XV. ANALYSIS OF QUANTITATIVE PHENOMENA
In the two preceding chapters we have been engaged in considering how a phenomenon may be accurately measured and expressed. So delicate and complex an operation is a measurement which pretends to any considerable degree of exactness, that no small part of the skill and patience of physicists is usually spent upon this work. Much of this difficulty arises from the fact that it is scarcely ever possible to measure a single effect at a time. The ultimate object must be to discover the mathematical equation or law connecting a quantitative cause with its quantitative effect; this purpose usually involves, as we shall see, the varying of one condition at a time, the other conditions being maintained constant. The labours of the experimentalist would be comparatively light if he could carry out this rule of varying one circumstance at a time. He would then obtain a series of corresponding values of the variable quantities concerned, from which he might by proper hypothetical treatment obtain the required law of connection. But in reality it is seldom possible to carry out this direction except in an approximate manner. Before then we proceed to the consideration of the actual process of quantitative induction, it is necessary to review the several devices by which a complicated series of effects can be disentangled. Every phenomenon measured will usually be the sum, difference, or it may be the product or quotient, of two or more different effects, and these must be in some way analysed and separately measured before we possess the materials for inductive treatment.
*Illustrations of the Complication of Effects.*
It is easy to bring forward a multitude of instances to show that a phenomenon is seldom to be observed simple and alone. A more or less elaborate process of analysis is almost always necessary. Thus if an experimentalist wishes to observe and measure the expansion of a liquid by heat, he places it in a thermometer tube and registers the rise of the column of liquid in the narrow tube. But he cannot heat the liquid without also heating the glass, so that the change observed is really the difference between the expansions of the liquid and the glass. More minute investigation will show the necessity perhaps of allowing for further minute effects, namely the compression of the liquid and the expansion of the bulb due to the increased pressure of the column as it becomes lengthened.
In a great many cases an observed effect will be apparently at least the simple sum of two separate and independent effects. The heat evolved in the combustion of oil is partly due to the carbon and partly to the hydrogen. A measurement of the heat yielded by the two jointly, cannot inform us how much proceeds from the one and how much from the other. If by some separate determination we can ascertain how much the hydrogen yields, then by mere subtraction we learn what is due to the carbon; and *vice versâ*. The heat conveyed by a liquid, may be partly conveyed by true conduction, partly by convection. The light dispersed in the interior of a liquid consists both of what is reflected by floating particles and what is due to true fluorescence;[233] and we must find some mode of determining one portion before we can learn the other. The apparent motion of the spots on the sun, is the algebraic sum of the sun’s axial rotation, and of the proper motion of the spots upon the sun’s surface; hence the difficulty of ascertaining by direct observations the period of the sun’s rotation.
[233] Stokes, *Philosophical Transactions* (1852), vol. cxlii. p. 529.
We cannot obtain the weight of a portion of liquid in a chemical balance without weighing it with the containing vessel. Hence to have the real weight of the liquid operated upon in an experiment, we must make a separate weighing of the vessel, with or without the adhering film of liquid according to circumstances. This is likewise the mode in which a cart and its load are weighed together, the *tare* of the cart previously ascertained being deducted. The variation in the height of the barometer is a joint effect, partly due to the real variation of the atmospheric pressure, partly to the expansion of the mercurial column by heat. The effects may be discriminated, if, instead of one barometer tube we have two tubes containing mercury placed closely side by side, so as to have the same temperature. If one of them be closed at the bottom so as to be unaffected by the atmospheric pressure, it will show the changes due to temperature only, and, by subtracting these changes from those shown in the other tube, employed as a barometer, we get the real oscillations of atmospheric pressure. But this correction, as it is called, of the barometric reading, is better effected by calculation from the readings of an ordinary thermometer.
In other cases a quantitative effect will be the difference of two causes acting in opposite directions. Sir John Herschel invented an instrument like a large thermometer, which he called the Actinometer,[234] and Pouillet constructed a somewhat similar instrument called the Pyrheliometer, for ascertaining the heating power of the sun’s rays. In both instruments the heat of the sun was absorbed by a reservoir containing water, and the rise of temperature of the water was exactly observed, either by its own expansion, or by the readings of a delicate thermometer immersed in it. But in exposing the actinometer to the sun, we do not obtain the full effect of the heat absorbed, because the receiving surface is at the same time radiating heat into empty space. The observed increment of temperature is in short the difference between what is received from the sun and lost by radiation. The latter quantity is capable of ready determination; we have only to shade the instrument from the direct rays of the sun, leaving it exposed to the sky, and we can observe how much it cools in a certain time. The total effect of the sun’s rays will obviously be the apparent effect *plus* the cooling effect in an equal time. By alternate exposure in sun and shade during equal intervals the desired result may be obtained with considerable accuracy.[235]
[234] *Admiralty Manual of Scientific Enquiry*, 2nd ed. p. 299.
[235] Pouillet, *Taylor’s Scientific Memoirs*, vol. iv. p. 45.
Two quantitative effects were beautifully distinguished in an experiment of John Canton, devised in 1761 for the purpose of demonstrating the compressibility of water. He constructed a thermometer with a large bulb full of water and a short capillary tube, the part of which above the water was freed from air. Under these circumstances the water was relieved from the pressure of the atmosphere, but the glass bulb in bearing that pressure was somewhat contracted. He next placed the instrument under the receiver of an air-pump, and on exhausting the air, the water sank in the tube. Having thus obtained a measure of the effect of atmospheric pressure on the bulb, he opened the top of the thermometer tube and admitted the air. The level of the water now sank still more, partly from the pressure on the bulb being now compensated, and partly from the compression of the water by the atmospheric pressure. It is obvious that the amount of the latter effect was approximately the difference of the two observed depressions.
Not uncommonly the actual phenomenon which we wish to measure is considerably less than various disturbing effects which enter into the question. Thus the compressibility of mercury is considerably less than the expansion of the vessels in which it is measured under pressure, so that the attention of the experimentalist has chiefly to be concentrated on the change of magnitude of the vessels. Many astronomical phenomena, such as the parallax or the proper motions of the fixed stars, are far less than the errors caused by instrumental imperfections, or motions arising from precession, nutation, and aberration. We need not be surprised that astronomers have from time to time mistaken one phenomenon for another, as when Flamsteed imagined that he had discovered the parallax of the Pole star.[236]
[236] Baily’s *Account of the Rev. John Flamsteed*, p. 58.
*Methods of Eliminating Error.*
In any particular experiment it is the object of the experimentalist to measure a single effect only, and he endeavours to obtain that effect free from interfering effects. If this cannot be, as it seldom or never can really be, he makes the effect as considerable as possible compared with the other effects, which he reduces to a minimum, and treats as noxious errors. Those quantities, which are called *errors* in one case, may really be most important and interesting phenomena in another investigation. When we speak of eliminating error we really mean disentangling the complicated phenomena of nature. The physicist rightly wishes to treat one thing at a time, but as this object can seldom be rigorously carried into practice, he has to seek some mode of counteracting the irrelevant and interfering causes.
The general principle is that a single observation can render known only a single quantity. Hence, if several different quantitative effects are known to enter into any investigation, we must have at least as many distinct observations as there are quantities to be determined. Every complete experiment will therefore consist in general of several operations. Guided if possible by previous knowledge of the causes in action, we must arrange the determinations, so that by a simple mathematical process we may distinguish the separate quantities. There appear to be five principal methods by which we may accomplish this object; these methods are specified below and illustrated in the succeeding sections.
(1) *The Method of Avoidance.* The physicist may seek for some special mode of experiment or opportunity of observation, in which the error is non-existent or inappreciable.
(2) *The Differential Method.* He may find opportunities of observation when all interfering phenomena remain constant, and only the subject of observation is at one time present and another time absent; the difference between two observations then gives its amount.
