OF THE LIMITS TO THE EXPLANATION OF LAWS OF NATURE; AND OF HYPOTHESES.
§ 1. The preceding considerations have led us to recognise a distinction
between two kinds of laws, or observed uniformities in nature: ultimate
laws, and what may be termed derivative laws. Derivative laws are such
as are deducible from, and may, in any of the modes which we have
pointed out, be resolved into, other and more general ones. Ultimate
laws are those which cannot. We are not sure that any of the
uniformities with which we are yet acquainted are ultimate laws; but we
know that there must be ultimate laws; and that every resolution of a
derivative law into more general laws, brings us nearer to them.
Since we are continually discovering that uniformities, not previously
known to be other than ultimate, are derivative, and resolvable into
more general laws; since (in other words) we are continually discovering
the explanation of some sequence which was previously known only as a
fact; it becomes an interesting question whether there are any necessary
limits to this philosophical operation, or whether it may proceed until
all the uniform sequences in nature are resolved into some one universal
law. For this seems, at first sight, to be the ultimatum towards which
the progress of induction, by the Deductive Method resting on a basis of
observation and experiment, is tending. Projects of this kind were
universal in the infancy of philosophy; any speculations which held out
a less brilliant prospect, being in those early times deemed not worth
pursuing. And the idea receives so much apparent countenance from the
nature of the most remarkable achievements of modern science, that
speculators are even now frequently appearing, who profess either to
have solved the problem, or to suggest modes in which it may one day be
solved. Even where pretensions of this magnitude are not made, the
character of the solutions which are given or sought of particular
classes of phenomena, often involves such conceptions of what
constitutes explanation, as would render the notion of explaining all
phenomena whatever by means of some one cause or law, perfectly
admissible.
§ 2. It is therefore useful to remark, that the ultimate Laws of Nature
cannot possibly be less numerous than the distinguishable sensations or
other feelings of our nature;--those, I mean, which are distinguishable
from one another in quality, and not merely in quantity or degree. For
example; since there is a phenomenon _sui generis_, called colour, which
our consciousness testifies to be not a particular degree of some other
phenomenon, as heat or odour or motion, but intrinsically unlike all
others, it follows that there are ultimate laws of colour; that though
the facts of colour may admit of explanation, they never can be
explained from laws of heat or odour alone, or of motion alone, but that
however far the explanation may be carried, there will always remain in
it a law of colour. I do not mean that it might not possibly be shown
that some other phenomenon, some chemical or mechanical action for
example, invariably precedes, and is the cause of, every phenomenon of
colour. But though this, if proved, would be an important extension of
our knowledge of nature, it would not explain how or why a motion, or a
chemical action, can produce a sensation of colour; and however diligent
might be our scrutiny of the phenomena, whatever number of hidden links
we might detect in the chain of causation terminating in the colour, the
last link would still be a law of colour, not a law of motion, nor of
any other phenomenon whatever. Nor does this observation apply only to
colour, as compared with any other of the great classes of sensations;
it applies to every particular colour, as compared with others. White
colour can in no manner be explained exclusively by the laws of the
production of red colour. In any attempt to explain it, we cannot but
introduce, as one element of the explanation, the proposition that some
antecedent or other produces the sensation of white.
The ideal limit, therefore, of the explanation of natural phenomena
(towards which as towards other ideal limits we are constantly tending,
without the prospect of ever completely attaining it) would be to show
that each distinguishable variety of our sensations, or other states of
consciousness, has only one sort of cause; that, for example, whenever
we perceive a white colour, there is some one condition or set of
conditions which is always present, and the presence of which always
produces in us that sensation. As long as there are several known modes
of production of a phenomenon, (several different substances, for
instance, which have the property of whiteness, and between which we
cannot trace any other resemblance,) so long it is not impossible that
one of these modes of production may be resolved into another, or that
all of them may be resolved into some more general mode of production
not hitherto recognised. But when the modes of production are reduced to
one, we cannot, in point of simplification, go any further. This one may
not, after all, be the ultimate mode; there may be other links to be
discovered between the supposed cause and the effect; but we can only
further resolve the known law, by introducing some other law hitherto
unknown; which will not diminish the number of ultimate laws.
In what cases, accordingly, has science been most successful in
explaining phenomena, by resolving their complex laws into laws of
greater simplicity and generality? Hitherto chiefly in cases of the
propagation of various phenomena through space: and, first and
principally, the most extensive and important of all facts of that
description, the fact of motion. Now this is exactly what might be
expected from the principles here laid down. Not only is motion one of
the most universal of all phenomena, it is also (as might be expected
from that circumstance) one of those which, apparently at least, are
produced in the greatest number of ways; but the phenomenon itself is
always, to our sensations, the same in every respect but degree.
