageSep{212}
reason for believing in the existence of material
objects? That, too, is only a convenient hypothesis;
only, it will never cease to be so, while some day,
no doubt, the ether will be thrown aside as useless.

But at the present moment the laws of optics,
and the equations which translate them into the
language of analysis, hold good---at least as a first
approximation. It will therefore be always useful
to study a theory which brings these equations
into connection.

The undulatory theory is based on a molecular
hypothesis; this is an advantage to those who
think they can discover the cause under the law.
But others find in it a reason for distrust; and
this distrust seems to me as unfounded as the
illusions of the former. These hypotheses play
but a secondary rôle. They may be sacrificed,
and the sole reason why this is not generally done
is, that it would involve a certain loss of lucidity
in the explanation. In fact, if we look at it a
little closer we shall see that we borrow from
molecular hypotheses but two things---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 the conclusions of Fresnel
remain unchanged when we adopt the electro-magnetic
theory of light.

\Par{Maxwell's Theory.}---We all know that it was
Maxwell who connected by a slender tie two
branches of physics---optics and electricity---until
\PageSep{213}
then unsuspected of having anything in common.
Thus blended in a larger aggregate, in a higher
harmony, Fresnel's theory of optics did not perish.
Parts of it are yet alive, and their mutual relations
are still the same. Only, the language which we
use to express them has changed; and, on the
other hand, Maxwell has revealed to us other
relations, hitherto unsuspected, between the
different branches of optics and the domain of
electricity.

\Pagelabel{213}%
The first time a French reader opens Maxwell's
book, his admiration is tempered with a feeling of
uneasiness, and often of distrust.

It is only after prolonged study, and at the cost
of much effort, that this feeling disappears. Some
minds of high calibre never lose this feeling. Why
is it so difficult for the ideas of this English
scientist to become acclimatised among us? No
doubt the education received by most enlightened
Frenchmen predisposes them to appreciate precision
and logic more than any other qualities.
In this respect the old theories of mathematical
physics gave us complete satisfaction. All our
masters, from Laplace to Cauchy, proceeded along
the same lines. Starting with clearly enunciated
hypotheses, they deduced from them all their
consequences with mathematical rigour, and then
compared them with experiment. It seemed to
be their aim to give to each of the branches
of physics the same precision as to celestial
mechanics.
\PageSep{214}

A mind accustomed to admire such models is
not easily satisfied with a theory. Not only will
it not tolerate the least appearance of contradiction,
but it will expect the different parts to be
logically connected with one another, and will
require the number of hypotheses to be reduced
to a minimum.

This is not all; there will be other demands
which appear to me to be less reasonable. Behind
the matter of which our senses are aware, and
which is made known to us by experiment, such
a thinker will expect to see another kind of matter---the
only true matter in its opinion---which will
no longer have anything but purely geometrical
qualities, and the atoms of which will be mathematical
points subject to the laws of dynamics
alone. And yet he will try to represent to
himself, by an unconscious contradiction, these
invisible and colourless atoms, and therefore
to bring them as close as possible to ordinary
matter.

Then only will he be thoroughly satisfied, and
he will then imagine that he has penetrated the
secret of the universe. Even if the satisfaction is
fallacious, it is none the less difficult to give it up.
Thus, on opening the pages of Maxwell, a Frenchman
expects to find a theoretical whole, as logical
and as precise as the physical optics that is founded
on the hypothesis of the ether. He is thus preparing
for himself a disappointment which I
should like the reader to avoid; so I will warn
\PageSep{215}
him at once of what he will find and what he will
not find in Maxwell.

Maxwell does not give a mechanical explanation
of electricity and magnetism; he confines himself
to showing that such an explanation is possible.
He shows that the phenomena of optics are only
a particular case of electro-magnetic phenomena.
From the whole theory of electricity a theory of
light can be immediately deduced. Unfortunately
the converse is not true; it is not always easy to
find a complete explanation of electrical phenomena.
In particular it is not easy if we take
as our starting-point Fresnel's theory; to do so,
no doubt, would be impossible; but none the less
we must ask ourselves if we are compelled to
surrender admirable results which we thought we
had definitively acquired. That seems a step
backwards, and many sound intellects will not
willingly allow of this.