(3) *The Method of Correction.* He may endeavour to estimate the amount of the interfering effect by the best available mode, and then make a corresponding correction in the results of observation.
(4) *The Method of Compensation.* He may invent some mode of neutralising the interfering cause by balancing against it an exactly equal and opposite cause of unknown amount.
(5) *The Method of Reversal.* He may so conduct the experiment that the interfering cause may act in opposite directions, in alternate observations, the mean result being free from interference.
I. *Method of Avoidance of Error.*
Astronomers seek opportunities of observation when errors will be as small as possible. In spite of elaborate observations and long-continued theoretical investigation, it is not practicable to assign any satisfactory law to the refractive power of the atmosphere. Although the apparent change of place of a heavenly body produced by refraction may be more or less accurately calculated yet the error depends upon the temperature and pressure of the atmosphere, and, when a ray is highly inclined to the perpendicular, the uncertainty in the refraction becomes very considerable. Hence astronomers always make their observations, if possible, when the object is at the highest point of its daily course, *i.e.* on the meridian. In some kinds of investigation, as, for instance, in the determination of the latitude of an observatory, the astronomer is at liberty to select one or more stars out of the countless number visible. There is an evident advantage in such a case, in selecting a star which passes close to the zenith, so that it may be observed almost entirely free from atmospheric refraction, as was done by Hooke.
Astronomers endeavour to render their clocks as accurate as possible, by removing the source of variation. The pendulum is perfectly isochronous so long as its length remains invariable, and the vibrations are exactly of equal length. They render it nearly invariable in length, that is in the distance between the centres of suspension and oscillation, by a compensatory arrangement for the change of temperature. But as this compensation may not be perfectly accomplished, some astronomers place their chief controlling clock in a cellar, or other apartment, where the changes of temperature may be as slight as possible. At the Paris Observatory a clock has been placed in the caves beneath the building, where there is no appreciable difference between the summer and winter temperature.
To avoid the effect of unequal oscillations Huyghens made his beautiful investigations, which resulted in the discovery that a pendulum, of which the centre of oscillation moved upon a cycloidal path, would be perfectly isochronous, whatever the variation in the length of oscillations. But though a pendulum may be easily rendered in some degree cycloidal by the use of a steel suspension spring, it is found that the mechanical arrangements requisite to produce a truly cycloidal motion introduce more error than they remove. Hence astronomers seek to reduce the error to the smallest amount by maintaining their clock pendulums in uniform movement; in fact, while a clock is in good order and has the same weights, there need be little change in the length of oscillation. When a pendulum cannot be made to swing uniformly, as in experiments upon the force of gravity, it becomes requisite to resort to the third method, and a correction is introduced, calculated on theoretical grounds from the amount of the observed change in the length of vibration.
It has been mentioned that the apparent expansion of a liquid by heat, when contained in a thermometer tube or other vessel, is the difference between the real expansion of the liquid and that of the containing vessel. The effects can be accurately distinguished provided that we can learn the real expansion by heat of any one convenient liquid; for by observing the apparent expansion of the same liquid in any required vessel we can by difference learn the amount of expansion of the vessel due to any given change of temperature. When we once know the change of dimensions of the vessel, we can of course determine the absolute expansion of any other liquid tested in it. Thus it became an all-important object in scientific research to measure with accuracy the absolute dilatation by heat of some one liquid, and mercury owing to several circumstances was by far the most suitable. Dulong and Petit devised a beautiful mode of effecting this by simply avoiding altogether the effect of the change of size of the vessel. Two upright tubes full of mercury were connected by a fine tube at the bottom, and were maintained at two different temperatures. As mercury was free to flow from one tube to the other by the connecting tube, the two columns necessarily exerted equal pressures by the principles of hydrostatics. Hence it was only necessary to measure very accurately by a cathetometer the difference of level of the surfaces of the two columns of mercury, to learn the difference of length of columns of equal hydrostatic pressure, which at once gives the difference of density of the mercury, and the dilatation by heat. The changes of dimension in the containing tubes became a matter of entire indifference, and the length of a column of mercury at different temperatures was measured as easily as if it had formed a solid bar. The experiment was carried out by Regnault with many improvements of detail, and the absolute dilatation of mercury, at temperatures between 0° Cent. and 350°, was determined almost as accurately as was needful.[237]
[237] Jamin, *Cours de Physique*, vol. ii. pp. 15–28.
The presence of a large and uncertain amount of error may render a method of experiment valueless. Foucault devised a beautiful experiment with the pendulum for demonstrating popularly the rotation of the earth, but it could be of no use for measuring the rotation exactly. It is impossible to make the pendulum swing in a perfect plane, and the slightest lateral motion gives it an elliptic path with a progressive motion of the axis of the ellipse, which disguises and often entirely overpowers that due to the rotation of the earth.[238]
[238] *Philosophical Magazine*, 1851, 4th Series, vol. ii. *passim*.
Faraday’s laborious experiments on the relation of gravity and electricity were much obstructed by the fact that it is impossible to move a large weight of metal without generating currents of electricity, either by friction or induction. To distinguish the electricity, if any, directly due to the action of gravity from the greater quantities indirectly produced was a problem of excessive difficulty. Baily in his experiments on the density of the earth was aware of the existence of inexplicable disturbances which have since been referred with much probability to the action of electricity.[239] The skill and ingenuity of the experimentalist are often exhausted in trying to devise a form of apparatus in which such causes of error shall be reduced to a minimum.
[239] Hearn, *Philosophical Transactions*, 1847, vol. cxxxvii. pp. 217–221.
In some rudimentary experiments we wish merely to establish the existence of a quantitative effect without precisely measuring its amount; if there exist causes of error of which we can neither render the amount known or inappreciable, the best way is to make them all negative so that the quantitative effects will be less than the truth rather than greater. Grove, for instance, in proving that the magnetisation or demagnetisation of a piece of iron raises its temperature, took care to maintain the electro-magnet by which the iron was magnetised at a lower temperature than the iron, so that it would cool rather than warm the iron by radiation or conduction.[240]
[240] *The Correlation of Physical Forces*, 3rd ed. p. 159.
Rumford’s celebrated experiment to prove that heat was generated out of mechanical force in the boring of a cannon was subject to the difficulty that heat might be brought to the cannon by conduction from neighbouring bodies. It was an ingenious device of Davy to produce friction by a piece of clock-work resting upon a block of ice in an exhausted receiver; as the machine rose in temperature above 32°, it was certain that no heat was received by conduction from the support.[241] In many other experiments ice may be employed to prevent the access of heat by conduction, and this device, first put in practice by Murray,[242] is beautifully employed in Bunsen’s calorimeter.
[241] *Collected Works of Sir H. Davy*, vol. ii. pp. 12–14. *Elements of Chemical Philosophy*, p. 94.
[242] *Nicholson’s Journal*, vol. i. p. 241; quoted in *Treatise on Heat*, Useful Knowledge Society, p. 24.
To observe the true temperature of the air, though apparently so easy, is really a very difficult matter, because the thermometer is sure to be affected either by the sun’s rays, the radiation from neighbouring objects, or the escape of heat into space. These sources of error are too fluctuating to allow of correction, so that the only accurate mode of procedure is that devised by Dr. Joule, of surrounding the thermometer with a copper cylinder ingeniously adjusted to the temperature of the air, as described by him, so that the effect of radiation shall be nullified.[243]
[243] Clerk Maxwell, *Theory of Heat*, p. 228. *Proceedings of the Manchester Philosophical Society*, Nov. 26, 1867, vol. vii. p. 35.