Differences of duration, or of velocity, are evidently differences in
degree only; and differences of direction in space, which alone has any
semblance of being a distinction in kind, entirely disappear (so far as
our sensations are concerned) by a change in our own position; indeed
the very same motion appears to us, according to our position, to take
place in every variety of direction, and motions in every different
direction to take place in the same. And again, motion in a straight
line and in a curve are no otherwise distinct than that the one is
motion continuing in the same direction, the other is motion which at
each instant changes its direction. There is, therefore, according to
the principles I have stated, no absurdity in supposing that all motion
may be produced in one and the same way; by the same kind of cause.
Accordingly, the greatest achievements in physical science have
consisted in resolving one observed law of the production of motion into
the laws of other known modes of production, or the laws of several such
modes into one more general mode; as when the fall of bodies to the
earth, and the motions of the planets, were brought under the one law of
the mutual attraction of all particles of matter; when the motions said
to be produced by magnetism were shown to be produced by electricity;
when the motions of fluids in a lateral direction, or even contrary to
the direction of gravity, were shown to be produced by gravity; and the
like. There is an abundance of distinct causes of motion still
unresolved into one another; gravitation, heat, electricity, chemical
action, nervous action, and so forth; but whether the efforts of the
present generation of savans to resolve all these different modes of
production into one, are ultimately successful or not, the attempt so to
resolve them is perfectly legitimate. For though these various causes
produce, in other respects, sensations intrinsically different, and are
not, therefore, capable of being resolved into one another, yet in so
far as they all produce motion, it is quite possible that the immediate
antecedent of the motion may in all these different cases be the same;
nor is it impossible that these various agencies themselves may, as the
new doctrines assert, all of them have for their own immediate
antecedent, modes of molecular motion.
We need not extend our illustration to other cases, as for instance to
the propagation of light, sound, heat, electricity, &c. through space,
or any of the other phenomena which have been found susceptible of
explanation by the resolution of their observed laws into more general
laws. Enough has been said to display the difference between the kind of
explanation and resolution of laws which is chimerical, and that of
which the accomplishment is the great aim of science; and to show into
what sort of elements the resolution must be effected, if at all.
§ 3. As, however, there is scarcely any one of the principles of a true
method of philosophizing which does not require to be guarded against
errors on both sides, I must enter a caveat against another
misapprehension, of a kind directly contrary to the preceding. M. Comte,
among other occasions on which he has condemned, with some asperity, any
attempt to explain phenomena which are "evidently primordial," (meaning,
apparently, no more than that every peculiar phenomenon must have at
least one peculiar and therefore inexplicable law,) has spoken of the
attempt to furnish any explanation of the colour belonging to each
substance, "la couleur élémentaire propre à chaque substance," as
essentially illusory. "No one," says he, "in our time attempts to
explain the particular specific gravity of each substance or of each
structure. Why should it be otherwise as to the specific colour, the
notion of which is undoubtedly no less primordial?"[1]
Now although, as he elsewhere observes, a colour must always remain a
different thing from a weight or a sound, varieties of colour might
nevertheless follow, or correspond to, given varieties of weight, or
sound, or some other phenomenon as different as these are from colour
itself. It is one question what a thing is, and another what it depends
on; and though to ascertain the conditions of an elementary phenomenon
is not to obtain any new insight into the nature of the phenomenon
itself, that is no reason against attempting to discover the conditions.
The interdict against endeavouring to reduce distinctions of colour to
any common principle, would have held equally good against a like
attempt on the subject of distinctions of sound; which nevertheless have
been found to be immediately preceded and caused by distinguishable
varieties in the vibrations of elastic bodies: though a sound, no doubt,
is quite as different as a colour is from any motion of particles,
vibratory or otherwise. We might add, that, in the case of colours,
there are strong positive indications that they are not ultimate
properties of the different kinds of substances, but depend on
conditions capable of being superinduced upon all substances; since
there is no substance which cannot, according to the kind of light
thrown upon it, be made to assume almost any colour; and since almost
every change in the mode of aggregation of the particles of the same
substance, is attended with alterations in its colour, and in its
optical properties generally.
The real defect in the attempts which have been made to account for
colours by the vibrations of a fluid, is not that the attempt itself is
unphilosophical, but that the existence of the fluid, and the fact of
its vibratory motion, are not proved; but are assumed, on no other
ground than the facility they are supposed to afford of explaining the
phenomena. And this consideration leads to the important question of the
proper use of scientific hypotheses; the connexion of which with the
subject of the explanation of the phenomena of nature, and of the
necessary limits to that explanation, needs not be pointed out.
