THEORY OF APPROXIMATION.
In order that we may gain a true understanding of the kind, degree, and
value of the knowledge which we acquire by experimental investigation,
it is requisite that we should be fully conscious of its approximate
character. We must learn to distinguish between what we can know
and cannot know--between the questions which admit of solution, and
those which only seem to be solved. Many persons may be misled by the
expression *exact science*, and may think that the knowledge acquired
by scientific methods admits of our reaching absolutely true laws,
exact to the last degree. There is even a prevailing impression that
when once mathematical formulæ have been successfully applied to a
branch of science, this portion of knowledge assumes a new nature, and
admits of reasoning of a higher character than those sciences which are
still unmathematical.
The very satisfactory degree of accuracy attained in the science of
astronomy gives a certain plausibility to erroneous notions of this
kind. Some persons no doubt consider it to be *proved* that planets
move in ellipses, in such a manner that all Kepler’s laws hold exactly
true; but there is a double error in any such notions. In the first
place, Kepler’s laws are *not proved*, if by proof we mean certain
demonstration of their exact truth. In the next place, even assuming
Kepler’s laws to be exactly true in a theoretical point of view, the
planets never move according to those laws. Even if we could observe
the motions of a planet, of a perfect globular form, free from all
perturbing or retarding forces, we could never prove that it moved
in a perfect ellipse. To prove the elliptical form we should have to
measure infinitely small angles, and infinitely small fractions of a
second; we should have to perform impossibilities. All we can do is to
show that the motion of an unperturbed planet approaches *very nearly*
to the form of an ellipse, and more nearly the more accurately our
observations are made. But if we go on to assert that the path *is* an
ellipse we pass beyond our data, and make an assumption which cannot be
verified by observation.
But, secondly, as a matter of fact no planet does move in a perfect
ellipse, or manifest the truth of Kepler’s laws exactly. The law of
gravity prevents its own results from being clearly exhibited, because
the mutual perturbations of the planets distort the elliptical paths.
Those laws, again, hold exactly true only of infinitely small bodies,
and when two great globes, like the sun and Jupiter, attract each
other, the law must be modified. The periodic time is then shortened
in the ratio of the square root of the number expressing the sun’s
mass, to that of the sum of the numbers expressing the masses of the
sun and planet, as was shown by Newton.[374] Even at the present day
discrepancies exist between the observed dimensions of the planetary
orbits and their theoretical magnitudes, after making allowance for
all disturbing causes.[375] Nothing is more certain in scientific
method than that approximate coincidence alone can be expected. In
the measurement of continuous quantity perfect correspondence must
be accidental, and should give rise to suspicion rather than to
satisfaction.
[374] *Principia*, bk. iii. Prop. 15.
[375] Lockyer’s *Lessons in Elementary Astronomy*, p. 301.
One remarkable result of the approximate character of our observations
is that we could never prove the existence of perfectly circular or
parabolic movement, even if it existed. The circle is a singular case
of the ellipse, for which the eccentricity is zero; it is infinitely
improbable that any planet, even if undisturbed by other bodies, would
have a circle for its orbit; but if the orbit were a circle we could
never prove the entire absence of eccentricity. All that we could
do would be to declare the divergence from the circular form to be
inappreciable. Delambre was unable to detect the slightest ellipticity
in the orbit of Jupiter’s first satellite, but he could only infer
that the orbit was *nearly* circular. The parabola is the singular
limit between the ellipse and the hyperbola. As there are elliptic and
hyperbolic comets, so we might conceive the existence of a parabolic
comet. Indeed if an undisturbed comet fell towards the sun from an
infinite distance it would move in a parabola; but we could never prove
that it so moved.
*Substitution of Simple Hypotheses.*
In truth men never can solve problems fulfilling the complex
circumstances of nature. All laws and explanations are in a certain
sense hypothetical, and apply exactly to nothing which we can know
to exist. In place of the actual objects which we see and feel, the
mathematician substitutes imaginary objects, only partially resembling
those represented, but so devised that the discrepancies are not of
an amount to alter seriously the character of the solution. When we
probe the matter to the bottom physical astronomy is as hypothetical as
Euclid’s elements. There may exist in nature perfect straight lines,
triangles, circles, and other regular geometrical figures; to our
science it is a matter of indifference whether they do or do not exist,
because in any case they must be beyond our powers of perception. If
we submitted a perfect circle to the most rigorous scrutiny, it is
impossible that we should discover whether it were perfect or not.
Nevertheless in geometry we argue concerning perfect curves, and
rectilinear figures, and the conclusions apply to existing objects so
far as we can assure ourselves that they agree with the hypothetical
conditions of our reasoning. This is in reality all that we can do in
the most perfect of the sciences.
Doubtless in astronomy we meet with the nearest approximation to
actual conditions. The law of gravity is not a complex one in itself,
and we believe it with much probability to be exactly true; but we
cannot calculate out in any real case its accurate results. The law
asserts that every particle of matter in the universe attracts every
other particle, with a force depending on the masses of the particles
and their distances. We cannot know the force acting on any particle
unless we know the masses and distances and positions of all other
particles in the universe. The physical astronomer has made a sweeping
assumption, namely, that all the millions of existing systems exert no
perturbing effects on our planetary system, that is to say, no effects
in the least appreciable. The problem at once becomes hypothetical,
because there is little doubt that gravitation between our sun and
planets and other systems does exist. Even when they consider the
relations of our planetary bodies *inter se*, all their processes are
only approximate. In the first place they assume that each of the
planets is a perfect ellipsoid, with a smooth surface and a homogeneous
interior. That this assumption is untrue every mountain and valley,
every sea, every mine affords conclusive evidence. If astronomers are
to make their calculations perfect, they must not only take account
of the Himalayas and the Andes, but must calculate separately the
attraction of every hill, nay, of every ant-hill. So far are they
from having considered any local inequality of the surface, that they
have not yet decided upon the general form of the earth; it is still
a matter of speculation whether or not the earth is an ellipsoid with
three unequal axes. If, as is probable, the globe is irregularly
compressed in some directions, the calculations of astronomers will
have to be repeated and refined, in order that they may approximate
to the attractive power of such a body. If we cannot accurately learn
the form of our own earth, how can we expect to ascertain that of
the moon, the sun, and other planets, in some of which probably are
irregularities of greater proportional amount?