Should the reader consent to set some bounds
to his hopes, he will still come across other
difficulties. The English scientist does not try
to erect a unique, definitive, and well-arranged
building; he seems to raise rather a large number
of provisional and independent constructions,
between which communication is difficult and
sometimes impossible. Take, for instance, the
chapter in which \Chg{electrostatic}{electro-static} attractions are
explained by the pressures and tensions of the
dielectric medium. This chapter might be suppressed
without the rest of the book being
\PageSep{216}
thereby less clear or less complete, and yet
it contains a theory which is self-sufficient, and
which can be understood without reading a
word of what precedes or follows. But it is
not only independent of the rest of the book; it
is difficult to reconcile it with the fundamental
ideas of the volume. Maxwell does not even
attempt to reconcile it; 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 be sufficient to show what
I mean; I could quote many others. Thus, who
would suspect on reading the pages devoted to
magnetic rotatory polarisation that there is an
identity between optical and magnetic phenomena?

We must not flatter ourselves that we have
avoided every contradiction, but we ought to
make up our minds. Two contradictory theories,
provided that they are kept from overlapping, and
that we do not look to find in them the explanation
of things, may, in fact, be very 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 ways.
But the fundamental idea is masked, as it were.
So far is this the case, that in most works that are
popularised, this idea is the only point which is
left completely untouched. To show the importance
of this, I think I ought to explain in what this
\PageSep{217}
fundamental idea consists; but for that purpose
a short digression is necessary.

\Par{The Mechanical Explanation of Physical Phenomena.}---In
every physical phenomenon there is a certain
number of parameters which are reached directly
by experiment, and which can be measured. I
shall call them the parameters~$q$. Observation
next teaches us the laws of the variations of these
parameters, and these laws can be generally stated
in the form of differential equations which connect
together the parameters~$q$ and time. What can
be done to give a mechanical interpretation to
such a phenomenon? We may endeavour to
explain it, either by the movements of ordinary
matter, or by those of one or more hypothetical
fluids. These fluids will be considered as formed
of a very large number of isolated molecules~$m$.
When may we say that we have a complete
mechanical explanation of the phenomenon? It
will be, on the one hand, when we know the
differential equations which are satisfied by the
co-ordinates of these hypothetical molecules~$m$,
equations which must, in addition, conform to the
laws of dynamics; and, on the other hand, when we
know the relations which define the co-ordinates
of the molecules~$m$ as functions of the parameters~$q$,
attainable by experiment. These equations, as
I have said, should conform to the principles of
dynamics, and, in particular, to the principle of
the conservation of energy, and to that of least
action.
\PageSep{218}

The first of these two principles teaches us that
the total energy is constant, and may be divided
into two parts:\Add{---}

(1) Kinetic energy, or \Foreign{vis~viva}, which depends
on the masses of the hypothetical molecules~$m$,
and on their velocities. This I shall call~$T$. (2)~The
potential energy which depends only on the
co-ordinates of these molecules, and this I shall
call~$U$. It is the sum of the energies $T$~and~$U$ that
is constant.

Now what are we taught by the principle of
least action? It teaches us that to pass from the
initial position occupied at the instant~$t_{0}$ to
the final position occupied at the instant~$t_{1}$, the
system must describe such a path that in the
interval of time between the instant $t_{0}$~and~$t_{1}$,
the mean value of the action---\ie, the \emph{difference}
between the two energies $T$~and~$U$, must be as
small as possible. The first of these two principles
is, moreover, a consequence of the second. If we
know the functions $T$~and~$U$, this second principle
is sufficient to determine the equations of motion.

Among the paths which enable us to pass from
one position to another, there is clearly one for
which the mean value of the action is smaller than
for all the others. In addition, there is only\Typo{ }{ one} such
path; and it follows from this, that the principle
of least action is sufficient to determine the path
followed, and therefore the equations of motion.
We thus obtain what are called the equations of
Lagrange. In these equations the independent
\PageSep{219}
variables are the co-ordinates of the hypothetical
molecules~$m$; but I now assume that we take for
the variables the parameters~$q$, which are directly
accessible to experiment.

The two parts of the energy should then be
expressed as a function of the parameters~$q$ and
their derivatives; it is clear that it is under this
form that they will appear to the experimenter.
The latter will naturally endeavour to define
kinetic and potential energy by the aid of
quantities he can directly observe.\footnote
  {We may add that $U$ will depend only on the $q$~parameters, that
  $T$~will depend on them and their derivatives with respect to time,
  and will be a homogeneous polynomial of the second degree with
  respect to these derivatives.}
If this be
granted, the system will always proceed from one
position to another by such a path that the mean
value of the action is 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 the aid of these
parameters that we define the initial and \Typo{fina}{final}
positions; the principle of least action will always
remain true.