§ 4. An hypothesis is any supposition which we make (either without
actual evidence, or on evidence avowedly insufficient) in order to
endeavour to deduce from it conclusions in accordance with facts which
are known to be real; under the idea that if the conclusions to which
the hypothesis leads are known truths, the hypothesis itself either must
be, or at least is likely to be, true. If the hypothesis relates to the
cause, or mode of production of a phenomenon, it will serve, if
admitted, to explain such facts as are found capable of being deduced
from it. And this explanation is the purpose of many, if not most,
hypotheses. Since explaining, in the scientific sense, means resolving
an uniformity which is not a law of causation, into the laws of
causation from which it results, or a complex law of causation into
simpler and more general ones from which it is capable of being
deductively inferred; if there do not exist any known laws which fulfil
this requirement, we may feign or imagine some which would fulfil it;
and this is making an hypothesis.
An hypothesis being a mere supposition, there are no other limits to
hypotheses than those of the human imagination; we may, if we please,
imagine, by way of accounting for an effect, some cause of a kind
utterly unknown, and acting according to a law altogether fictitious.
But as hypotheses of this sort would not have any of the plausibility
belonging to those which ally themselves by analogy with known laws of
nature, and besides would not supply the want which arbitrary hypotheses
are generally invented to satisfy, by enabling the imagination to
represent to itself an obscure phenomenon in a familiar light; there is
probably no hypothesis in the history of science in which both the agent
itself and the law of its operation were fictitious. Either the
phenomenon assigned as the cause is real, but the law according to which
it acts, merely supposed; or the cause is fictitious, but is supposed to
produce its effects according to laws similar to those of some known
class of phenomena. An instance of the first kind is afforded by the
different suppositions made respecting the law of the planetary central
force, anterior to the discovery of the true law, that the force varies
as the inverse square of the distance; which also suggested itself to
Newton, in the first instance, as an hypothesis, and was verified by
proving that it led deductively to Kepler's laws. Hypotheses of the
second kind are such as the vortices of Descartes, which were
fictitious, but were supposed to obey the known laws of rotatory motion;
or the two rival hypotheses respecting the nature of light, the one
ascribing the phenomena to a fluid emitted from all luminous bodies, the
other (now generally received) attributing them to vibratory motions
among the particles of an ether pervading all space. Of the existence of
either fluid there is no evidence, save the explanation they are
calculated to afford of some of the phenomena; but they are supposed to
produce their effects according to known laws; the ordinary laws of
continued locomotion in the one case, and in the other, those of the
propagation of undulatory movements among the particles of an elastic
fluid.
According to the foregoing remarks, hypotheses are invented to enable
the Deductive Method to be earlier applied to phenomena. But[2] in order
to discover the cause of any phenomenon by the Deductive Method, the
process must consist of three parts; induction, ratiocination, and
verification. Induction, (the place of which, however, may be supplied
by a prior deduction,) to ascertain the laws of the causes;
ratiocination, to compute from those laws, how the causes will operate
in the particular combination known to exist in the case in hand;
verification, by comparing this calculated effect with the actual
phenomenon. No one of these three parts of the process can be dispensed
with. In the deduction which proves the identity of gravity with the
central force of the solar system, all the three are found. First, it is
proved from the moon's motions, that the earth attracts her with a force
varying as the inverse square of the distance. This (though partly
dependent on prior deductions) corresponds to the first, or purely
inductive, step, the ascertainment of the law of the cause. Secondly,
from this law, and from the knowledge previously obtained of the moon's
mean distance from the earth, and of the actual amount of her deflexion
from the tangent, it is ascertained with what rapidity the earth's
attraction would cause the moon to fall, if she were no further off, and
no more acted upon by extraneous forces, than terrestrial bodies are:
that is the second step, the ratiocination. Finally, this calculated
velocity being compared with the observed velocity with which all heavy
bodies fall, by mere gravity, towards the surface of the earth, (sixteen
feet in the first second, forty-eight in the second, and so forth, in
the ratio of the odd numbers, 1, 3, 5, &c.,) the two quantities are
found to agree. The order in which the steps are here presented, was not
that of their discovery; but it is their correct logical order, as
portions of the proof that the same attraction of the earth which causes
the moon's motion, causes also the fall of heavy bodies to the earth: a
proof which is thus complete in all its parts.
Now, the Hypothetical Method suppresses the first of the three steps,
the induction to ascertain the law; and contents itself with the other
two operations, ratiocination and verification; the law which is
reasoned from, being assumed, instead of proved.
This process may evidently be legitimate on one supposition, namely, if
the nature of the case be such that the final step, the verification,
shall amount to, and fulfil the conditions of, a complete induction. We
want to be assured that the law we have hypothetically assumed is a true
one; and its leading deductively to true results will afford this
assurance, provided the case be such that a false law cannot lead to a
true result; provided no law, except the very one which we have assumed,
can lead deductively to the same conclusions which that leads to. And
this proviso is often realized. For example, in the very complete
specimen of deduction which we just cited, the original major premise of
the ratiocination, the law of the attractive force, was ascertained in
this mode; by this legitimate employment of the Hypothetical Method.