In a further way the science of physical astronomy is merely
approximate and hypothetical. Given homogeneous ellipsoids acting upon
each other according to the law of gravity, the best mathematicians
have never and perhaps never will determine exactly the resulting
movements. Even when three bodies simultaneously attract each other the
complication of effects is so great that only approximate calculations
can be made. Astronomers have not even attempted the general problem
of the simultaneous attractions of four, five, six, or more bodies;
they resolve the general problem into so many different problems of
three bodies. The principle upon which the calculations of physical
astronomy proceed, is to neglect every quantity which does not seem
likely to lead to an effect appreciable in observation, and the
quantities rejected are far more numerous and complex than the few
larger terms which are retained. All then is merely approximate.
Concerning other branches of physical science the same statements are
even more evidently true. We speak and calculate about inflexible
bars, inextensible lines, heavy points, homogeneous substances,
uniform spheres, perfect fluids and gases, and we deduce a great
number of beautiful theorems; but all is hypothetical. There is no
such thing as an inflexible bar, an inextensible line, nor any one
of the other perfect objects of mechanical science; they are to be
classed with those mythical existences, the straight line, triangle,
circle, &c., about which Euclid so freely reasoned. Take the simplest
operation considered in statics--the use of a crowbar in raising a
heavy stone, and we shall find, as Thomson and Tait have pointed
out, that we neglect far more than we observe.[376] If we suppose
the bar to be quite rigid, the fulcrum and stone perfectly hard, and
the points of contact real points, we may give the true relation of
the forces. But in reality the bar must bend, and the extension and
compression of different parts involve us in difficulties. Even if
the bar be homogeneous in all its parts, there is no mathematical
theory capable of determining with accuracy all that goes on; if, as
is infinitely more probable, the bar is not homogeneous, the complete
solution will be immensely more complicated, but hardly more hopeless.
No sooner had we determined the change of form according to simple
mechanical principles, than we should discover the interference of
thermodynamic principles. Compression produces heat and extension
cold, and thus the conditions of the problem are modified throughout.
In attempting a fourth approximation we should have to allow for the
conduction of heat from one part of the bar to another. All these
effects are utterly inappreciable in a practical point of view, if
the bar be a good stout one; but in a theoretical point of view they
entirely prevent our saying that we have solved a natural problem. The
faculties of the human mind, even when aided by the wonderful powers
of abbreviation conferred by analytical methods, are utterly unable to
cope with the complications of any real problem. And had we exhausted
all the known phenomena of a mechanical problem, how can we tell that
hidden phenomena, as yet undetected, do not intervene in the commonest
actions? It is plain that no phenomenon comes within the sphere of
our senses unless it possesses a momentum capable of irritating the
appropriate nerves. There may then be worlds of phenomena too slight to
rise within the scope of our consciousness.
[376] *Treatise on Natural Philosophy*, vol. i. pp. 337, &c.
All the instruments with which we perform our measurements are faulty.
We assume that a plumb-line gives a vertical line; but this is never
true in an absolute sense, owing to the attraction of mountains
and other inequalities in the surface of the earth. In an accurate
trigonometrical survey, the divergencies of the plumb-line must be
approximately determined and allowed for. We assume a surface of
mercury to be a perfect plane, but even in the breadth of 5 inches
there is a calculable divergence from a true plane of about one
ten-millionth part of an inch; and this surface further diverges from
true horizontality as the plumb-line does from true verticality.
That most perfect instrument, the pendulum, is not theoretically
perfect, except for infinitely small arcs of vibration, and the
delicate experiments performed with the torsion balance proceed on the
assumption that the force of torsion of a wire is proportional to the
angle of torsion, which again is only true for infinitely small angles.
Such is the purely approximate character of all our operations that it
is not uncommon to find the theoretically worse method giving truer
results than the theoretically perfect method. The common pendulum
which is not isochronous is better for practical purposes than the
cycloidal pendulum, which is isochronous in theory but subject to
mechanical difficulties. The spherical form is not the correct form for
a speculum or lense, but it differs so slightly from the true form, and
is so much more easily produced mechanically, that it is generally
best to rest content with the spherical surface. Even in a six-feet
mirror the difference between the parabola and the sphere is only about
one ten-thousandth part of an inch, a thickness which would be taken
off in a few rubs of the polisher. Watts’ ingenious parallel motion was
intended to produce rectilinear movement of the piston-rod. In reality
the motion was always curvilinear, but for his purposes a certain part
of the curve approximated sufficiently to a straight line.
*Approximation to Exact Laws.*
Though we can not prove numerical laws with perfect accuracy, it would
be a great mistake to suppose that there is any inexactness in the laws
of nature. We may even discover a law which we believe to represent
the action of forces with perfect exactness. The mind may seem to pass
in advance of its data, and choose out certain numerical results as
absolutely true. We can never really pass beyond our data, and so far
as assumption enters in, so far want of certainty will attach to our
conclusions; nevertheless we may sometimes rightly prefer a probable
assumption of a precise law to numerical results, which are at the best
only approximate. We must accordingly draw a strong distinction between
the laws of nature which we believe to be accurately stated in our
formulas, and those to which our statements only make an approximation,
so that at a future time the law will be differently stated.
The law of gravitation is expressed in the form F = Mm/D^{2},
meaning that gravity is proportional directly to the product of
the gravitating masses, and indirectly to the square of their
distance. The latent heat of steam is expressed by the equation
log F = *a* + *b*α^{t} + *c*β^{t}, in which are five quantities *a*,
*b*, *c*, α, β, to be determined by experiment. There is every reason
to believe that in the progress of science the law of gravity will
remain entirely unaltered, and the only effect of further inquiry will
be to render it a more and more probable expression of the absolute
truth. The law of the latent heat of steam on the other hand, will be
modified by every new series of experiments, and it may not improbably
be shown that the assumed law can never be made to agree exactly with
the results of experiment.