Now here again, of the whole of the paths which
lead from one position to another, there is one and
only one for which the mean action is a minimum.
The principle of least action is therefore sufficient
for the determination of the differential equations
which define the variations of the parameters~$q$.
The equations thus obtained are another form of
Lagrange's equations.
\PageSep{220}

To form these equations we need not know the
relations which connect the parameters~$q$ with the
co-ordinates of the hypothetical molecules, nor the
masses of the molecules, nor the expression of~$U$
as a function of the co-ordinates of these molecules.
All we need know is the expression of~$U$ as a
function of the parameters~$q$, and that of~$T$ as a
function of the parameters~$q$ and their derivatives---\ie,
the expressions of the kinetic and potential
energy in terms of experimental data.

One of two things must now happen. Either for
a convenient choice of $T$~and~$U$ the Lagrangian
equations, constructed as we have indicated, will
be identical with the differential equations deduced
from experiment, or there will be no functions $T$~and~$U$
for which this identity takes place. In the
latter case it is clear that no mechanical explanation
is possible. The \emph{necessary} condition for a
mechanical explanation to be possible is therefore
this: that we may choose the functions $T$~and~$U$ so
as to satisfy the principle of least action, and of the
conservation of energy. Besides, this condition is
\emph{sufficient}. Suppose, in fact, that we have found a
function~$U$ of the parameters~$q$, which represents
one of the parts of energy, and that the part of the
energy which we represent by~$T$ is a function of
the parameters~$q$ and their derivatives; that it
is a polynomial of the second degree with respect
to its derivatives, and finally that the Lagrangian
equations formed by the aid of these two functions
$T$~and~$U$ are in conformity with the data of the
\PageSep{221}
experiment. How can we deduce from this a
mechanical explanation? $U$~must be regarded as
the potential energy of a system of which $T$~is the
kinetic energy. There is no difficulty as far as $U$~is
concerned, but can $T$ be regarded as the \Foreign{vis~viva}
of a material system?

It is easily shown that this is always possible,
and in an unlimited number of ways. I will be
content with referring the reader to the pages of
the preface of my \Title{Électricité et Optique} for further
details. Thus, if the principle of least action
cannot be satisfied, no mechanical explanation is
possible; if it can be satisfied, there is not only one
explanation, but an unlimited number, whence it
follows that since there is one there must be an
unlimited number.

One more remark. Among the quantities that
may be reached by experiment directly we shall
consider some as the co-ordinates of our hypothetical
molecules, some will be our parameters~$q$,
and the rest will be regarded as dependent not
only on the co-ordinates but on the velocities---or
what comes to the same thing, we look on them as
derivatives of the parameters~$q$, or as combinations
of these parameters and their derivatives.

Here then a question occurs: among all these
quantities measured experimentally which shall we
choose to represent the parameters~$q$? and which
shall we prefer to regard as the derivatives of these
parameters? This choice remains arbitrary to a
large extent, but a mechanical explanation will be
\PageSep{222}
possible if it is done so as to satisfy the principle of
least action.

Next, Maxwell asks: Can this choice and that of
the two energies $T$~and~$U$ be made so that electric
phenomena will satisfy this principle? Experiment
shows us that the energy of an electro-magnetic
field decomposes into electro-static and electro-dynamic
energy. Maxwell recognised that if we
regard the former as the potential energy~$U$, and
the latter as the kinetic energy~$T$, and that if on
the other hand we take the electro-static charges
of the conductors as the parameters~$q$, and the intensity
of the currents as derivatives of other
parameters~$q$---under these conditions, Maxwell
has recognised that electric phenomena \Reword{satisfies}{satisfy} the
principle of least action. He was then certain of
a mechanical explanation. If he had expounded
this theory at the beginning of his first volume,
instead of relegating it to a corner of the second, it
would not have escaped the attention of most
readers. If therefore a phenomenon allows of a
complete mechanical explanation, it allows of an
unlimited number of others, which will equally take
into account 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 polarisation; Neumann holds that it is
parallel to that plane. For a long time an \Foreign{experimentum
crucis} was sought for, which would enable
us to decide between these two theories, but in
\PageSep{223}
vain. In the same way, without going out of the
domain of electricity, we find that the theory of
two fluids and the single fluid theory equally
account in a satisfactory manner for all the laws
of electro-statics. All these facts are easily explained,
thanks to the properties of the Lagrange
equations.

\Pagelabel{223}%
It is easy now to understand Maxwell's fundamental
idea. To demonstrate the possibility of a
mechanical explanation of electricity we need not
trouble to find the explanation itself; we need only
know the expression of the two functions $T$~and~$U$,
which are the two parts of energy, and to form with
these two functions Lagrange's equations, and
then to compare these equations with the experimental
laws.