Newton began by an assumption, that the force which at each instant
deflects a planet from its rectilineal course, and makes it describe a
curve round the sun, is a force tending directly towards the sun. He
then proved that if this be so, the planet will describe, as we know by
Kepler's first law that it does describe, equal areas in equal times;
and, lastly, he proved that if the force acted in any other direction
whatever, the planet would not describe equal areas in equal times. It
being thus shown that no other hypothesis would accord with the facts,
the assumption was proved; the hypothesis became an inductive truth. Not
only did Newton ascertain by this hypothetical process the direction of
the deflecting force; he proceeded in exactly the same manner to
ascertain the law of variation of the quantity of that force. He assumed
that the force varied inversely as the square of the distance; showed
that from this assumption the remaining two of Kepler's laws might be
deduced; and finally, that any other law of variation would give results
inconsistent with those laws, and inconsistent, therefore, with the real
motions of the planets, of which Kepler's laws were known to be a
correct expression.
I have said that in this case the verification fulfils the conditions of
an induction: but an induction of what sort? On examination we find that
it conforms to the canon of the Method of Difference. It affords the two
instances, A B C, _a b c_, and B C, _b c_. A represents central force; A
B C, the planets _plus_ a central force; B C, the planets apart from a
central force. The planets with a central force give _a_, areas
proportional to the times; the planets without a central force give _b
c_ (a set of motions) without _a_, or with something else instead of
_a_. This is the Method of Difference in all its strictness. It is true,
the two instances which the method requires are obtained in this case,
not by experiment, but by a prior deduction. But that is of no
consequence. It is immaterial what is the nature of the evidence from
which we derive the assurance that A B C will produce _a b c_, and B C
only _b c_; it is enough that we have that assurance. In the present
case, a process of reasoning furnished Newton with the very instances,
which, if the nature of the case had admitted of it, he would have
sought by experiment.
It is thus perfectly possible, and indeed is a very common occurrence,
that what was an hypothesis at the beginning of the inquiry, becomes a
proved law of nature before its close. But in order that this should
happen, we must be able, either by deduction or experiment, to obtain
_both_ the instances which the Method of Difference requires. That we
are able from the hypothesis to deduce the known facts, gives only the
affirmative instance, A B C, _a b c_. It is equally necessary that we
should be able to obtain, as Newton did, the negative instance B C, _b
c_; by showing that no antecedent, except the one assumed in the
hypothesis, would in conjunction with B C produce _a_.
Now it appears to me that this assurance cannot be obtained, when the
cause assumed in the hypothesis is an unknown cause, imagined solely to
account for _a_. When we are only seeking to determine the precise law
of a cause already ascertained, or to distinguish the particular agent
which is in fact the cause, among several agents of the same kind, one
or other of which it is already known to be, we may then obtain the
negative instance. An inquiry, which of the bodies of the solar system
causes by its attraction some particular irregularity in the orbit or
periodic time of some satellite or comet, would be a case of the second
description. Newton's was a case of the first. If it had not been
previously known that the planets were hindered from moving in straight
lines by some force tending towards the interior of their orbit, though
the exact direction was doubtful; or if it had not been known that the
force increased in some proportion or other as the distance diminished,
and diminished as it increased; Newton's argument would not have proved
his conclusion. These facts, however, being already certain, the range
of admissible suppositions was limited to the various possible
directions of a line, and the various possible numerical relations
between the variations of the distance, and the variations of the
attractive force: now among these it was easily shown that different
suppositions could not lead to identical consequences.
Accordingly, Newton could not have performed his second great scientific
operation, that of identifying terrestrial gravity with the central
force of the solar system, by the same hypothetical method. When the law
of the moon's attraction had been proved from the data of the moon
itself, then on finding the same law to accord with the phenomena of
terrestrial gravity, he was warranted in adopting it as the law of those
phenomena likewise; but it would not have been allowable for him,
without any lunar data, to assume that the moon was attracted towards
the earth with a force as the inverse square of the distance, merely
because that ratio would enable him to account for terrestrial gravity:
for it would have been impossible for him to prove that the observed law
of the fall of heavy bodies to the earth could not result from any
force, save one extending to the moon, and proportional to the inverse
square.
It appears, then, to be a condition of a genuinely scientific
hypothesis, that it be not destined always to remain an hypothesis, but
be of such a nature as to be either proved or disproved by comparison
with observed facts. This condition is fulfilled when the effect is
already known to depend on the very cause supposed, and the hypothesis
relates only to the precise mode of dependence; the law of the variation
of the effect according to the variations in the quantity or in the
relations of the cause. With these may be classed the hypotheses which
do not make any supposition with regard to causation, but only with
regard to the law of correspondence between facts which accompany each
other in their variations, though there may be no relation of cause and
effect between them. Such were the different false hypotheses which
Kepler made respecting the law of the refraction of light. It was known
that the direction of the line of refraction varied with every variation
in the direction of the line of incidence, but it was not known how;
that is, what changes of the one corresponded to the different changes
of the other. In this case any law, different from the true one, must
have led to false results. And, lastly, we must add to these, all
hypothetical modes of merely representing, or _describing_, phenomena;
such as the hypothesis of the ancient astronomers that the heavenly
bodies moved in circles; the various hypotheses of excentrics,
deferents, and epicycles, which were added to that original hypothesis;
the nineteen false hypotheses which Kepler made and abandoned respecting
the form of the planetary orbits; and even the doctrine in which he
finally rested, that those orbits are ellipses, which was but an
hypothesis like the rest until verified by facts.