Philosophers have not always supposed that the law of gravity was
exactly true. Newton, though he had the highest confidence in its
truth, admitted that there were motions in the planetary system which
he could not reconcile with the law. Euler and Clairaut who were, with
D’Alembert, the first to apply the full powers of mathematical analysis
to the theory of gravitation as explaining the perturbations of the
planets, did not think the law sufficiently established to attribute
all discrepancies to the errors of calculation and observation. They
did not feel certain that the force of gravity exactly obeyed the
well-known rule. The law might involve other powers of the distance. It
might be expressed in the form
F = ... + *a*/D + *b*/D^{2} + *c*/D^{3} + ...
and the coefficients *a* and *c* might be so small that those terms
would become apparent only in very accurate comparisons with fact.
Attempts have been made to account for difficulties, by attributing
value to such neglected terms. Gauss at one time thought the even more
fundamental principle of gravity, that the force is dependent only on
mass and distance, might not be exactly true, and he undertook accurate
pendulum experiments to test this opinion. Only as repeated doubts have
time after time been resolved in favour of the law of Newton, has it
been assumed as precisely correct. But this belief does not rest on
experiment or observation only. The calculations of physical astronomy,
however accurate, could never show that the other terms of the above
expression were absolutely devoid of value. It could only be shown that
they had such slight value as never to become apparent.
There are, however, other reasons why the law is probably complete
and true as commonly stated. Whatever influence spreads from a point,
and expands uniformly through space, will doubtless vary inversely
in intensity as the square of the distance, because the area over
which it is spread increases as the square of the radius. This part
of the law of gravity may be considered as due to the properties of
space, and there is a perfect analogy in this respect between gravity
and all other *emanating* forces, as was pointed out by Keill.[377]
Thus the undulations of light, heat, and sound, and the attractions
of electricity and magnetism obey the very same law so far as we
can ascertain. If the molecules of a gas or the particles of matter
constituting odour were to start from a point and spread uniformly,
their distances would increase and their density decrease according to
the same principle.
[377] *An Introduction to Natural Philosophy*, 3rd edit. 1733, p. 5.
Other laws of nature stand in a similar position. Dalton’s laws of
definite combining proportions never have been, and never can be,
exactly proved; but chemists having shown, to a considerable degree of
approximation, that the elements combine together as if each element
had atoms of an invariable mass, assume that this is exactly true. They
go even further. Prout pointed out in 1815 that the equivalent weights
of the elements appeared to be simple numbers; and the researches of
Dumas, Pelouze, Marignac, Erdmann, Stas, and others have gradually
rendered it likely that the atomic weights of hydrogen, carbon, oxygen,
nitrogen, chlorine, and silver, are in the ratios of the numbers 1,
12, 16, 14, 35·5, and 108. Chemists then step beyond their data; they
throw aside their actual experimental numbers, and assume that the true
ratios are not those exactly indicated by any weighings, but the simple
ratios of these numbers. They boldly assume that the discrepancies are
due to experimental errors, and they are justified by the fact that
the more elaborate and skilful the researches on the subject, the more
nearly their assumption is verified. Potassium is the only element
whose atomic weight has been determined with great care, but which has
not shown an approach to a simple ratio with the other elements. This
exception may be due to some unsuspected cause of error.[378] A similar
assumption is made in the law of definite combining volumes of gases,
and Brodie has clearly pointed out the line of argument by which the
chemist, observing that the discrepancies between the law and fact are
within the limits of experimental error, assumes that they are due to
error.[379]
[378] Watts, *Dictionary of Chemistry*, vol. i. p. 455.
[379] *Philosophical Transactions*, (1866) vol. clvi. p. 809.
Faraday, in one of his researches, expressly makes an assumption
of the same kind. Having shown, with some degree of experimental
precision, that there exists a simple proportion between quantities of
electrical energy and the quantities of chemical substances which it
can decompose, so that for every atom dissolved in the battery cell an
atom ought theoretically, that is without regard to dissipation of some
of the energy, to be decomposed in the electrolytic cell, he does not
stop at his numerical results. “I have not hesitated,” he says,[380]
“to apply the more strict results of chemical analysis to correct the
numbers obtained as electrolytic results. This, it is evident, may be
done in a great number of cases, without using too much liberty towards
the due severity of scientific research.”
[380] *Experimental Researches in Electricity*, vol. i. p. 246.
The law of the conservation of energy, one of the widest of all
physical generalisations, rests upon the same footing. The most that
we can do by experiment is to show that the energy entering into any
experimental combination is almost equal to what comes out of it,
and more nearly so the more accurately we perform the measurements.
Absolute equality is always a matter of assumption. We cannot even
prove the indestructibility of matter; for were an exceedingly minute
fraction of existing matter to vanish in any experiment, say one part
in ten millions, we could never detect the loss.
*Successive Approximations to Natural Conditions.*
When we examine the history of scientific problems, we find that one
man or one generation is usually able to make but a single step at
a time. A problem is solved for the first time by making some bold
hypothetical simplification, upon which the next investigator makes
hypothetical modifications approaching more nearly to the truth. Errors
are successively pointed out in previous solutions, until at last there
might seem little more to be desired. Careful examination, however,
will show that a series of minor inaccuracies remain to be corrected
and explained, were our powers of reasoning sufficiently great, and the
purpose adequate in importance.