How shall we choose from all the possible
explanations one in which the help of experiment
will be wanting? The day will perhaps come
when physicists will no longer concern themselves
with questions which are inaccessible to positive
methods, and will leave them to the metaphysicians.
That day has not yet come; man does not
so easily resign himself to remaining for ever ignorant
of the causes of things. Our choice cannot be
therefore any longer guided by considerations in
which personal appreciation plays too large a part.
There are, however, solutions which all will reject
because of their fantastic nature, and others which
all will prefer because of their simplicity. As
far as magnetism and electricity are concerned,
\PageSep{224}
Maxwell abstained from making any choice. It is
not that he has a systematic contempt for all that
positive methods cannot reach, as may be seen
from the time he has devoted to the kinetic theory
of gases. I may add that if in his \Foreign{magnum opus} he
develops no complete explanation, he has attempted
one in an article in the \Title{Philosophical Magazine}.
The strangeness and the complexity of the
hypotheses he found himself compelled to make,
led him afterwards to withdraw it.

The same spirit is found throughout his whole
work. He throws into relief the essential---\ie,
what is common to all theories; everything that
suits only a particular theory is passed over almost
in silence. The reader therefore finds himself in
the presence of form nearly devoid of matter,
which at first he is tempted to take as a fugitive
and unassailable phantom. But the efforts he is
thus compelled to make force him to think, and
eventually he sees that there is often something
rather artificial in the theoretical ``aggregates''
which he once admired.
\Pagelabel{224}%
\PageSep{225}


\Chapter{XIII.}{Electro-Dynamics.}

\First{The} history of electro-dynamics is very instructive
from our point of view. The title of Ampère's
immortal work is, \Title{Théorie des phénomènes electro-dynamiques,
uniquement fondée sur expérience}. He
therefore imagined that he had made no hypotheses;
but as we shall not be long in recognising, he was
mistaken; only, of these hypotheses he was quite
unaware. On the other hand, his successors see
them clearly enough, because their attention is
attracted by the weak points in Ampère's solution.
They made fresh hypotheses, but this time
deliberately. How many times they had to change
them before they reached the classic system, which
is perhaps even now not quite definitive, we shall
see.

\Par[I. ]{Ampère's Theory.}---In Ampère's experimental
study of the mutual action of currents, he has
operated, and he could operate only, with closed
currents. This was not because he denied the
existence or possibility of open currents. If two
conductors are positively and negatively charged
and brought into communication by a wire, a
current is set up which passes from one to the
\PageSep{226}
other until the two potentials are equal. According
to the ideas of Ampère's time, this was
considered to be an open current; the current was
known to pass from the first conductor to the
second, but they did not know it returned from the
second to the first. All currents of this kind were
therefore considered by Ampère to be open
currents---for instance, the currents of discharge
of a condenser; he was unable to experiment on
them, their duration being too short. Another
kind of open current may be imagined. Suppose
we have two conductors $A$~and~$B$ connected by a
wire~$AMB$. Small conducting masses in motion
are first of all placed in contact with the conductor~$B$,
receive an electric charge, and leaving~$B$ are
set in motion along a path~$BNA$, carrying their
charge with them. On coming into contact with~$A$
they lose their charge, which then returns to~$B$
along the wire~$AMB$. Now here we have, in a
sense, a closed circuit, since the electricity describes
the closed circuit~$BNAMB$; but the two parts of
the current are quite different. In the wire~$AMB$
the electricity is displaced \emph{through} a fixed conductor
like a voltaic current, overcoming an ohmic resistance
and developing heat; we say that it is
displaced by \emph{conduction}. In the part~$BNA$ the
electricity is \emph{carried} by a moving conductor, and is
said to be displaced by \emph{convection}. If therefore the
convection current is considered to be perfectly
analogous to the conduction current, the circuit~$BNAMB$
is closed; if on the contrary the convection
\PageSep{227}
current is not a ``true current,'' and, for
instance, does not act on the magnet, there is only
the conduction current~$AMB$, which is \emph{open}. For
example, if we connect by a wire the 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 kind are
very difficult to produce with appreciable intensity;
in fact, with the means at Ampère's disposal we
may almost say it was impossible.

To sum up, Ampère could conceive of the existence
of two kinds of open currents, but he could
experiment 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 current, because a current can be
made to describe a \emph{closed} circuit, of which part may
be in motion and the other part fixed. The displacements
of the moving part may be studied 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 or on another
open current.