In all these cases, verification is proof; if the supposition accords
with the phenomena there needs no other evidence of it. But in order
that this may be the case, I conceive it to be necessary, when the
hypothesis relates to causation, that the supposed cause should not only
be a real phenomenon, something actually existing in nature, but should
be already known to exercise, or at least to be capable of exercising,
an influence of some sort over the effect. In any other case, it is no
evidence of the truth of the hypothesis that we are able to deduce the
real phenomena from it.
Is it, then, never allowable, in a scientific hypothesis, to assume a
cause; but only to ascribe an assumed law to a known cause? I do not
assert this. I only say, that in the latter case alone can the
hypothesis be received as true merely because it explains the phenomena:
in the former case it is only useful by suggesting a line of
investigation which may possibly terminate in obtaining real proof. For
this purpose, as is justly remarked by M. Comte, it is indispensable
that the cause suggested by the hypothesis should be in its own nature
susceptible of being proved by other evidence. This seems to be the
philosophical import of Newton's maxim, (so often cited with approbation
by subsequent writers,) that the cause assigned for any phenomenon must
not only be such as if admitted would explain the phenomenon, but must
also be a _vera causa_. What he meant by a _vera causa_ Newton did not
indeed very explicitly define; and Dr. Whewell, who dissents from the
propriety of any such restriction upon the latitude of framing
hypotheses, has had little difficulty in showing[3] that his conception
of it was neither precise nor consistent with itself: accordingly his
optical theory was a signal instance of the violation of his own rule.
It is certainly not necessary that the cause assigned should be a cause
already known; else how could we ever become acquainted with any new
cause? But what is true in the maxim is, that the cause, though not
known previously, should be capable of being known thereafter; that its
existence should be capable of being detected, and its connexion with
the effect ascribed to it should be susceptible of being proved, by
independent evidence. The hypothesis, by suggesting observations and
experiments, puts us on the road to that independent evidence if it be
really attainable; and till it be attained, the hypothesis ought not to
count for more than a conjecture.
§ 5. This function, however, of hypotheses, is one which must be
reckoned absolutely indispensable in science. When Newton said,
"Hypotheses non fingo," he did not mean that he deprived himself of the
facilities of investigation afforded by assuming in the first instance
what he hoped ultimately to be able to prove. Without such assumptions,
science could never have attained its present state: they are necessary
steps in the progress to something more certain; and nearly everything
which is now theory was once hypothesis. Even in purely experimental
science, some inducement is necessary for trying one experiment rather
than another; and though it is abstractedly possible that all the
experiments which have been tried, might have been produced by the mere
desire to ascertain what would happen in certain circumstances, without
any previous conjecture as to the result; yet, in point of fact, those
unobvious, delicate, and often cumbrous and tedious processes of
experiment, which have thrown most light upon the general constitution
of nature, would hardly ever have been undertaken by the persons or at
the time they were, unless it had seemed to depend on them whether some
general doctrine or theory which had been suggested, but not yet proved,
should be admitted or not. If this be true even of merely experimental
inquiry, the conversion of experimental into deductive truths could
still less have been effected without large temporary assistance from
hypotheses. The process of tracing regularity in any complicated, and at
first sight confused set of appearances, is necessarily tentative: we
begin by making any supposition, even a false one, to see what
consequences will follow from it; and by observing how these differ from
the real phenomena, we learn what corrections to make in our assumption.