Newton’s successful solution of the problem of the planetary movements
entirely depended at first upon a great simplification. The law of
gravity only applies directly to two infinitely small particles, so
that when we deal with vast globes like the earth, Jupiter, and the
sun, we have an immense aggregate of separate attractions to deal with,
and the law of the aggregate need not coincide with the law of the
elementary particles. But Newton, by a great effort of mathematical
reasoning, was able to show that two homogeneous spheres of matter act
as if the whole of their masses were concentrated at the centres; in
short, that such spheres are centrobaric bodies (p. 364). He was then
able with comparative ease to calculate the motions of the planets on
the hypothesis of their being spheres, and to show that the results
roughly agreed with observation. Newton, indeed, was one of the few men
who could make two great steps at once. He did not rest contented with
the spherical hypothesis; having reason to believe that the earth was
really a spheroid with a protuberance around the equator, he proceeded
to a second approximation, and proved that the attraction of the
protuberant matter upon the moon accounted for the precession of the
equinoxes, and led to various complicated effects. But, (p. 459), even
the spheroidal hypothesis is far from the truth. It takes no account
of the irregularities of surface, the great protuberance of land in
Central Asia and South America, and the deficiency in the bed of the
Atlantic.
To determine the law according to which a projectile, such as a cannon
ball, moves through the atmosphere is a problem very imperfectly
solved at the present day, but in which many successive advances have
been made. So little was known concerning the subject three or four
centuries ago that a cannon ball was supposed to move at first in a
straight line, and after a time to be deflected into a curve. Tartaglia
ventured to maintain that the path was curved throughout, as by the
principle of continuity it should be; but the ingenuity of Galileo
was required to prove this opinion, and to show that the curve was
approximately a parabola. It is only, however, under forced hypotheses
that we can assert the path of a projectile to be truly a parabola: the
path must be through a perfect vacuum, where there is no resisting
medium of any kind; the force of gravity must be uniform and act in
parallel lines; or else the moving body must be either a mere point, or
a perfect centrobaric body, that is a body possessing a definite centre
of gravity. These conditions cannot be really fulfilled in practice.
The next great step in the problem was made by Newton and Huyghens, the
latter of whom asserted that the atmosphere would offer a resistance
proportional to the velocity of the moving body, and concluded that
the path would have in consequence a logarithmic character. Newton
investigated in a general manner the subject of resisting media, and
came to the conclusion that the resistance is more nearly proportional
to the square of the velocity. The subject then fell into the hands
of Daniel Bernoulli, who pointed out the enormous resistance of the
air in cases of rapid movement, and calculated that a cannon ball, if
fired vertically in a vacuum, would rise eight times as high as in the
atmosphere. In recent times an immense amount both of theoretical and
experimental investigation has been spent upon the subject, since it is
one of importance in the art of war. Successive approximations to the
true law have been made, but nothing like a complete and final solution
has been achieved or even hoped for.[381]
[381] Hutton’s *Mathematical Dictionary*, vol. ii. pp. 287–292.
It is quite to be expected that the earliest experimenters in any
branch of science will overlook errors which afterwards become most
apparent. The Arabian astronomers determined the meridian by taking the
middle point between the places of the sun when at equal altitudes on
the same day. They overlooked the fact that the sun has its own motion
in the time between the observations. Newton thought that the mutual
disturbances of the planets might be disregarded, excepting perhaps the
effect of the mutual attraction of the greater planets, Jupiter and
Saturn, near their conjunction.[382] The expansion of quicksilver was
long used as the measure of temperature, no clear idea being possessed
of temperature apart from some of its more obvious effects. Rumford,
in the first experiment leading to a determination of the mechanical
equivalent of heat, disregarded the heat absorbed by the apparatus,
otherwise he would, in Dr. Joule’s opinion, have come nearly to the
correct result.
[382] *Principia*, bk. iii. Prop. 13.
It is surprising to learn the number of causes of error which enter
into the simplest experiment, when we strive to attain rigid accuracy.
We cannot accurately perform the simple experiment of compressing gas
in a bent tube by a column of mercury, in order to test the truth
of Boyle’s Law, without paying regard to--(1) the variations of
atmospheric pressure, which are communicated to the gas through the
mercury; (2) the compressibility of mercury, which causes the column
of mercury to vary in density; (3) the temperature of the mercury
throughout the column; (4) the temperature of the gas, which is with
difficulty maintained invariable; (5) the expansion of the glass tube
containing the gas. Although Regnault took all these circumstances
into account in his examination of the law,[383] there is no reason to
suppose that he exhausted the sources of inaccuracy.
[383] Jamin, *Cours de Physique*, vol. i. pp. 282, 283.
The early investigations concerning the nature of waves in elastic
media proceeded upon the assumption that waves of different lengths
would travel with equal speed. Newton’s theory of sound led him to
this conclusion, and observation (p. 295) had verified the inference.
When the undulatory theory came to be applied at the commencement of
this century to explain the phenomena of light, a great difficulty was
encountered. The angle at which a ray of light is refracted in entering
a denser medium depends, according to that theory, on the velocity
with which the wave travels, so that if all waves of light were to
travel with equal velocity in the same medium, the dispersion of mixed
light by the prism and the production of the spectrum could not take
place. Some most striking phenomena were thus in direct conflict with
the theory. Cauchy first pointed out the explanation, namely, that all
previous investigators had made an arbitrary assumption for the sake
of simplifying the calculations. They had assumed that the particles
of the vibrating medium are so close together that the intervals are
inconsiderable compared with the length of the wave. This hypothesis
happened to be approximately true in the case of air, so that no error
was discovered in experiments on sound. Had it not been so, the earlier
analysts would probably have failed to give any solution, and the
progress of the subject might have been retarded. Cauchy was able to
make a new approximation under the more difficult supposition, that
the particles of the vibrating medium are situated at considerable
distances, and act and react upon the neighbouring particles by
attractive and repulsive forces. To calculate the rate of propagation
of disturbance in such a medium is a work of excessive difficulty. The
complete solution of the problem appears indeed to be beyond human
power, so that we must be content, as in the case of the planetary
motions, to look forward to successive approximations. All that Cauchy
could do was to show that certain quantities, neglected in previous
theories, became of considerable amount under the new conditions of
the problem, so that there will exist a relation between the length
of the wave, and the velocity at which it travels. To remove, then,
the difficulties in the way of the undulatory theory of light, a new
approach to probable conditions was needed.[384]
[384] Lloyd’s *Lectures on the Wave Theory*, pp. 22, 23.