\Par[1.\ ]{The Case of Closed Currents.}---In the case of
the mutual action of two closed currents, experiment
revealed to Ampère remarkably simple
laws. The following will be useful to us in the
sequel:---
\PageSep{228}

(1) \emph{If the intensity of the currents is kept constant},
and if the two circuits, after having undergone any
displacements and deformations whatever, return
finally to their initial positions, the total work
done by the electro-dynamical actions is zero. In
other words, there is an \emph{electro-dynamical potential}
of the two circuits proportional to the product of
their intensities, and depending on the form and
relative positions of the circuits; the work done
by the electro-dynamical actions is equal to the
change of this potential.

(2) The action of a closed solenoid is zero.

(3) The action of a circuit~$C$ on another voltaic
circuit~$C'$ depends only on the ``magnetic field''
developed by the circuit~$C$. 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:---

(\textit{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 the pole.

(\textit{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
product of the magnetic force, the magnetic
moment of the needle, and the sine of the dip
of the needle.

(\textit{c}) If the circuit~$C'$ is displaced, the amount of
the work done by the electro-dynamic action of~$C$
on~$C'$ will be equal to the increment of ``flow
\PageSep{229}
of magnetic force'' which passes through the
circuit.

\Par[2.\ ]{Action of a Closed Current on a Portion of
Current.}---Ampère being unable to produce the
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, one movable
and the other fixed. The movable part was,
for instance, a movable wire~$\alpha\beta$, the ends $\alpha$~and~$\beta$
of which could slide along a fixed wire. In one of
the positions of the movable wire the end~$\alpha$ rested
on the point~$A$, and the end~$\beta$ on the point~$B$ of
the fixed wire. The current ran from~$\alpha$ to~$\beta$---\ie,
from~$A$ to~$B$ along the movable wire, and then
from~$B$ to~$A$ along the fixed wire. \emph{This current
was therefore closed.}

In the second position, the movable wire
having slipped, the points $\alpha$~and~$\beta$ were respectively
at $A'$~and~$B'$ on the fixed wire. The current
ran from~$\alpha$ to~$\beta$---\ie, from~$A'$ to~$B'$ on the movable
wire, and returned from~$B'$ to~$B$, and
then from~$B$ to~$A$, and then from~$A$ to~$A'$---all on
the fixed wire. This current was also closed.
If a similar circuit be exposed to the action of a
closed current~$C$, the movable part will be displaced
just as if it were acted on by a force.
Ampère \emph{admits} that the force, apparently acting on
the movable part~$AB$, representing the action of~$C$
on the portion~$\alpha\beta$ of the current, remains the
same whether an open current runs through~$\alpha\beta$,
\PageSep{230}
stopping at $\alpha$~and~$\beta$, or whether a closed current
runs first to~$\beta$ and then returns to~$\alpha$ through the
fixed portion of the circuit. This hypothesis
seemed natural enough, and Ampère innocently
assumed it; nevertheless the hypothesis \emph{is not a
necessity}, for we shall presently see that Helmholtz
rejected it. However that may be, it enabled
Ampère, although he had never produced an open
current, to lay down the laws of the action of a
closed current on an open current, or even on an
element of current. They are simple:\Add{---}

(1) The force acting on an element of current
is applied to that element; it is normal to the
element and to the magnetic force, and proportional
to that component of the magnetic force
which is normal to the element.

(2) The action of a closed solenoid on an
element of current is zero. But the electro-dynamic
potential has disappeared---\ie, when a
closed and an open current of constant intensities
return to their initial positions, the total work
done is not zero.

\Par[3.\ ]{Continuous Rotations.}---The most remarkable
electro-dynamical experiments are those in which
continuous rotations are produced, and which are
called \emph{unipolar induction} experiments. A magnet
may turn about its axis; a current passes first
through a fixed wire and then enters the magnet
by the pole~$N$, for instance, passes through
half the magnet, and emerges by a sliding contact
and re-enters the fixed wire. The magnet
\PageSep{231}
then begins to rotate continuously. This is
Faraday's experiment. How is it possible? If it
were a question of two circuits of invariable form,
$C$~fixed and $C'$~movable about an axis, the latter
would never take up a position of continuous
rotation; in fact, there is an electro-dynamical
potential; there must therefore be a position of
equilibrium when the potential is a maximum.
Continuous rotations are therefore possible only
when the circuit~$C'$ is composed of two parts---one
fixed, and the other movable about an axis,
as in the case of Faraday's experiment. Here
again it is convenient to draw a distinction. The
passage from the fixed to the movable part, or
\Foreign{vice~versâ}, 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 sliding contact, the same point of
the movable part coming successively into contact
with the different 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 up a position
of equilibrium; but, when at the point of reaching
that position, the sliding contact puts the moving
part in contact with a fresh point in the fixed
part; it changes the connexions and therefore the
conditions of equilibrium, so that as the position
of equilibrium is ever eluding, so to speak, the
system which is trying to reach it, rotation may
take place indefinitely.
\PageSep{232}