The simplest supposition which accords with the more obvious facts, is
the best to begin with; because its consequences are the most easily
traced. This rude hypothesis is then rudely corrected, and the operation
repeated; and the comparison of the consequences deducible from the
corrected hypothesis, with the observed facts, suggests still further
correction, until the deductive results are at last made to tally with
the phenomena. "Some fact is as yet little understood, or some law is
unknown: we frame on the subject an hypothesis as accordant as possible
with the whole of the data already possessed; and the science, being
thus enabled to move forward freely, always ends by leading to new
consequences capable of observation, which either confirm or refute,
unequivocally, the first supposition." Neither induction nor deduction
would enable us to understand even the simplest phenomena, "if we did
not often commence by anticipating on the results; by making a
provisional supposition, at first essentially conjectural, as to some of
the very notions which constitute the final object of the inquiry."[4]
Let any one watch the manner in which he himself unravels a complicated
mass of evidence; let him observe how, for instance, he elicits the true
history of any occurrence from the involved statements of one or of many
witnesses: he will find that he does not take all the items of evidence
into his mind at once, and attempt to weave them together: he
extemporises, from a few of the particulars, a first rude theory of the
mode in which the facts took place, and then looks at the other
statements one by one, to try whether they can be reconciled with that
provisional theory, or what alterations or additions it requires to make
it square with them. In this way, which has been justly compared to the
Methods of Approximation of mathematicians, we arrive, by means of
hypotheses, at conclusions not hypothetical.[5]
§ 6. It is perfectly consistent with the spirit of the method, to
assume in this provisional manner not only an hypothesis respecting the
law of what we already know to be the cause, but an hypothesis
respecting the cause itself. It is allowable, useful, and often even
necessary, to begin by asking ourselves what cause _may_ have produced
the effect, in order that we may know in what direction to look out for
evidence to determine whether it actually _did_. The vortices of
Descartes would have been a perfectly legitimate hypothesis, if it had
been possible, by any mode of exploration which we could entertain the
hope of ever possessing, to bring the reality of the vortices, as a fact
in nature, conclusively to the test of observation. The hypothesis was
vicious, simply because it could not lead to any course of investigation
capable of converting it from an hypothesis into a proved fact. It might
chance to be _dis_proved, either by some want of correspondence with the
phenomena it purported to explain, or (as actually happened) by some
extraneous fact. "The free passage of comets through the spaces in which
these vortices should have been, convinced men that these vortices did
not exist."[6] But the hypothesis would have been false, though no such
direct evidence of its falsity had been procurable. Direct evidence of
its truth there could not be.
The prevailing hypothesis of a luminiferous ether, in other respects not
without analogy to that of Descartes, is not in its own nature entirely
cut off from the possibility of direct evidence in its favour. It is
well known that the difference between the calculated and the observed
times of the periodical return of Encke's comet, has led to a conjecture
that a medium capable of opposing resistance to motion is diffused
through space. If this surmise should be confirmed, in the course of
ages, by the gradual accumulation of a similar variance in the case of
the other bodies of the solar system, the luminiferous ether would have
made a considerable advance towards the character of a _vera causa_,
since the existence would have been ascertained of a great cosmical
agent, possessing some of the attributes which the hypothesis assumes;
though there would still remain many difficulties, and the
identification of the ether with the resisting medium would even, I
imagine, give rise to new ones. At present, however, this supposition
cannot be looked upon as more than a conjecture; the existence of the
ether still rests on the possibility of deducing from its assumed laws a
considerable number of the phenomena of light; and this evidence I
cannot regard as conclusive, because we cannot have, in the case of such
an hypothesis, the assurance that if the hypothesis be false it must
lead to results at variance with the true facts.
Accordingly, most thinkers of any degree of sobriety allow, that an
hypothesis of this kind is not to be received as probably true because
it accounts for all the known phenomena; since this is a condition
sometimes fulfilled tolerably well by two conflicting hypotheses; while
there are probably a thousand more which are equally possible, but
which, for want of anything analogous in our experience, our minds are
unfitted to conceive. But it seems to be thought that an hypothesis of
the sort in question is entitled to a more favourable reception, if,
besides accounting for all the facts previously known, it has led to the
anticipation and prediction of others which experience afterwards
verified; as the undulatory theory of light led to the prediction,
subsequently realized by experiment, that two luminous rays might meet
each other in such a manner as to produce darkness. Such predictions and
their fulfilment are, indeed, well calculated to impress the uninformed,
whose faith in science rests solely on similar coincidences between its
prophecies and what comes to pass. But it is strange that any
considerable stress should be laid upon such a coincidence by persons of
scientific attainments. If the laws of the propagation of light accord
with those of the vibrations of an elastic fluid in as many respects as
is necessary to make the hypothesis afford a correct expression of all
or most of the phenomena known at the time, it is nothing strange that
they should accord with each other in one respect more. Though twenty
such coincidences should occur, they would not prove the reality of the
undulatory ether; it would not follow that the phenomena of light were
results of the laws of elastic fluids, but at most that they are
governed by laws partially identical with these; which, we may observe,
is already certain, from the fact that the hypothesis in question could
be for a moment tenable.[7] Cases may be cited, even in our imperfect
acquaintance with nature, where agencies that we have good reason to
consider as radically distinct, produce their effects, or some of their
effects, according to laws which are identical. The law, for example, of
the inverse square of the distance, is the measure of the intensity not
only of gravitation, but (it is believed) of illumination, and of heat
diffused from a centre. Yet no one looks upon this identity as proving
similarity in the mechanism by which the three kinds of phenomena are
produced.