In a similar manner Fourier’s theory of the conduction and radiation
of heat was based upon the hypothesis that the quantity of heat
passing along any line is simply proportional to the rate of change
of temperature. But it has since been shown by Forbes that the
conductivity of a body diminishes as its temperature increases. All
the details of Fourier’s solution therefore require modification, and
the results are in the meantime to be regarded as only approximately
true.[385]
[385] Tait’s *Thermodynamics*, p. 10.
We ought to distinguish between those problems which are physically and
those which are merely mathematically incomplete. In the latter case
the physical law is correctly seized, but the mathematician neglects,
or is more often unable to follow out the law in all its results.
The law of gravitation and the principles of harmonic or undulatory
movement, even supposing the data to be correct, can never be followed
into all their ultimate results. Young explained the production of
Newton’s rings by supposing that the rays reflected from the upper and
lower surfaces of a thin film of a certain thickness were in opposite
phases, and thus neutralised each other. It was pointed out, however,
that as the light reflected from the nearer surface must be undoubtedly
a little brighter than that from the further surface, the two rays
ought not to neutralise each other so completely as they are observed
to do. It was finally shown by Poisson that the discrepancy arose only
from incomplete solution of the problem; for the light which has once
got into the film must be to a certain extent reflected backwards and
forwards *ad infinitum*; and if we follow out this course of the light
by perfect mathematical analysis, absolute darkness may be shown to
result from the interference of the rays.[386] In this case the natural
laws concerned, those of reflection and refraction, are accurately
known, and the only difficulty consists in developing their full
consequences.
[386] Lloyd’s *Lectures on the Wave Theory*, pp. 82, 83.
*Discovery of Hypothetically Simple Laws.*
In some branches of science we meet with natural laws of a simple
character which are in a certain point of view exactly true and yet can
never be manifested as exactly true in natural phenomena. Such, for
instance, are the laws concerning what is called a *perfect gas*. The
gaseous state of matter is that in which the properties of matter are
exhibited in the simplest manner. There is much advantage accordingly
in approaching the question of molecular mechanics from this side.
But when we ask the question--What is a gas? the answer must be a
hypothetical one. Finding that gases *nearly* obey the law of Boyle
and Mariotte; that they *nearly* expand by heat at the uniform rate of
one part in 272·9 of their volume at 0° for each degree centigrade;
and that they *more nearly* fulfil these conditions the more distant
the point of temperature at which we examine them from the liquefying
point, we pass by the principle of continuity to the conception of a
perfect gas. Such a gas would probably consist of atoms of matter at
so great a distance from each other as to exert no attractive forces
upon each other; but for this condition to be fulfilled the distances
must be infinite, so that an absolutely perfect gas cannot exist. But
the perfect gas is not merely a limit to which we may approach, it is a
limit passed by at least one real gas. It has been shown by Despretz,
Pouillet, Dulong, Arago, and finally Regnault, that all gases diverge
from the Boylean law, and in nearly all cases the density of the gas
increases in a somewhat greater ratio than the pressure, indicating
a tendency on the part of the molecules to approximate of their own
accord. In the more condensable gases such as sulphurous acid, ammonia,
and cyanogen, this tendency is strongly apparent near the liquefying
point. Hydrogen, on the contrary, diverges from the law of a perfect
gas in the opposite direction, that is, the density increases less than
in the ratio of the pressure.[387] This is a singular exception, the
bearing of which I am unable to comprehend.
[387] Jamin, *Cours de Physique*, vol. i. pp. 283–288.
All gases diverge again from the law of uniform expansion by heat, but
the divergence is less as the gas in question is less condensable, or
examined at a temperature more removed from its liquefying point. Thus
the perfect gas must have an infinitely high temperature. According
to Dalton’s law each gas in a mixture retains its own properties
unaffected by the presence of any other gas.[388] This law is probably
true only by approximation, but it is obvious that it would be true of
the perfect gas with infinitely distant particles.[389]
[388] Joule and Thomson, *Philosophical Transactions*, 1854,
vol. cxliv. p. 337.
[389] The properties of a perfect gas have been described by Rankine,
*Transactions of the Royal Society of Edinburgh*, vol. xxv. p. 561.
*Mathematical Principles of Approximation.*
The approximate character of physical science will be rendered more
plain if we consider it from a mathematical point of view. Throughout
quantitative investigations we deal with the relation of one quantity
to other quantities, of which it is a function; but the subject is
sufficiently complicated if we view one quantity as a function of
one other. Now, as a general rule, a function can be developed or
expressed as the sum of quantities, the values of which depend upon the
successive powers of the variable quantity. If *y* be a function of *x*
then we may say that
*y* = A + B*x* + C*x*^{2} + D*x*^{3} + E*x*^{4} ....
In this equation, A, B, C, D, &c., are fixed quantities, of different
values in different cases. The terms may be infinite in number or
after a time may cease to have any value. Any of the coefficients A,
B, C, &c., may be zero or negative; but whatever they be they are
fixed. The quantity *x* on the other hand may be made what we like,
being variable. Suppose, in the first place, that *x* and *y* are both
lengths. Let us assume that 1/10,000 part of an inch is the least that
we can take note of. Then when *x* is one hundredth of an inch, we have
*x*^{2} = 1/10,000, and if C be less than unity, the term C*x*^{2} will
be inappreciable, being less than we can measure. Unless any of the
quantities D, E, &c., should happen to be very great, it is evident
that all the succeeding terms will also be inappreciable, because the
powers of *x* become rapidly smaller in geometrical ratio. Thus when
*x* is made small enough the quantity *y* seems to obey the equation
*y* = A + B*x*.