When the avoidance of error is not practicable, it will yet be desirable to reduce the absolute amount of the interfering error as much as possible before employing the succeeding methods to correct the result. As a general rule we can determine a quantity with less inaccuracy as it is smaller, so that if the error itself be small the error in determining that error will be of a still lower order of magnitude. But in some cases the absolute amount of an error is of no consequence, as in the index error of a divided circle, or the difference between a chronometer and astronomical time. Even the rate at which a clock gains or loses is a matter of little importance provided it remain constant, so that a sure calculation of its amount can be made.
2. *Differential Method.*
When we cannot avoid the existence of error, we can often resort with success to the second mode by measuring phenomena under such circumstances that the error shall remain very nearly the same in all the observations, and neutralise itself as regards the purposes in view. This mode is available whenever we want a difference between quantities and not the absolute quantity of either. The determination of the parallax of the fixed stars is exceedingly difficult, because the amount of parallax is far less than most of the corrections for atmospheric refraction, nutation, aberration, precession, instrumental irregularities, &c., and can with difficulty be detected among these phenomena of various magnitude. But, as Galileo long ago suggested, all such difficulties would be avoided by the differential observation of stars, which, though apparently close together, are really far separated on the line of sight. Two such stars in close apparent proximity will be subject to almost exactly equal errors, so that all we need do is to observe the apparent change of place of the nearer star as referred to the more distant one. A good telescope furnished with an accurate micrometer is alone needed for the application of the method. Huyghens appears to have been the first observer who actually tried to employ the method practically, but it was not until 1835 that the improvement of telescopes and micrometers enabled Struve to detect in this way the parallax of the star α Lyræ. It is one of the many advantages of the observation of transits of Venus for the determination of the solar parallax that the refraction of the atmosphere affects in an exactly equal degree the planet and the portion of the sun’s face over which it is passing. Thus the observations are strictly of a differential nature.
By the process of substitutive weighing it is possible to ascertain the equality or inequality of two weights with almost perfect freedom from error. If two weights A and B be placed in the scales of the best balance we cannot be sure that the equilibrium of the beam indicates exact equality, because the arms of the beam may be unequal or unbalanced. But if we take B out and put another weight C in, and equilibrium still exists, it is apparent that the same causes of erroneous weighing exist in both cases, supposing that the balance has not been disarranged; B then must be exactly equal to C, since it has exactly the same effect under the same circumstances. In like manner it is a general rule that, if by any uniform mechanical process we get a copy of an object, it is unlikely that this copy will be precisely the same as the original in magnitude and form, but two copies will equally diverge from the original, and will therefore almost exactly resemble each other.
Leslie’s Differential Thermometer[244] was well adapted to the experiments for which it was invented. Having two equal bulbs any alteration in the temperature of the air will act equally by conduction on each and produce no change in the indications of the instrument. Only that radiant heat which is purposely thrown upon one of the bulbs will produce any effect. This thermometer in short carries out the principle of the differential method in a mechanical manner.
[244] Leslie, *Inquiry into the Nature of Heat*, p. 10.
3. *Method of Correction.*
Whenever the result of an experiment is affected by an interfering cause to a calculable amount, it is sufficient to add or subtract this amount. We are said to correct observations when we thus eliminate what is due to extraneous causes, although of course we are only separating the correct effects of several agents. The variation in the height of the barometer is partly due to the change of temperature, but since the coefficient of absolute dilatation of mercury has been exactly determined, as already described (p. 341), we have only to make calculations of a simple character, or, what is better still, tabulate a series of such calculations for general use, and the correction for temperature can be made with all desired accuracy. The height of the mercury in the barometer is also affected by capillary attraction, which depresses it by a constant amount depending mainly on the diameter of the tube. The requisite corrections can be estimated with accuracy sufficient for most purposes, more especially as we can check the correctness of the reading of a barometer by comparison with a standard barometer, and introduce if need be an index error including both the error in the affixing of the scale and the effect due to capillarity. But in constructing the standard barometer itself we must take greater precautions; the capillary depression depends somewhat upon the quality of the glass, the absence of air, and the perfect cleanliness of the mercury, so that we cannot assign the exact amount of the effect. Hence a standard barometer is constructed with a wide tube, sometimes even an inch in diameter, so that the capillary effect may be rendered almost zero.[245] Gay-Lussac made barometers in the form of a uniform siphon tube, so that the capillary forces acting at the upper and lower surfaces should balance and destroy each other; but the method fails in practice because the lower surface, being open to the air, becomes sullied and subject to a different force of capillarity.
[245] Jevons, Watts’ *Dictionary of Chemistry*, vol. i. pp. 513–515.
In mechanical experiments friction is an interfering condition, and drains away a portion of the energy intended to be operated upon in a definite manner. We should of course reduce the friction in the first place to the lowest possible amount, but as it cannot be altogether prevented, and is not calculable with certainty from any general laws, we must determine it separately for each apparatus by suitable experiments. Thus Smeaton, in his admirable but almost forgotten researches concerning water-wheels, eliminated friction in the most simple manner by determining by trial what weight, acting by a cord and roller upon his model water-wheel, would make it turn without water as rapidly as the water made it turn. In short, he ascertained what weight concurring with the water would exactly compensate for the friction.[246] In Dr. Joule’s experiments to determine the mechanical equivalent of heat by the condensation of air, a considerable amount of heat was produced by friction of the condensing pump, and a small portion by stirring the water employed to absorb the heat. This heat of friction was measured by simply repeating the experiment in an exactly similar manner except that no condensation was effected, and observing the change of temperature then produced.[247]
[246] *Philosophical Transactions*, vol. li. p. 100.
[247] *Philosophical Magazine*, 3rd Series, vol. xxvi. p. 372.
We may describe as *test experiments* any in which we perform operations not intended to give the quantity of the principal phenomenon, but some quantity which would otherwise remain as an error in the result. Thus in astronomical observations almost every instrumental error may be avoided by increasing the number of observations and distributing them in such a manner as to produce in the final mean as much error in one way as in the other. But there is one source of error, first discovered by Maskelyne, which cannot be thus avoided, because it affects all observations in the same direction and to the same average amount, namely the Personal Error of the observer or the inclination to record the passage of a star across the wires of the telescope a little too soon or a little too late. This personal error was first carefully described in the *Edinburgh Journal of Science*, vol. i. p. 178. The difference between the judgment of observers at the Greenwich Observatory usually varies from 1/100 to 1/3 of a second, and remains pretty constant for the same observers.[248] One practised observer in Sir George Airy’s pendulum experiments recorded all his time observations half a second too early on the average as compared with the chief observer.[249] In some observers it has amounted to seven or eight-tenths of a second.[250] De Morgan appears to have entertained the opinion that this source of error was essentially incapable of elimination or correction.[251] But it seems clear, as I suggested without knowing what had been done,[252] that this personal error might be determined absolutely with any desirable degree of accuracy by test experiments, consisting in making an artificial star move at a considerable distance and recording by electricity the exact moment of its passage over the wire. This method has in fact been successfully employed in Leyden, Paris, and Neuchatel.[253] More recently, observers were trained for the Transit of Venus Expeditions by means of a mechanical model representing the motion of Venus over the sun, this model being placed at a little distance and viewed through a telescope, so that differences in the judgments of different observers would become apparent. It seems likely that tests of this nature might be employed with advantage in other cases.
[248] *Greenwich Observations for* 1866, p. xlix.
[249] *Philosophical Transactions*, 1856, p. 309.
[250] Penny *Cyclopædia*, art. *Transit*, vol. xxv. pp. 129, 130.
[251] Ibid. art. *Observation*, p. 390.
[252] *Nature*, vol. i. p. 85.
[253] *Nature*, vol. i. p 337. See references to the Memoirs describing the method.