According to Dr. Whewell, the coincidence of results predicted from an
hypothesis, with facts afterwards observed, amounts to a conclusive
proof of the truth of the theory. "If I copy a long series of letters,
of which the last half dozen are concealed, and if I guess these aright,
as is found to be the case when they are afterwards uncovered, this must
be because I have made out the import of the inscription. To say, that
because I have copied all that I could see, it is nothing strange that I
should guess those which I cannot see, would be absurd, without
supposing such a ground for guessing."[8] If any one, from examining the
greater part of a long inscription, can interpret the characters so that
the inscription gives a rational meaning in a known language, there is a
strong presumption that his interpretation is correct; but I do not
think the presumption much increased by his being able to guess the few
remaining letters without seeing them: for we should naturally expect
(when the nature of the case excludes chance) that even an erroneous
interpretation which accorded with all the visible parts of the
inscription would accord also with the small remainder; as would be the
case, for example, if the inscription had been designedly so contrived
as to admit of a double sense. I assume that the uncovered characters
afford an amount of coincidence too great to be merely casual: otherwise
the illustration is not a fair one. No one supposes the agreement with
the phenomena of light with the theory of undulations to be merely
fortuitous. It must arise from the actual identity of some of the laws
of undulations with some of those of light: and if there be that
identity, it is reasonable to suppose that its consequences would not
end with the phenomena which first suggested the identification, nor be
even confined to such phenomena as were known at the time. But it does
not follow, because some of the laws agree with those of undulations,
that there are any actual undulations; no more than it followed because
some (though not so many) of the same laws agreed with those of the
projection of particles, that there was actual emission of particles.
Even the undulatory hypothesis does not account for all the phenomena of
light. The natural colours of objects, the compound nature of the solar
ray, the absorption of light, and its chemical and vital action, the
hypothesis leaves as mysterious as it found them; and some of these
facts are, at least apparently, more reconcileable with the emission
theory than with that of Young and Fresnel. Who knows but that some
third hypothesis, including all these phenomena, may in time leave the
undulatory theory as far behind as that has left the theory of Newton
and his successors?
To the statement, that the condition of accounting for all the known
phenomena is often fulfilled equally well by two conflicting hypotheses,
Dr. Whewell makes answer that he knows "of no such case in the history
of science, where the phenomena are at all numerous and complicated."[9]
Such an affirmation, by a writer of Dr. Whewell's minute acquaintance
with the history of science, would carry great authority, if he had
not, a few pages before, taken pains to refute it,[10] by maintaining
that even the exploded scientific hypotheses might always, or almost
always, have been so modified as to make them correct representations of
the phenomena. The hypothesis of vortices, he tells us, was, by
successive modifications, brought to coincide in its results with the
Newtonian theory and with the facts. The vortices did not indeed explain
all the phenomena which the Newtonian theory was ultimately found to
account for, such as the precession of the equinoxes; but this
phenomenon was not, at the time, in the contemplation of either party,
as one of the facts to be accounted for. All the facts which they did
contemplate, we may believe on Dr. Whewell's authority to have accorded
as accurately with the Cartesian hypothesis, in its finally improved
state, as with Newton's.
But it is not, I conceive, a valid reason for accepting any given
hypothesis, that we are unable to imagine any other which will account
for the facts. There is no necessity for supposing that the true
explanation must be one which, with only our present experience, we
could imagine. Among the natural agents with which we are acquainted,
the vibrations of an elastic fluid may be the only one whose laws bear a
close resemblance to those of light; but we cannot tell that there does
not exist an unknown cause, other than an elastic ether diffused through
space, yet producing effects identical in some respects with those which
would result from the undulations of such an ether. To assume that no
such cause can exist, appears to me an extreme case of assumption
without evidence.