If *x* should be still less, if it should become as small, for
instance, as 1/1,000,000 of an inch, and B should not be very great,
then *y* would appear to be the fixed quantity A, and would not seem to
vary with *x* at all. On the other hand, were x to grow greater, say
equal to 1/10 inch, and C not be very small, the term C*x*^{2} would
become appreciable, and the law would now be more complicated.
We can invert the mode of viewing this question, and suppose that
while the quantity *y* undergoes variations depending on many powers
of *x*, our power of detecting the changes of value is more or less
acute. While our powers of observation remain very rude we may be
unable to detect any change in the quantity at all, that is to say,
B*x* may always be too small to come within our notice, just as in
former days the fixed stars were so called because they remained at
apparently fixed distances from each other. With the use of telescopes
and micrometers we become able to detect the existence of some motion,
so that the distance of one star from another may be expressed by
A + B*x*, the term including *x*^{2} being still inappreciable. Under
these circumstances the star will seem to move uniformly, or in simple
proportion to the time *x*. With much improved means of measurement it
will probably be found that this uniformity of motion is only apparent,
and that there exists some acceleration or retardation. More careful
investigation will show the law to be more and more complicated than
was previously supposed.
There is yet another way of explaining the apparent results of a
complicated law. If we take any curve and regard a portion of it free
from any kind of discontinuity, we may represent the character of such
portion by an equation of the form
*y* = A + B*x* + C*x*^{2} + D*x*^{3} + ....
Restrict the attention to a very small portion of the curve, and the
eye will be unable to distinguish its difference from a straight
line, which amounts to saying that in the portion examined the term
C*x*^{2} has no value appreciable by the eye. Take a larger portion of
the curve and it will be apparent that it possesses curvature, but it
will be possible to draw a parabola or ellipse so that the curve shall
apparently coincide with a portion of that parabola or ellipse. In the
same way if we take larger and larger arcs of the curve it will assume
the character successively of a curve of the third, fourth, and perhaps
higher degrees; that is to say, it corresponds to equations involving
the third, fourth, and higher powers of the variable quantity.
We have arrived then at the conclusion that every phenomenon, when its
amount can only be rudely measured, will either be of fixed amount,
or will seem to vary uniformly like the distance between two inclined
straight lines. More exact measurement may show the error of this first
assumption, and the variation will then appear to be like that of the
distance between a straight line and a parabola or ellipse. We may
afterwards find that a curve of the third or higher degrees is really
required to represent the variation. I propose to call the variation
of a quantity *linear*, *elliptic*, *cubic*, *quartic*, *quintic*, &c.,
according as it is discovered to involve the first, second, third,
fourth, fifth, or higher powers of the variable. It is a general
rule in quantitative investigation that we commence by discovering
linear, and afterwards proceed to elliptic or more complicated laws of
variation. The approximate curves which we employ are all, according
to De Morgan’s use of the name, parabolas of some order or other; and
since the common parabola of the second order is approximately the same
as a very elongated ellipse, and is in fact an infinitely elongated
ellipse, it is convenient and proper to call variation of the second
order *elliptic*. It might also be called *quadric* variation.
As regards many important phenomena we are yet only in the first stage
of approximation. We know that the sun and many so-called fixed stars,
especially 61 Cygni, have a proper motion through space, and the
direction of this motion at the present time is known with some degree
of accuracy. But it is hardly consistent with the theory of gravity
that the path of any body should really be a straight line. Hence, we
must regard a rectilinear path as only a provisional description of
the motion, and look forward to the time when its curvature will be
detected, though centuries perhaps must first elapse.
We are accustomed to assume that on the surface of the earth the force
of gravity is uniform, because the variation is of so slight an amount
that we are scarcely able to detect it. But supposing we could measure
the variation, we should find it simply proportional to the height.
Taking the earth’s radius to be unity, let *h* be the height at which
we measure the force of gravity. Then by the well-known law of the
inverse square, that force will be proportional to
*g*/(1 + *h*)^{2}, or to *g*(1 - 2*h* + 3*h*^{2} - 4*h*^{3} + ...).
But at all heights to which we can attain *h* will be so small a
fraction of the earth’s radius that 3*h*^{2} will be inappreciable, and
the force of gravity will seem to follow the law of linear variation,
being proportional to 1 - 2*h*.
When the circumstances of an experiment are much altered, different
powers of the variable may become prominent. The resistance of a liquid
to a body moving through it may be approximately expressed as the sum
of two terms respectively involving the first and second powers of the
velocity. At very low velocities the first power is of most importance,
and the resistance, as Professor Stokes has shown, is nearly in simple
proportion to the velocity. When the motion is rapid the resistance
increases in a still greater degree, and is more nearly proportional to
the square of the velocity.
*Approximate Independence of Small Effects.*
One result of the theory of approximation possesses such importance
in physical science, and is so often applied, that we may consider
it separately. The investigation of causes and effects is immensely
simplified when we may consider each cause as producing its own effect
invariably, whether other causes are acting or not. Thus, if the
body P produces *x*, and Q produces *y*, the question is whether P
and Q acting together will produce the sum of the separate effects,
*x* + *y*. It is under this supposition that we treated the methods of
eliminating error (Chap. XV.), and errors of a less amount would still
remain if the supposition was a forced one. There are probably some
parts of science in which the supposition of independence of effects
holds rigidly true. The mutual gravity of two bodies is entirely
unaffected by the presence of other gravitating bodies. People do not
usually consider that this important principle is involved in such a
simple thing as putting two pound weights in the scale of a balance.
How do we know that two pounds together will weigh twice as much as
one? Do we know it to be exactly so? Like other results founded on
induction we cannot prove it absolutely, but all the calculations of
physical astronomy proceed upon the assumption, so that we may consider
it proved to a very high degree of approximation. Had not this been
true, the calculations of physical astronomy would have been infinitely
more complex than they actually are, and the progress of knowledge
would have been much slower.