Newton employed the pendulum for making experiments on the impact of balls. Two balls were hung in contact, and one of them, being drawn aside through a measured arc, was then allowed to strike the other, the arcs of vibration giving sufficient data for calculating the distribution of energy at the moment of impact. The resistance of the air was an interfering cause which he estimated very simply by causing one of the balls to make several complete vibrations without impact and then marking the reduction in the lengths of the arcs, a proper fraction of which reduction was added to each of the other arcs of vibration when impact took place.[254]
[254] *Principia*, Book I. Law III. Corollary VI. Scholium. Motte’s translation, vol. i. p. 33.
The exact definition of the standard of length is one of the most important, as it is one of the most difficult questions in physical science, and the different practice of different nations introduces needless confusion. Were all standards constructed so as to give the true length at a fixed uniform temperature, for instance the freezing-point, then any two standards could be compared without the interference of temperature by bringing them both to exactly the same fixed temperature. Unfortunately the French metre was defined by a bar of platinum at 0°C, while our yard was defined by a bronze bar at 62°F. It is quite impossible, then, to make a comparison of the yard and metre without the introduction of a correction, either for the expansion of platinum or bronze, or both. Bars of metal differ too so much in their rates of expansion according to their molecular condition that it is dangerous to infer from one bar to another.
When we come to use instruments with great accuracy there are many minute sources of error which must be guarded against. If a thermometer has been graduated when perpendicular, it will read somewhat differently when laid flat, as the pressure of a column of mercury is removed from the bulb. The reading may also be somewhat altered if it has recently been raised to a higher temperature than usual, if it be placed under a vacuous receiver, or if the tube be unequally heated as compared with the bulb. For these minute causes of error we may have to introduce troublesome corrections, unless we adopt the simple precaution of using the thermometer in circumstances of position, &c., exactly similar to those in which it was graduated. There is no end to the number of minute corrections which may ultimately be required. A large number of experiments on gases, standard weights and measures, &c., depend upon the height of the barometer; but when experiments in different parts of the world are compared together we ought as a further refinement to take into account the varying force of gravity, which even between London and Paris makes a difference of ·008 inch of mercury.
The measurement of quantities of heat is a matter of great difficulty, because there is no known substance impervious to heat, and the problem is therefore as difficult as to measure liquids in porous vessels. To determine the latent heat of steam we must condense a certain amount of the steam in a known weight of water, and then observe the rise of temperature of the water. But while we are carrying out the experiment, part of the heat will escape by radiation and conduction from the condensing vessel or calorimeter. We may indeed reduce the loss of heat by using vessels with double sides and bright surfaces, surrounded with swans-down wool or other non-conducting materials; and we may also avoid raising the temperature of the water much above that of the surrounding air. Yet we cannot by any such means render the loss of heat inconsiderable. Rumford ingeniously proposed to reduce the loss to zero by commencing the experiment when the temperature of the calorimeter is as much below that of the air as it is at the end of the experiment above it. Thus the vessel will first gain and then lose by radiation and conduction, and these opposite errors will approximately balance each other. But Regnault has shown that the loss and gain do not proceed by exactly the same laws, so that in very accurate investigations Rumford’s method is not sufficient. There remains the method of correction which was beautifully carried out by Regnault in his determination of the latent heat of steam. He employed two calorimeters, made in exactly the same way and alternately used to condense a certain amount of steam, so that while one was measuring the latent heat, the other calorimeter was engaged in determining the corrections to be applied, whether on account of radiation and conduction from the vessel or on account of heat reaching the vessel by means of the connecting pipes.[255]
[255] Graham’s *Chemical Reports and Memoirs*, Cavendish Society, pp. 247, 268, &c.
4. *Method of Compensation.*
There are many cases in which a cause of error cannot conveniently be rendered null, and is yet beyond the reach of the third method, that of calculating the requisite correction from independent observations. The magnitude of an error may be subject to continual variations, on account of change of weather, or other fickle circumstances beyond our control. It may either be impracticable to observe the variation of those circumstances in sufficient detail, or, if observed, the calculation of the amount of error may be subject to doubt. In these cases, and only in these cases, it will be desirable to invent some artificial mode of counterpoising the variable error against an equal error subject to exactly the same variation.
We cannot weigh an object with great accuracy unless we make a correction for the weight of the air displaced by the object, and add this to the apparent weight. In very accurate investigations relating to standard weights, it is usual to note the barometer and thermometer at the time of making a weighing, and, from the measured bulks of the objects compared, to calculate the weight of air displaced; the third method in fact is adopted. To make these calculations in the frequent weighings requisite in chemical analysis would be exceedingly laborious, hence the correction is usually neglected. But when the chemist wishes to weigh gas contained in a large glass globe for the purpose of determining its specific gravity, the correction becomes of much importance. Hence chemists avoid at once the error, and the labour of correcting it, by attaching to the opposite scale of the balance a dummy sealed glass globe of equal capacity to that containing the gas to be weighed, noting only the difference of weight when the operating globe is full and empty. The correction, being the same for both globes, may be entirely neglected.[256]
[256] Regnault’s *Cours Elémentaire de Chimie*, 1851, vol i. p. 141.
A device of nearly the same kind is employed in the construction of galvanometers which measure the force of an electric current by the deflection of a suspended magnetic needle. The resistance of the needle is partly due to the directive influence of the earth’s magnetism, and partly to the torsion of the thread. But the former force may often be inconveniently great as well as troublesome to determine for different inclinations. Hence it is customary to connect together two equally magnetised needles, with their poles pointing in opposite directions, one needle being within and another without the coil of wire. As regards the earth’s magnetism, the needles are now *astatic* or indifferent, the tendency of one needle towards the pole being balanced by that of the other.
An elegant instance of the elimination of a disturbing force by compensation is found in Faraday’s researches upon the magnetism of gases. To observe the magnetic attraction or repulsion of a gas seems impossible unless we enclose the gas in an envelope, probably best made of glass. But any such envelope is sure to be more or less affected by the magnet, so that it becomes difficult to distinguish between three forces which enter into the problem, namely, the magnetism of the gas in question, that of the envelope, and that of the surrounding atmospheric air. Faraday avoided all difficulties by employing two equal and similar glass tubes connected together, and so suspended from the arm of a torsion balance that the tubes were in similar parts of the magnetic field. One tube being filled with nitrogen and the other with oxygen, it was found that the oxygen seemed to be attracted and the nitrogen repelled. The suspending thread of the balance was then turned until the force of torsion restored the tubes to their original places, where the magnetism of the tubes as well as that of the surrounding air, being the same and in the opposite directions upon the two tubes, could not produce any interference. The force required to restore the tubes was measured by the amount of torsion of the thread, and it indicated correctly the difference between the attractive powers of oxygen and nitrogen. The oxygen was then withdrawn from one of the tubes, and a second experiment made, so as to compare a vacuum with nitrogen. No force was now required to maintain the tubes in their places, so that nitrogen was found to be, approximately speaking, indifferent to the magnet, that is, neither magnetic nor diamagnetic, while oxygen was proved to be positively magnetic.[257] It required the highest experimental skill on the part of Faraday and Tyndall, to distinguish between what is apparent and real in magnetic attraction and repulsion.
[257] Tyndall’s *Faraday*, pp. 114, 115.
Experience alone can finally decide when a compensating arrangement is conducive to accuracy. As a general rule mechanical compensation is the last resource, and in the more accurate observations it is likely to introduce more uncertainty than it removes. A multitude of instruments involving mechanical compensation have been devised, but they are usually of an unscientific character,[258] because the errors compensated can be more accurately determined and allowed for. But there are exceptions to this rule, and it seems to be proved that in the delicate and tiresome operation of measuring a base line, invariable bars, compensated for expansion by heat, give the most accurate results. This arises from the fact that it is very difficult to determine accurately the temperature of the measuring bars under varying conditions of weather and manipulation.[259] Again, the last refinement in the measurement of time at Greenwich Observatory depends upon mechanical compensation. Sir George Airy, observing that the standard clock increased its losing rate 0·30 second for an increase of one inch in atmospheric pressure, placed a magnet moved by a barometer in such a position below the pendulum, as almost entirely to neutralise this cause of irregularity. The thorough remedy, however, would be to remove the cause of error altogether by placing the clock in a vacuous case.