Ampère admits 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
an open current. He concluded that the action of
a closed on an open current, or \Foreign{vice~versâ}, that of
an open current on a fixed current, may give rise
to continuous rotation. But this conclusion
depends on the hypothesis which I have enunciated,
and to which, as I said above, Helmholtz
declined to subscribe.

\Par[4.\ ]{Mutual Action of Two Open Currents.}---As far
as the mutual action of two open currents, and in
particular that of two elements of current, is
concerned, all experiment breaks down. Ampère
falls back on hypothesis. He assumes: (1)~that
the mutual action of two elements reduces to a
force acting along their \emph{join}; (2)~that the action
of two closed currents is the resultant of the
mutual actions of their different elements, which
are the same as if these elements were isolated.

The remarkable thing is that here again Ampère
makes two hypotheses without being aware of it.
However that may be, these two hypotheses,
together with the experiments on closed currents,
suffice to determine completely the law of 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 electro-dynamical potential; nor was
there any, as we have seen, in the case of a closed
\PageSep{233}
current acting on an open current. Next, there
is, properly speaking, no magnetic force; and we
have above defined this force in three different
ways: (1)~By the action on a magnetic pole;
(2)~by the director couple which orientates the
magnetic needle; (3)~by the action on an element
of current.

In the case with which we are immediately
concerned, not only are these three definitions not
in harmony, but each has lost its meaning:---

(1) A magnetic pole is no longer acted on by a
unique force applied to that pole. We have seen,
in fact, 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.

(2) 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 zero. It decomposes into a director couple,
properly so called, and a supplementary couple
which tends to produce the continuous rotation of
which we have spoken above.

(3) Finally, the force acting on an element of
a current is not normal to that element. In
other words, \emph{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 also exercise the same action on an
indefinitely small magnetic needle, or on an element
\PageSep{234}
of current placed at the point in space at which the
pole is. Well, this is true if the two systems only
contain closed currents, and according to Ampère
it would not be true if the systems contained open
currents. It is sufficient to remark, for instance,
that if a magnetic pole is placed at~$A$ and an
element at~$B$, the direction of the element being
in~$AB$ produced, this element, which will exercise
no action on the pole, will exercise an action
either on a magnetic needle placed at~$A$, or on
an element of current at~$A$.

\Par[5.\ ]{Induction.}---We know that the discovery of
electro-dynamical induction followed not long after
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 us to deduce the laws of induction
from the electro-dynamical laws of Ampère. But
on the condition, as Bertrand has shown,---that
we make a certain number of hypotheses.

The same principle again enables this deduction
to be made in the case of open currents, although
the result cannot be tested by experiment, since
such currents cannot be produced.

If we wish to compare this method of analysis
with Ampère's theorem on open currents, we get
results which are calculated to surprise us. In
the first place, induction cannot be deduced from
the variation of the magnetic field by the well-known
formula of scientists and practical men;
\PageSep{235}
in fact, as I have said, properly speaking, there
is no magnetic field. But further, if a circuit~$C$
is subjected to the induction of a variable voltaic
system~$S$, and 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, then so long
as after these variations the system eventually
returns to its initial position, it seems natural
to suppose that the \emph{mean} electro-motive force
%[** TN: "induite dans le circuit C est nulle" in the French edition.]
induced in the \Reword{current}{circuit}~$C$ is zero. This is true if
the circuit~$C$ is closed, and if the system~$S$ only
contains closed currents. It is no longer true if
we accept the theory of Ampère, since there would
be open currents. So that not only will induction
no longer be the variation of the flow of magnetic
force in any of the usual senses of the word, but
it cannot be represented by the variation of that
force whatever it may be.