It is a general principle of scientific method that if effects be of
small amount, comparatively to our means of observation, all joint
effects will be of a higher order of smallness, and may therefore
be rejected in a first approximation. This principle was employed
by Daniel Bernoulli in the theory of sound, under the title of *The
Principle of the Coexistence of Small Vibrations*. He showed that if
a string is affected by two kinds of vibrations, we may consider each
to be going on as if the other did not exist. We cannot perceive that
the sounding of one musical instrument prevents or even modifies the
sound of another, so that all sounds would seem to travel through the
air, and act upon the ear in independence of each other. A similar
assumption is made in the theory of tides, which are great waves. One
wave is produced by the attraction of the moon, and another by the
attraction of the sun, and the question arises, whether when these
waves coincide, as at the time of spring tides, the joint wave will be
simply the sum of the separate waves. On the principle of Bernoulli
this will be so, because the tides on the ocean are very small compared
with the depth of the ocean.
The principle of Bernoulli, however, is only approximately true. A wave
never is exactly the same when another wave is interfering with it,
but the less the displacement of particles due to each wave, the less
in a still higher degree is the effect of one wave upon the other. In
recent years Helmholtz was led to suspect that some of the phenomena
of sound might after all be due to resultant effects overlooked by the
assumption of previous physicists. He investigated the secondary waves
which would arise from the interference of considerable disturbances,
and was able to show that certain summation of resultant tones ought to
be heard, and experiments subsequently devised for the purpose showed
that they might be heard.
[Illustration]
Throughout the mechanical sciences the *Principle of the Superposition
of Small Motions* is of fundamental importance,[390] and it may be
thus explained. Suppose that two forces, acting from the points B and
C, are simultaneously moving a body A. Let the force acting from B be
such that in one second it would move A to *p*, and similarly let the
second force, acting alone, move A to *r*. The question arises, then,
whether their joint action will urge A to *q* along the diagonal of the
parallelogram. May we say that A will move the distance A*p* in the
direction AB, and A*r* in the direction AC, or, what is the same thing,
along the parallel line *pq*? In strictness we cannot say so; for when
A has moved towards *p*, the force from C will no longer act along the
line AC, and similarly the motion of A towards *r* will modify the
action of the force from B. This interference of one force with the
line of action of the other will evidently be greater the larger is
the extent of motion considered; on the other hand, as we reduce the
parallelogram A*pqr*, compared with the distances AB and AC, the less
will be the interference of the forces. Accordingly mathematicians
avoid all error by considering the motions as infinitely small, so that
the interference becomes of a still higher order of infinite smallness,
and may be entirely neglected. By the resources of the differential
calculus it is possible to calculate the motion of the particle A, as
if it went through an infinite number of infinitely small diagonals
of parallelograms. The great discoveries of Newton really arose from
applying this method of calculation to the movements of the moon round
the earth, which, while constantly tending to move onward in a straight
line, is also deflected towards the earth by gravity, and moves
through an elliptic curve, composed as it were of the infinitely small
diagonals of infinitely numerous parallelograms. The mathematician,
in his investigation of a curve, always treats it as made up of a
great number of straight lines, and it may be doubted whether he could
treat it in any other manner. There is no error in the final results,
because having obtained the formulæ flowing from this supposition, each
straight line is then regarded as becoming infinitely small, and the
polygonal line becomes undistinguishable from a perfect curve.[391]
[390] Thomson and Tait’s *Natural Philosophy*, vol. i. p. 60.
[391] Challis, *Notes on the Principles of Pure and Applied
Calculation*, 1869, p. 83.
In abstract mathematical theorems the approximation to absolute truth
is perfect, because we can treat of infinitesimals. In physical
science, on the contrary, we treat of the least quantities which are
perceptible. Nevertheless, while carefully distinguishing between these
two different cases, we may fearlessly apply to both the principle
of the superposition of small effects. In physical science we have
only to take care that the effects really are so small that any joint
effect will be unquestionably imperceptible. Suppose, for instance,
that there is some cause which alters the dimensions of a body in the
ratio of 1 to 1 + α, and another cause which produces an alteration in
the ratio of 1 to 1 + β. If they both act at once the change will be
in the ratio of 1 to (1 + α)(1 + β), or as 1 to 1 + α + β + αβ. But if
α and β be both very small fractions of the total dimensions, αβ will
be yet far smaller and may be disregarded; the ratio of change is then
approximately that of 1 to 1 + α + β, or the joint effect is the sum of
the separate effects. Thus if a body were subjected to three strains,
at right angles to each other, the total change in the volume of the
body would be approximately equal to the sum of the changes produced
by the separate strains, provided that these are very small. In like
manner not only is the expansion of every solid and liquid substance
by heat approximately proportional to the change of temperature, when
this change is very small in amount, but the cubic expansion may also
be considered as being three times as great as the linear expansion.
For if the increase of temperature expands a bar of metal in the ratio
of 1 to 1 + α, and the expansion be equal in all directions, then a
cube of the same metal would expand as 1 to (1 + α)^{3}, or as 1 to
1 + 3α + 3α^{2} + α^{3}. When α is a very small quantity the third term
3α^{2} will be imperceptible, and still more so the fourth term α^{3}.
The coefficients of expansion of solids are in fact so small, and so
imperfectly determined, that physicists seldom take into account their
second and higher powers.
It is a result of these principles that all small errors may be assumed
to vary in simple proportion to their causes--a new reason why, in
eliminating errors, we should first of all make them as small as
possible. Let us suppose that there is a right-angled triangle of which
the two sides containing the right angle are really of the lengths 3
and 4, so that the hypothenuse is √(3^{2} + 4^{2}) or 5. Now,
if in two measurements of the first side we commit slight errors,
making it successively 4·001 and 4·002, then calculation will give the
lengths of the hypothenuse as almost exactly 5·0008 and 5·0016, so that
the error in the hypothenuse will seem to vary in simple proportion
to that of the side, although it does not really do so with perfect
exactness. The logarithm of a number does not vary in proportion to
that number--nevertheless we find the difference between the logarithms
of the numbers 100000 and 100001 to be almost exactly equal to that
between the numbers 100001 and 100002. It is thus a general rule that
very small differences between successive values of a function are
approximately proportional to the small differences of the variable
quantity.