[258] See, for instance, the Compensated Sympiesometer, *Philosophical Magazine*, 4th Series, vol. xxxix. p. 371.
[259] Grant, *History of Physical Astronomy*, pp. 146, 147.
We thus see that the choice of one or other mode of eliminating an error depends entirely upon circumstances and the object in view; but we may safely lay down the following conclusions. First of all, seek to avoid the source of error altogether if it can be conveniently done; if not, make the experiment so that the error may be as small, but more especially as constant, as possible. If the means are at hand for determining its amount by calculation from other experiments and principles of science, allow the error to exist and make a correction in the result. If this cannot be accurately done or involves too much labour for the purposes in view, then throw in a counteracting error which shall as nearly as possible be of equal amount in all circumstances with that to be eliminated. There yet remains, however, one important method, that of Reversal, which will form an appropriate transition to the succeeding chapters on the Method of Mean Results and the Law of Error.
5. *Method of Reversal.*
The fifth method of eliminating error is most potent and satisfactory when it can be applied, but it requires that we shall be able to reverse the apparatus and mode of procedure, so as to make the interfering cause act alternately in opposite directions. If we can get two experimental results, one of which is as much too great as the other is too small, the error is equal to half the difference, and the true result is the mean of the two apparent results. It is an unavoidable defect of the chemical balance, for instance, that the points of suspension of the pans cannot be fixed at exactly equal distances from the centre of suspension of the beam. Hence two weights which seem to balance each other will never be quite equal in reality. The difference is detected by reversing the weights, and it may be estimated by adding small weights to the deficient side to restore equilibrium, and then taking as the true weight the geometric mean of the two apparent weights of the same object. If the difference is small, the arithmetic mean, that is half the sum, may be substituted for the geometric mean, from which it will not appreciably differ.
This method of reversal is most extensively employed in practical astronomy. The apparent elevation of a heavenly body is observed by a telescope moving upon a divided circle, upon which the inclination of the telescope is read off. Now this reading will be erroneous if the circle and the telescope have not accurately the same centre. But if we read off at the same time both ends of the telescope, the one reading will be about as much too small as the other is too great, and the mean will be nearly free from error. In practice the observation is differently conducted, but the principle is the same; the telescope is fixed to the circle, which moves with it, and the angle through which it moves is read off at three, six, or more points, disposed at equal intervals round the circle. The older astronomers, down even to the time of Flamsteed, were accustomed to use portions only of a divided circle, generally quadrants, and Römer made a vast improvement when he introduced the complete circle.
The transit circle, employed to determine the meridian passage of heavenly bodies, is so constructed that the telescope and the axis bearing it, in fact the whole moving part of the instrument, can be taken out of the bearing sockets and turned over, so that what was formerly the western pivot becomes the eastern one, and *vice versâ*. It is impossible that the instrument could have been so perfectly constructed, mounted, and adjusted that the telescope should point exactly to the meridian, but the effect of the reversal is that it will point as much to the west in one position as it does to the east in the other, and the mean result of observations in the two positions must be free from such cause of error.
The accuracy with which the inclination of the compass needle can be determined depends almost entirely on the method of reversal. The dip needle consists of a bar of magnetised steel, suspended somewhat like the beam of a delicate balance on a slender axis passing through the centre of gravity of the bar, so that it is at liberty to rest in that exact degree of inclination in the magnetic meridian which the magnetism of the earth induces. The inclination is read off upon a vertical divided circle, but to avoid error arising from the centring of the needle and circle, both ends are read, and the mean of the results is taken. The whole instrument is now turned carefully round through 180°, which causes the needle to assume a new position relatively to the circle and gives two new readings, in which any error due to the wrong position of the zero of the division will be reversed. As the axis of the needle may not be exactly horizontal, it is now reversed in the same manner as the transit instrument, the end of the axis which formerly pointed east being made to point west, and a new set of four readings is taken.
Finally, error may arise from the axis not passing accurately through the centre of gravity of the bar, and this error can only be detected and eliminated on changing the magnetic poles of the bar by the application of a strong magnet. The error is thus made to act in opposite directions. To ensure all possible accuracy each reversal ought to be combined with each other reversal, so that the needle will be observed in eight different positions by sixteen readings, the mean of the whole of which will give the required inclination free from all eliminable errors.[260]
[260] Quetelet, *Sur la Physique du Globe*, p. 174. Jamin, *Cours de Physique*, vol. i. p. 504.Return to passage
There are certain cases in which a disturbing cause can with ease be made to act in opposite directions, in alternate observations, so that the mean of the results will be free from disturbance. Thus in direct experiments upon the velocity of sound in passing through the air between stations two or three miles apart, the wind is a cause of error. It will be well, in the first place, to choose a time for the experiment when the air is very nearly at rest, and the disturbance slight, but if at the same moment signal sounds be made at each station and observed at the other, two sounds will be passing in opposite directions through the same body of air and the wind will accelerate one sound almost exactly as it retards the other. Again, in trigonometrical surveys the apparent height of a point will be affected by atmospheric refraction and the curvature of the earth. But if in the case of two points the apparent elevation of each as seen from the other be observed, the corrections will be the same in amount, but reversed in direction, and the mean between the two apparent differences of altitude will give the true difference of level.
In the next two chapters we really pursue the Method of Reversal into more complicated applications.
XVI. THE METHOD OF MEANS
All results of the measurement of continuous quantity can be only approximately true. Were this assertion doubted, it could readily be proved by direct experience. If any person, using an instrument of the greatest precision, makes and registers successive observations in an unbiassed manner, it will almost invariably be found that the results differ from each other. When we operate with sufficient care we cannot perform so simple an experiment as weighing an object in a good balance without getting discrepant numbers. Only the rough and careless experimenter will think that his observations agree, but in reality he will be found to overlook the differences. The most elaborate researches, such as those undertaken in connection with standard weights and measures, always render it apparent that complete coincidence is out of the question, and that the more accurate our modes of observation are rendered, the more numerous are the sources of minute error which become apparent. We may look upon the existence of error in all measurements as the normal state of things. It is absolutely impossible to eliminate separately the multitude of small disturbing influences, except by balancing them off against each other. Even in drawing a mean it is to be expected that we shall come near the truth rather than exactly to it. In the measurement of continuous quantity, absolute coincidence, if it seems to occur, must be only apparent, and is no indication of precision. It is one of the most embarrassing things we can meet when experimental results agree too closely. Such coincidences should raise our suspicion that the apparatus in use is in some way restricted in its operation, so as not really to give the true result at all, or that the actual results have not been faithfully recorded by the assistant in charge of the apparatus.
If then we cannot get twice over exactly the same result, the question arises, How can we ever attain the truth or select the result which may be supposed to approach most nearly to it? The quantity of a certain phenomenon is expressed in several numbers which differ from each other; no more than one of them at the most can be true, and it is more probable that they are all false. It may be suggested, perhaps, that the observer should select the one observation which he judged to be the best made, and there will often doubtless be a feeling that one or more results were satisfactory, and the others less trustworthy. This seems to have been the course adopted by the early astronomers. Flamsteed, when he had made several observations of a star, probably chose in an arbitrary manner that which seemed to him nearest to the truth.[261]
[261] Baily’s *Account of Flamsteed*, p. 376.