\Par[II. ]{Helmholtz's Theory.}---I have dwelt upon the
consequences of Ampère's theory and on his
method of explaining the action of open currents.
It is difficult to disregard the paradoxical and
artificial character of the propositions to which
we are thus led. We feel bound to think ``it
cannot be so.'' We may imagine then that
Helmholtz has been led to look for something
else. He rejects the fundamental hypothesis of
Ampère---namely, that the mutual action of two
elements of current reduces to a force along their
join. He admits that an clement of current is not
\PageSep{236}
acted upon by a single force but by a force and a
couple, and this is what gave rise to the celebrated
polemic between Bertrand and Helmholtz.
Helmholtz replaces Ampère's hypothesis by the
following:---Two elements of current always
admit of an electro-dynamic potential, depending
solely upon 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 do so without explicitly announcing it. In
the case of closed currents, which alone are
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 that acting
on the movable portion if it were isolated and
if it constituted an open current. Let us return
to the circuit~$C'$, of which we spoke above, and
which was formed of a movable wire sliding on
a fixed wire. In the only experiment that can be
made the movable portion~$\alpha\beta$ is not isolated, but is
part of a closed circuit. When it passes from~$AB$
to~$A'B'$, the total electro-dynamic potential
varies for two reasons. First, it has a slight increment
because the potential of~$A'B'$ with respect
to the circuit~$C$ is not the same as that of~$AB$;
secondly, it has a second increment because it
must be increased by the potentials of the elements
\PageSep{237}
$AA'$~and~$B'B$ with respect to~$C$. It is this \emph{double}
increment which represents the work of the force
acting upon the portion~$AB$. If, on the contrary,
$\alpha\beta$~be isolated, the potential would only have the
first increment, and this first increment alone
would measure the work of the force acting on~$AB$.
In the second place, there could be no
continuous rotation without sliding contact, and
in fact, that, as we have seen in the case of closed
currents, is an immediate consequence of the
existence of an electro-dynamic potential. In
Faraday's experiment, if the magnet is fixed,
and if the part of the current external to the
magnet runs along a movable wire, that movable
wire may undergo continuous rotation. But it
does not mean that, if the contacts of the \Typo{weir}{wire}
with the magnet were suppressed, and an open
current were to run along the wire, the wire
would still have a movement of continuous rotation.
I have just said, in fact, that an isolated
element is not acted on in the same way as a
movable element making part of a closed circuit.
But there is another difference. The action of a
solenoid on a closed current is zero according to
experiment and according to the two theories.
Its action on an open current would be zero
according to Ampère, and it would not be
zero according to Helmholtz. From this follows
an important consequence. We have given above
three definitions of the magnetic force. The third
has no meaning here, since an element of current
\PageSep{238}
is no longer acted upon by a single force. Nor
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,
the action exercised by an open current on
an indefinite solenoid would only depend on the
position of the extremity of that solenoid---\ie,
that the action of a closed solenoid is zero. Now
we have just seen that this is not the case. On
the other hand, there is nothing to prevent us
from 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 electro-dynamic effects will
depend solely on the distribution of the lines
of force in this magnetic field.

\Par[III. ]{Difficulties raised by these Theories.}---Helmholtz's
theory is an advance on that of Ampère;
it is necessary, however, that every difficulty
should be removed. In both, the name ``magnetic
field'' has no meaning, or, if we give it one by a
more or less artificial convention, the ordinary
laws so familiar to electricians no longer apply;
and it is thus that the electro-motive force induced
in a wire is no longer measured by the number
of lines of force met by that wire. And our
objections do not proceed only from the fact that
it is difficult to give up deeply-rooted habits of
\PageSep{239}
language and thought. There is something more.
If we do not believe in actions at a distance,
electro-dynamic phenomena must be explained by
a modification of the medium. And this medium
is precisely what we call ``magnetic field,'' and
then the electro-magnetic effects should only
depend on that field. All these difficulties arise
from the hypothesis of open currents.

\Par[IV. ]{Maxwell's Theory.}---Such were the difficulties
raised by the current theories, when Maxwell with
a stroke of the pen caused them to vanish. To
his mind, in fact, all currents are closed currents.
Maxwell admits 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 called the \emph{current
of displacement}. If, then, two conductors bearing
positive and negative charges are placed in connection
by means of a wire, during the discharge
there is an open current of conduction in that
wire; 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
period such a conception was only a daring hypothesis
which could be supported by no experiment;
but after twenty years Maxwell's ideas received the
confirmation of experiment. Hertz succeeded in
producing systems of electric oscillations which
\PageSep{240}
reproduce all the properties of light, and only
differ by the length of their wave---that is to say,
as violet differs from red. In some measure he
made a synthesis of light. It might be said that
Hertz has not directly proved Maxwell's fundamental
idea of the action of the current of
displacement on the galvanometer. That is true
in a sense. What he has shown directly is that
electro-magnetic induction is not instantaneously
propagated, as was supposed, but its speed is the
speed of light. Yet, to suppose there is no current
of displacement, and that induction is with the
speed of light; or, rather, to suppose that the
currents of displacement produce inductive effects,
and that the induction takes place instantaneously---\emph{comes
to the same thing}. This cannot be seen at
the first glance, but it is proved by an analysis
of which I must not even think of giving even a
summary here.