On these principles it is easy to draw up a series of rules such as
those given by Kohlrausch[392] for performing calculations in an
abbreviated form when the variable quantity is very small compared with
unity. Thus for 1 ÷ (1 + α) we may substitute 1 - α; for 1 ÷ (1 - α) we
may put 1 + α; 1 ÷ √(1 + α) becomes 1 - (1/2)α, and so forth.
[392] *An Introduction to Physical Measurements*, translated by
Waller and Procter, 1873, p. 10.
*Four Meanings of Equality.*
Although it might seem that there are few terms more free from
ambiguity than the term *equal*, yet scientific men do employ it with
at least four meanings, which it is desirable to distinguish. These
meanings I may describe as
(1) Absolute Equality.
(2) Sub-equality.
(3) Apparent Equality.
(4) Probable Equality.
By *absolute equality* we signify that which is complete and perfect
to the last degree; but it is obvious that we can only know such
equality in a theoretical or hypothetical manner. The areas of two
triangles standing upon the same base and between the same parallels
are absolutely equal. Hippocrates beautifully proved that the area
of a lunula or figure contained between two segments of circles was
absolutely equal to that of a certain right-angled triangle. As a
general rule all geometrical and other elementary mathematical theorems
involve absolute equality.
De Morgan proposed to describe as *sub-equal* those quantities which
are equal within an infinitely small quantity, so that *x* is sub-equal
to *x* + *dx*. The differential calculus may be said to arise out
of the neglect of infinitely small quantities, and in mathematical
science other subtle distinctions may have to be drawn between kinds of
equality, as De Morgan has shown in a remarkable memoir “On Infinity;
and on the sign of Equality.”[393]
[393] *Cambridge Philosophical Transactions* (1865), vol. xi. Part I.
*Apparent equality* is that with which physical science deals. Those
magnitudes are apparently equal which differ only by an imperceptible
quantity. To the carpenter anything less than the hundredth part of
an inch is non-existent; there are few arts or artists to which the
hundred-thousandth of an inch is of any account. Since all coincidence
between physical magnitudes is judged by one or other sense, we must be
restricted to a knowledge of apparent equality.
In reality even apparent equality is rarely to be expected. More
commonly experiments will give only *probable equality*, that is
results will come so near to each other that the difference may be
ascribed to unimportant disturbing causes. Physicists often assume
quantities to be equal provided that they fall within the limits of
probable error of the processes employed. We cannot expect observations
to agree with theory more closely than they agree with each other, as
Newton remarked of his investigations concerning Halley’s Comet.
*Arithmetic of Approximate Quantities.*
Considering that almost all the quantities which we treat in physical
and social science are approximate only, it seems desirable that
attention should be paid in the teaching of arithmetic to the correct
interpretation and treatment of approximate numerical statements. We
seem to need notation for expressing the approximateness or exactness
of decimal numbers. The fraction ·025 may mean either precisely one
40th part, or it may mean anything between ·0245 and ·0255. I propose
that when a decimal fraction is completely and exactly given, a *small
cipher* or circle should be added to indicate that there is nothing
more to come, as in ·025◦. When the first figure of the decimals
rejected is 5 or more, the first figure retained should be raised by
a unit, according to a rule approved by De Morgan, and now generally
recognised. To indicate that the fraction thus retained is more than
the truth, a point has been placed over the last figure in some tables
of logarithms; but a similar point is used to denote the period of a
repeating decimal, and I should therefore propose to employ a colon
*after* the figure; thus ·025: would mean that the true quantity lies
between ·0245° and ·025° inclusive of the lower but not the higher
limit. When the fraction is less than the truth, two dots might be
placed horizontally as in 025.. which would mean anything between ·025°
and ·0255° not inclusive.
When approximate numbers are added, subtracted, multiplied, or divided,
it becomes a matter of some complexity to determine the degree of
accuracy of the result. There are few persons who could assert off-hand
that the sum of the approximate numbers 34·70, 52·693, 80·1, is 167·5
*within less than* ·07. Mr. Sandeman has traced out the rules of
approximate arithmetic in a very thorough manner, and his directions
are worthy of careful attention.[394] The third part of Sonnenschein
and Nesbitt’s excellent book on arithmetic[395] describes fully all
kinds of approximate calculations, and shows both how to avoid needless
labour and how to take proper account of inaccuracy in operating with
approximate decimal fractions. A simple investigation of the subject is
to be found in Sonnet’s *Algèbre Elémentaire* (Paris, 1848) chap. xiv.,
“Des Approximations Absolues et Relatives.” There is also an American
work on the subject.[396]
[394] Sandeman, *Pelicotetics*, p. 214.
[395] *The Science and Art of Arithmetic for the Use of Schools.*
(Whitaker and Co.)
[396] *Principles of Approximate Calculations*, by J. J. Skinner,
C.E. (New York, Henry Holt), 1876.
Although the accuracy of measurement has so much advanced since the
time of Leslie, it is not superfluous to repeat his protest against
the unfairness of affecting by a display of decimal fractions a
greater degree of accuracy than the nature of the case requires and
admits.[397] I have known a scientific man to register the barometer
to a second of time when the nearest quarter of an hour would have
been amply sufficient. Chemists often publish results of analysis to
the ten-thousandth or even the millionth part of the whole, when in
all probability the processes employed cannot be depended on beyond
the hundredth part. It is seldom desirable to give more than one
place of figures of uncertain amount; but it must be allowed that a
nice perception of the degree of accuracy possible and desirable is
requisite to save misapprehension and needless computation on the one
hand, and to secure all attainable exactness on the other hand.
[397] Leslie, *Inquiry into the Nature of Heat*, p. 505.