When Horrocks selected for his estimate of the sun’s semi-diameter a mean between the results of Kepler and Tycho, he professed not to do it from any regard to the idle adage, “Medio tutissimus ibis,” but because he thought it from his own observations to be correct.[262] But this method will not apply at all when the observer has made a number of measurements which are equally good in his opinion, and it is quite apparent that in using an instrument or apparatus of considerable complication the observer will not necessarily be able to judge whether slight causes have affected its operation or not.
[262] *The Transit of Venus across the Sun*, by Horrocks, London, 1859, p. 146.
In this question, as indeed throughout inductive logic, we deal only with probabilities. There is no infallible mode of arriving at the absolute truth, which lies beyond the reach of human intellect, and can only be the distant object of our long-continued and painful approximations. Nevertheless there is a mode pointed out alike by common sense and the highest mathematical reasoning, which is more likely than any other, as a general rule, to bring us near the truth. The ἄριστον μέτρον, or the *aurea mediocritas*, was highly esteemed in the ancient philosophy of Greece and Rome; but it is not probable that any of the ancients should have been able clearly to analyse and express the reasons why they advocated the *mean* as the safest course. But in the last two centuries this apparently simple question of the mean has been found to afford a field for the exercise of the utmost mathematical skill. Roger Cotes, the editor of the *Principia*, appears to have had some insight into the value of the mean; but profound mathematicians such as De Moivre, Daniel Bernoulli, Laplace, Lagrange, Gauss, Quetelet, De Morgan, Airy, Leslie Ellis, Boole, Glaisher, and others, have hardly exhausted the subject.
*Several uses of the Mean Result.*
The elimination of errors of unknown sources, is almost always accomplished by the simple arithmetical process of taking the *mean*, or, as it is often called, the *average* of several discrepant numbers. To take an average is to add the several quantities together, and divide by the number of quantities thus added, which gives a quotient lying among, or in the *middle* of, the several quantities. Before however inquiring fully into the grounds of this procedure, it is essential to observe that this one arithmetical process is really applied in at least three different cases, for different purposes, and upon different principles, and we must take great care not to confuse one application of the process with another. A *mean result*, then, may have any one of the following significations.
(1) It may give a merely representative number, expressing the general magnitude of a series of quantities, and serving as a convenient mode of comparing them with other series of quantities. Such a number is properly called *The fictitious mean* or *The average result*.
(2) It may give a result approximately free from disturbing quantities, which are known to affect some results in one direction, and other results equally in the opposite direction. We may say that in this case we get a *Precise mean result*.
(3) It may give a result more or less free from unknown and uncertain errors; this we may call the *Probable mean result*.
Of these three uses of the mean the first is entirely different in nature from the two last, since it does not yield an approximation to any natural quantity, but furnishes us with an arithmetic result comparing the aggregate of certain quantities with their number. The third use of the mean rests entirely upon the theory of probability, and will be more fully considered in a later part of this chapter. The second use is closely connected, or even identical with, the Method of Reversal already described, but it will be desirable to enter somewhat fully into all the three employments of the same arithmetical process.
*The Mean and the Average.*
Much confusion exists in the popular, or even the scientific employment of the terms *mean* and *average*, and they are commonly taken as synonymous. It is necessary to ascertain carefully what significations we ought to attach to them. The English word *mean* is equivalent to *medium*, being derived, perhaps through the French *moyen*, from the Latin *medius*, which again is undoubtedly kindred with the Greek μεσος. Etymologists believe, too, that this Greek word is connected with the preposition μετα, the German *mitte*, and the true English *mid* or *middle*; so that after all the *mean* is a technical term identical in its root with the more popular equivalent *middle*.
If we inquire what is the mean in a mathematical point of view, the true answer is that there are several or many kinds of means. The old arithmeticians recognised ten kinds, which are stated by Boethius, and an eleventh was added by Jordanus.[263]
[263] De Morgan, Supplement to the *Penny Cyclopædia*, art. *Old Appellations of Numbers*.
The *arithmetic mean* is the one by far the most commonly denoted by the term, and that which we may understand it to signify in the absence of any qualification. It is the sum of a series of quantities divided by their number, and may be represented by the formula 1/2(*a* + *b*). But there is also the *geometric mean*, which is the square root of the product, √(*a* × *b*), or that quantity the logarithm of which is the arithmetic mean of the logarithms of the quantities. There is also the *harmonic mean*, which is the reciprocal of the arithmetic mean of the reciprocals of the quantities. Thus if *a* and *b* be the quantities, as before, their reciprocals are 1/*a* and 1/*b*, the mean of which is 1/2 (1/*a* + 1/*b*), and the reciprocal again is (2*ab*)/(*a* + *b*), which is the harmonic mean. Other kinds of means might no doubt be invented for particular purposes, and we might apply the term, as De Morgan pointed out,[264] to any quantity a function of which is equal to a function of two or more other quantities, and is such that the interchange of these latter quantities among themselves will make no alteration in the value of the function. Symbolically, if Φ(*y*, *y*, *y* ....) = Φ(*x*{1}, *x*{2}, *x*{3} ....), then *y* is a kind of mean of the quantities, *x*{1}, *x*_{2}, &c.
[264] *Penny Cyclopædia*, art. *Mean*.
The geometric mean is necessarily adopted in certain cases. When we estimate the work done against a force which varies inversely as the square of the distance from a fixed point, the mean force is the geometric mean between the forces at the beginning and end of the path. When in an imperfect balance, we reverse the weights to eliminate error, the true weight will be the geometric mean of the two apparent weights. In almost all the calculations of statistics and commerce the geometric mean ought, strictly speaking, to be used. If a commodity rises in price 100 per cent. and another remains unaltered, the mean rise of a price is not 50 per cent. because the ratio 150 : 200 is not the same as 100 : 150. The mean ratio is as unity to √(1·00 × 2·00) or 1 to 1·41. The difference between the three kinds of means in such a case[265] is very considerable; while the rise of price estimated by the Arithmetic mean would be 50 per cent. it would be only 41 and 33 per cent. respectively according to the Geometric and Harmonic means.
[265] Jevons, *Journal of the Statistical Society*, June 1865, vol. xxviii, p. 296.
In all calculations concerning the average rate of progress of a community, or any of its operations, the geometric mean should be employed. For if a quantity increases 100 per cent. in 100 years, it would not on the average increase 10 per cent. in each ten years, as the 10 per cent. would at the end of each decade be calculated upon larger and larger quantities, and give at the end of 100 years much more than 100 per cent., in fact as much as 159 per cent. The true mean rate in each decade would be ^{10}√2 or about 1·07, that is, the increase would be about 7 per cent. in each ten years. But when the quantities differ very little, the arithmetic and geometric means are approximately the same. Thus the arithmetic mean of 1·000 and 1·001 is 1·0005, and the geometric mean is about 1·0004998, the difference being of an order inappreciable in almost all scientific and practical matters. Even in the comparison of standard weights by Gauss’ method of reversal, the arithmetic mean may usually be substituted for the geometric mean which is the true result.
Regarding the mean in the absence of express qualification to the contrary as the common arithmetic mean, we must still distinguish between its two uses where it gives with more or less accuracy and probability a really existing quantity, and where it acts as a mere representative of other quantities. If I make many experiments to determine the atomic weight of an element, there is a certain number which I wish to approximate to, and the mean of my separate results will, in the absence of any reasons to the contrary, be the most probable approximate result. When we determine the mean density of the earth, it is not because any part of the earth is of that exact density; there may be no part exactly corresponding to the mean density, and as the crust of the earth has only about half the mean density, the internal matter of the globe must of course be above the mean. Even the density of a homogeneous substance like carbon or gold must be regarded as a mean between the real density of its atoms, and the zero density of the intervening vacuous space.