I do not mean to condemn those who employ themselves in working out into
detail this sort of hypotheses; it is useful to ascertain what are the
known phenomena, to the laws of which those of the subject of inquiry
bear the greatest, or even a great analogy, since this may suggest (as
in the case of the luminiferous ether it actually did) experiments to
determine whether the analogy which goes so far does not extend still
further. But that, in doing this, we should imagine ourselves to be
seriously inquiring whether the hypothesis of an ether, an electric
fluid, or the like, is true; that we should fancy it possible to obtain
the assurance that the phenomena are produced in that way and no other;
seems to me, I confess, unworthy of the present improved conceptions of
the methods of physical science. And at the risk of being charged with
want of modesty, I cannot help expressing astonishment that a
philosopher of Dr. Whewell's abilities and attainments should have
written an elaborate treatise on the philosophy of induction, in which
he recognises absolutely no mode of induction except that of trying
hypothesis after hypothesis until one is found which fits the phenomena;
which one, when found, is to be assumed as true, with no other
reservation than that if on re-examination it should appear to assume
more than is needful for explaining the phenomena, the superfluous part
of the assumption should be cut off. And this without the slightest
distinction between the cases in which it may be known beforehand that
two different hypotheses cannot lead to the same result, and those in
which, for aught we can ever know, the range of suppositions, all
equally consistent with the phenomena, may be infinite.[11]
§ 7. It is necessary, before quitting the subject of hypotheses, to
guard against the appearance of reflecting upon the scientific value of
several branches of physical inquiry, which, though only in their
infancy, I hold to be strictly inductive. There is a great difference
between inventing agencies to account for classes of phenomena, and
endeavouring, in conformity with known laws, to conjecture what former
collocations of known agents may have given birth to individual facts
still in existence. The latter is the legitimate operation of inferring
from an observed effect, the existence, in time past, of a cause similar
to that by which we know it to be produced in all cases in which we have
actual experience of its origin. This, for example, is the scope of the
inquiries of geology; and they are no more illogical or visionary than
judicial inquiries, which also aim at discovering a past event by
inference from those of its effects which still subsist. As we can
ascertain whether a man was murdered or died a natural death, from the
indications exhibited by the corpse, the presence or absence of signs of
struggling on the ground or on the adjacent objects, the marks of
blood, the footsteps of the supposed murderers, and so on, proceeding
throughout on uniformities ascertained by a perfect induction without
any mixture of hypothesis; so if we find, on and beneath the surface of
our planet, masses exactly similar to deposits from water, or to results
of the cooling of matter melted by fire, we may justly conclude that
such has been their origin; and if the effects, though similar in kind,
are on a far larger scale than any which are now produced, we may
rationally, and without hypothesis, conclude either that the causes
existed formerly with greater intensity, or that they have operated
during an enormous length of time. Further than this no geologist of
authority has, since the rise of the present enlightened school of
geological speculation, attempted to go.
In many geological inquiries it doubtless happens that though the laws
to which the phenomena are ascribed are known laws, and the agents known
agents, those agents are not known to have been present in the
particular case. In the speculation respecting the igneous origin of
trap or granite, the fact does not admit of direct proof, that those
substances have been actually subjected to intense heat. But the same
thing might be said of all judicial inquiries which proceed on
circumstantial evidence. We can conclude that a man was murdered, though
it is not proved by the testimony of eye-witnesses that some person who
had the intention of murdering him was present on the spot. It is
enough, for most purposes, if no other known cause could have generated
the effects shown to have been produced.
The celebrated speculation of Laplace concerning the origin of the earth
and planets, participates essentially in the inductive character of
modern geological theory. The speculation is, that the atmosphere of the
sun originally extended to the present limits of the solar system; from
which, by the process of cooling, it has contracted to its present
dimensions; and since, by the general principles of mechanics, the
rotation of the sun and of its accompanying atmosphere must increase in
rapidity as its volume diminishes, the increased centrifugal force
generated by the more rapid rotation, overbalancing the action of
gravitation, has caused the sun to abandon successive rings of vaporous
matter, which are supposed to have condensed by cooling, and to have
become the planets. There is in this theory no unknown substance
introduced on supposition, nor any unknown property or law ascribed to a
known substance. The known laws of matter authorize us to suppose that a
body which is constantly giving out so large an amount of heat as the
sun is, must be progressively cooling, and that, by the process of
cooling, it must contract; if, therefore, we endeavour, from the present
state of that luminary, to infer its state in a time long past, we must
necessarily suppose that its atmosphere extended much farther than at
present, and we are entitled to suppose that it extended as far as we
can trace effects such as it might naturally leave behind it on
retiring; and such the planets are. These suppositions being made, it
follows from known laws that successive zones of the solar atmosphere
might be abandoned; that these would continue to revolve round the sun
with the same velocity as when they formed part of its substance; and
that they would cool down, long before the sun itself, to any given
temperature, and consequently to that at which the greater part of the
vaporous matter of which they consisted would become liquid or solid.
The known law of gravitation would then cause them to agglomerate in
masses, which would assume the shape our planets actually exhibit; would
acquire, each about its own axis, a rotatory movement; and would in that
state revolve, as the planets actually do, about the sun, in the same
direction with the sun's rotation, but with less velocity, because in
the same periodic time which the sun's rotation occupied when his
atmosphere extended to that point. There is thus, in Laplace's theory,
nothing, strictly speaking, hypothetical: it is an example of legitimate
reasoning from a present effect to a possible past cause, according to
the known laws of that cause. The theory therefore is, as I have said,
of a similar character to the theories of geologists; but considerably
inferior to them in point of evidence. Even if it were proved (which it
is not) that the conditions necessary for determining the breaking off
of successive rings would certainly occur; there would still be a much
greater chance of error in assuming that the existing laws of nature are
the same which existed at the origin of the solar system, than in merely
presuming (with geologists) that those laws have lasted through a few
revolutions and transformations of a single one among the bodies of
which that system is composed.