\Par[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 cases in which the electric charges
describe a closed contour, being displaced by conduction
in one part of the circuit and by convection
in the other part. The question might be
regarded as solved for open currents of the first
kind; they were closed by currents of displacement.
For open currents of the second kind the
solution appeared still more simple.
\PageSep{241}

It seemed that if the current were closed it
could only be by the current of convection itself.
For that purpose it was sufficient to admit that a
``convection current''---\ie, 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 increasing as much as possible the charge
and the velocity of the conductors. Rowland, an
extremely skilful experimentalist, was the first to
triumph, or to seem to triumph, over these difficulties.
A disc received a strong \Chg{electrostatic}{electro-static}
charge and a very high speed of rotation. An
astatic magnetic system placed beside the disc
underwent deviations. The experiment was made
twice by Rowland, once in Berlin and once at Baltimore.
It was afterwards repeated by Himstedt.
These physicists even believed that they could
announce that they had succeeded in making
quantitative measurements. For twenty years
Rowland's law was admitted without objection
by all physicists, and, indeed, everything seemed
to confirm it. The spark certainly does produce a
magnetic effect, and does it not seem extremely
likely that the spark discharged 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
recognise the lines of the metal of the electrode,
a proof of it? The spark would then be a real
current of induction.
\PageSep{242}

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 also be a current of convection; but it
acts on the magnetic needle. And in the same
way for cathode rays; \Typo{Crooks}{Crookes} attributed these
rays to very subtle matter charged with negative
electricity and moving with very high velocity.
He looked upon 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 \Chg{re-action}{reaction}, they should in
their turn deviate the magnetic needle. It is
true that Hertz believed he had proved that the
cathodic rays do not carry negative electricity, and
that they do not act on the magnetic needle; but
Hertz was wrong. 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 the effects due to the action of the X-rays,
which were not yet discovered. Afterwards, and
quite recently, the action of the cathodic rays on
the magnetic needle has been brought to light.
Thus all these phenomena looked upon as currents
of convection, electric sparks, electrolytic currents,
cathodic rays, act in the same manner on the
galvanometer and in conformity to Rowland's
law.

\Par[VI. ]{Lorentz's Theory.}---We need not go much
further. According to Lorentz's theory, currents
\PageSep{243}
of conduction would themselves be true convection
currents. Electricity would remain indissolubly
connected with certain material particles called
\emph{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 check
the movement of the electrons. Lorentz's theory
is very attractive. It gives a very simple explanation
of certain phenomena, which the earlier
theories---even Maxwell's in its primitive form---could
only deal with in an unsatisfactory manner;
for example, the aberration of light, the partial
impulse of luminous waves, magnetic polarisation,
and Zeeman's experiment.

A few objections still remained. The phenomena
of an electric system seemed to depend on
the absolute velocity of translation of the centre
of gravity of this system, which is contrary to
the idea that we have of the relativity of space.
Supported by M.~Crémieu, M.~Lippman has presented
this objection in a very 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
\PageSep{244}
absolute velocity, but their relative velocity \emph{with
respect to the ether}, so that the principle of relativity
is safe.'' Whatever there may be in these
objections, the edifice of electro-dynamics seemed,
at any rate in its broad lines, definitively constructed.
Everything was presented under the
most satisfactory aspect. The theories of Ampère
and Helmholtz, which were made for the open
currents that no longer existed, seem to have no
more than purely historic interest, and the inextricable
complications to which these theories
led have been almost forgotten. This quiescence
has been recently disturbed by the experiments of
M.~Crémieu, which have contradicted, or at least
have seemed to contradict, the results formerly
obtained by Rowland. Numerous investigators
have endeavoured to solve the question, and fresh
experiments have been undertaken. What result
will they give? I shall take care not to risk a
prophecy which might be falsified between the
day this book is ready for the press and the day on
which it is placed before the public.
\begin{center}
\vfill
\footnotesize THE END.
\vfill\vfill
\rule{1in}{0.5pt} \\[4pt]
\makebox[0pt][c]{\scriptsize THE WALTER SCOTT PUBLISHING CO., LIMITED, FELLING-ON-TYNE.}
\end{center}

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