The very different signification of the word “mean” in these two uses was fully explained by Quetelet,[266] and the importance of the distinction was pointed out by Sir John Herschel in reviewing his work.[267] It is much to be desired that scientific men would mark the difference by using the word *mean* only in the former sense when it denotes approximation to a definite existing quantity; and *average*, when the mean is only a fictitious quantity, used for convenience of thought and expression. The etymology of this word “average” is somewhat obscure; but according to De Morgan[268] it comes from *averia*, “havings or possessions,” especially applied to farm stock. By the accidents of language *averagium* came to mean the labour of farm horses to which the lord was entitled, and it probably acquired in this manner the notion of distributing a whole into parts, a sense in which it was early applied to maritime averages or contributions of the other owners of cargo to those whose goods have been thrown overboard or used for the safety of the vessel.
[266] *Letters on the Theory of Probabilities*, transl. by Downes, Part ii.
[267] Herschel’s *Essays*, &c. pp. 404, 405.
[268] *On the Theory of Errors of Observations, Cambridge Philosophical Transactions*, vol. x. Part ii. 416.
*On the Average or Fictitious Mean.*
Although the average when employed in its proper sense of a fictitious mean, represents no really existing quantity, it is yet of the highest scientific importance, as enabling us to conceive in a single result a multitude of details. It enables us to make a hypothetical simplification of a problem, and avoid complexity without committing error. The weight of a body is the sum of the weights of infinitely small particles, each acting at a different place, so that a mechanical problem resolves itself, strictly speaking, into an infinite number of distinct problems. We owe to Archimedes the first introduction of the beautiful idea that one point may be discovered in a gravitating body such that the weight of all the particles may be regarded as concentrated in that point, and yet the behaviour of the whole body will be exactly represented by the behaviour of this heavy point. This Centre of Gravity may be within the body, as in the case of a sphere, or it may be in empty space, as in the case of a ring. Any two bodies, whether connected or separate, may be conceived as having a centre of gravity, that of the sun and earth lying within the sun and only 267 miles from its centre.
Although we most commonly use the notion of a centre or average point with regard to gravity, the same notion is applicable to other cases. Terrestrial gravity is a case of approximately parallel forces, and the centre of gravity is but a special case of the more general Centre of Parallel Forces. Wherever a number of forces of whatever amount act in parallel lines, it is possible to discover a point at which the algebraic sum of the forces may be imagined to act with exactly the same effect. Water in a cistern presses against the side with a pressure varying according to the depth, but always in a direction perpendicular to the side. We may then conceive the whole pressure as exerted on one point, which will be one-third from the bottom of the cistern, and may be called the Centre of Pressure. The Centre of Oscillation of a pendulum, discovered by Huyghens, is that point at which the whole weight of the pendulum may be considered as concentrated, without altering the time of oscillation (p. 315). When one body strikes another the Centre of Percussion is that point in the striking body at which all its mass might be concentrated without altering the effect of the stroke. In position the Centre of Percussion does not differ from the Centre of Oscillation. Mathematicians have also described the Centre of Gyration, the Centre of Conversion, the Centre of Friction, &c.
We ought carefully to distinguish between those cases in which an *invariable* centre can be assigned, and those in which it cannot. In perfect strictness, there is no such thing as a true invariable centre of gravity. As a general rule a body is capable of possessing an invariable centre only for perfectly parallel forces, and gravity never does act in absolutely parallel lines. Thus, as usual, we find that our conceptions are only hypothetically correct, and only approximately applicable to real circumstances. There are indeed certain geometrical forms called *Centrobaric*,[269] such that a body of that shape would attract another exactly as if the mass were concentrated at the centre of gravity, whether the forces act in a parallel manner or not. Newton showed that uniform spheres of matter have this property, and this truth proved of the greatest importance in simplifying his calculations. But it is after all a purely hypothetical truth, because we can nowhere meet with, nor can we construct, a perfectly spherical and homogeneous body. The slightest irregularity or protrusion from the surface will destroy the rigorous correctness of the assumption. The spheroid, on the other hand, has no invariable centre at which its mass may always be regarded as concentrated. The point from which its resultant attraction acts will move about according to the distance and position of the other attracting body, and it will only coincide with the centre as regards an infinitely distant body whose attractive forces may be considered as acting in parallel lines.
[269] Thomson and Tait, *Treatise on Natural Philosophy*, vol. i. p. 394.
Physicists speak familiarly of the poles of a magnet, and the term may be used with convenience. But, if we attach any definite meaning to the word, the poles are not the ends of the magnet, nor any fixed points within, but the variable points from which the resultants of all the forces exerted by the particles in the bar upon exterior magnetic particles may be considered as acting. The poles are, in short, Centres of Magnetic Forces; but as those forces are never really parallel, these centres will vary in position according to the relative place of the object attracted. Only when we regard the magnet as attracting a very distant, or, strictly speaking, infinitely distant particle, do its centres become fixed points, situated in short magnets approximately at one-sixth of the whole length from each end of the bar. We have in the above instances of centres or poles of force sufficient examples of the mode in which the Fictitious Mean or Average is employed in physical science.
*The Precise Mean Result.*
We now turn to that mode of employing the mean result which is analogous to the method of reversal, but which is brought into practice in a most extensive manner throughout many branches of physical science. We find the simplest possible case in the determination of the latitude of a place by observations of the Pole-star. Tycho Brahe suggested that if the elevation of any circumpolar star were observed at its higher and lower passages across the meridian, half the sum of the elevations would be the latitude of the place, which is equal to the height of the pole. Such a star is as much above the pole at its highest passage, as it is below at its lowest, so that the mean must necessarily give the height of the pole itself free from doubt, except as regards incidental errors. The Pole-star is usually selected for the purpose of such observations because it describes the smallest circle, and is thus on the whole least affected by atmospheric refraction.
Whenever several causes are in action, each of which at one time increases and at another time decreases the joint effect by equal quantities, we may apply this method and disentangle the effects. Thus the solar and lunar tides roll on in almost complete independence of each other. When the moon is new or full the solar tide coincides, or nearly so, with that caused by the moon, and the joint effect is the sum of the separate effects. When the moon is in quadrature, or half full, the two tides are acting in opposition, one raising and the other depressing the water, so that we observe only the difference of the effects. We have in fact--
Spring tide = lunar tide + solar tide; Neap tide = lunar tide - solar tide.
We have only then to add together the heights of the maximum spring tide and the minimum neap tide, and half the sum is the true height of the lunar tide. Half the difference of the spring and neap tides on the other hand gives the solar tide.
Effects of very small amount may be detected with great approach to certainty among much greater fluctuations, provided that we have a series of observations sufficiently numerous and long continued to enable us to balance all the larger effects against each other. For this purpose the observations should be continued over at least one complete cycle, in which the effects run through all their variations, and return exactly to the same relative positions as at the commencement. If casual or irregular disturbing causes exist, we should probably require many such cycles of results to render their effect inappreciable. We obtain the desired result by taking the mean of all the observations in which a cause acts positively, and the mean of all in which it acts negatively. Half the difference of these means will give the effect of the cause in question, provided that no other effect happens to vary in the same period or nearly so.
Since the moon causes a movement of the ocean, it is evident that its attraction must have some effect upon the atmosphere. The laws of atmospheric tides were investigated by Laplace, but as it would be impracticable by theory to calculate their amounts we can only determine them by observation, as Laplace predicted that they would one day be determined.[270] But the oscillations of the barometer thus caused are far smaller than the oscillations due to several other causes. Storms, hurricanes, or changes of weather produce movements of the barometer sometimes as much as a thousand times as great as the tides in question. There are also regular daily, yearly, or other fluctuations, all greater than the desired quantity. To detect and measure the atmospheric tide it was desirable that observations should be made in a place as free as possible from irregular disturbances. On this account several long series of observations were made at St. Helena, where the barometer is far more regular in its movements than in a continental climate. The effect of the moon’s attraction was then detected by taking the mean of all the readings when the moon was on the meridian and the similar mean when she was on the horizon. The difference of these means was found to be only ·00365, yet it was possible to discover even the variation of this tide according as the moon was nearer to or further from the earth, though this difference was only ·00056 inch.[271] It is quite evident that such minute effects could never be discovered in a purely empirical manner. Having no information but the series of observations before us, we could have no clue as to the mode of grouping them which would give so small a difference. In applying this method of means in an extensive manner we must generally then have *à priori* knowledge as to the periods at which a cause will act in one direction or the other.
[270] *Essai Philosophique sur les Probabilités*, pp. 49, 50.
[271] Grant, *History of Physical Astronomy*, p. 163.
We are sometimes able to eliminate fluctuations and take a mean result by purely mechanical arrangements. The daily variations of temperature, for instance, become imperceptible one or two feet below the surface of the earth, so that a thermometer placed with its bulb at that depth gives very nearly the true daily mean temperature. At a depth of twenty feet even the yearly fluctuations are nearly effaced, and the thermometer stands a little above the true mean temperature of the locality. In registering the rise and fall of the tide by a tide-gauge, it is desirable to avoid the oscillations arising from surface waves, which is very readily accomplished by placing the float in a cistern communicating by a small hole with the sea. Only a general rise or fall of the level is then perceptible, just as in the marine barometer the narrow tube prevents any casual fluctuations and allows only a continued change of pressure to manifest itself.
*Determination of the Zero point.*
In many important observations the chief difficulty consists in defining exactly the zero point from which we are to measure. We can point a telescope with great precision to a star and can measure to a second of arc the angle through which the telescope is raised or lowered; but all this precision will be useless unless we know exactly the centre point of the heavens from which we measure, or, what comes to the same thing, the horizontal line 90° distant from it. Since the true horizon has reference to the figure of the earth at the place of observation, we can only determine it by the direction of gravity, as marked either by the plumb-line or the surface of a liquid. The question resolves itself then into the most accurate mode of observing the direction of gravity, and as the plumb-line has long been found hopelessly inaccurate, astronomers generally employ the surface of mercury in repose as the criterion of horizontality. They ingeniously observe the direction of the surface by making a star the index. From the laws of reflection it follows that the angle between the direct ray from a star and that reflected from a surface of mercury will be exactly double the angle between the surface and the direct ray from the star. Hence the horizontal or zero point is the mean between the apparent place of any star or other very distant object and its reflection in mercury.
A plumb-line is perpendicular, or a liquid surface is horizontal only in an approximate sense; for any irregularity of the surface of the earth, a mountain, or even a house must cause some deviation by its attracting power. To detect such deviation might seem very difficult, because every other plumb-line or liquid surface would be equally affected by gravity. Nevertheless it can be detected; for if we place one plumb-line to the north of a mountain, and another to the south, they will be about equally deflected in opposite directions, and if by observations of the same star we can measure the angle between the plumb-lines, half the inclination will be the deviation of either, after allowance has been made for the inclination due to the difference of latitude of the two places of observation. By this mode of observation applied to the mountain Schiehallion the deviation of the plumb-line was accurately measured by Maskelyne, and thus a comparison instituted between the attractive forces of the mountain and the whole globe, which led to a probable estimate of the earth’s density.
In some cases it is actually better to determine the zero point by the average of equally diverging quantities than by direct observation. In delicate weighings by a chemical balance it is requisite to ascertain exactly the point at which the beam comes to rest, and when standard weights are being compared the position of the beam is ascertained by a carefully divided scale viewed through a microscope. But when the beam is just coming to rest, friction, small impediments or other accidental causes may readily obstruct it, because it is near the point at which the force of stability becomes infinitely small. Hence it is found better to let the beam vibrate and observe the terminal points of the vibrations. The mean between two extreme points will nearly indicate the position of rest. Friction and the resistance of air tend to reduce the vibrations, so that this mean will be erroneous by half the amount of this effect during a half vibration. But by taking several observations we may determine this retardation and allow for it. Thus if *a*, *b*, *c* be the readings of the terminal points of three excursions of the beam from the zero of the scale, then 1/2(*a* + *b*) will be about as much erroneous in one direction as 1/2(*b* + *c*) in the other, so that the mean of these two means, or 1/4(*a* + 2*b* + *c*), will be exceedingly near to the point of rest.[272] A still closer approximation may be made by taking four readings and reducing them by the formula 1/6(*a* + 2*b* + 2*c* + *d*).
[272] Gauss, Taylor’s *Scientific Memoirs*, vol. ii. p. 43, &c.
The accuracy of Baily’s experiments, directed to determine the density of the earth, entirely depended upon this mode of observing oscillations. The balls whose gravitation was measured were so delicately suspended by a torsion balance that they never came to rest. The extreme points of the oscillations were observed both when the heavy leaden attracting ball was on one side and on the other. The difference of the mean points when the leaden ball was on the right hand and that when it was on the left hand gave double the amount of the deflection.
A beautiful instance of avoiding the use of a zero point is found in Mr. E. J. Stone’s observations on the radiant heat of the fixed stars. The difficulty of these observations arose from the comparatively great amounts of heat which were sent into the telescope from the atmosphere, and which were sufficient to disguise almost entirely the feeble heat rays of a star. But Mr. Stone fixed at the focus of his telescope a double thermo-electric pile of which the two parts were reversed in order. Now any disturbance of temperature which acted uniformly upon both piles produced no effect upon the galvanometer needle, and when the rays of the star were made to fall alternately upon one pile and the other, the total amount of the deflection represented double the heating power of the star. Thus Mr. Stone was able to detect with much certainty a heating effect of the star Arcturus, which even when concentrated by the telescope amounted only to 0°·02 Fahr., and which represents a heating effect of the direct ray of only about 0°·00000137 Fahr., equivalent to the heat which would be received from a three-inch cubic vessel full of boiling water at the distance of 400 yards.[273] It is probable that Mr. Stone’s arrangement of the pile might be usefully employed in other delicate thermometric experiments subject to considerable disturbing influences.
[273] *Proceedings of the Royal Society*, vol. xviii. p. 159 (Jan. 13, 1870). *Philosophical Magazine* (4th Series), vol. xxxix. p. 376.
*Determination of Maximum Points.*
We employ the method of means in a certain number of observations directed to determine the moment at which a phenomenon reaches its highest point in quantity. In noting the place of a fixed star at a given time there is no difficulty in ascertaining the point to be observed, for a star in a good telescope presents an exceedingly small disc. In observing a nebulous body which from a bright centre fades gradually away on all sides, it will not be possible to select with certainty the middle point. In many such cases the best method is not to select arbitrarily the supposed middle point, but points of equal brightness on either side, and then take the mean of the observations of these two points for the centre. As a general rule, a variable quantity in reaching its maximum increases at a less and less rate, and after passing the highest point begins to decrease by insensible degrees. The maximum may indeed be defined as that point at which the increase or decrease is null. Hence it will usually be the most indefinite point, and if we can accurately measure the phenomenon we shall best determine the place of the maximum by determining points on either side at which the ordinates are equal. There is moreover this advantage in the method that several points may be determined with the corresponding ones on the other side, and the mean of the whole taken as the true place of the maximum. But this method entirely depends upon the existence of symmetry in the curve, so that of two equal ordinates one shall be as far on one side of the maximum as the other is on the other side. The method fails when other laws of variation prevail.
In tidal observations great difficulty is encountered in fixing the moment of high water, because the rate at which the water is then rising or falling, is almost imperceptible. Whewell proposed, therefore, to note the time at which the water passes a fixed point somewhat below the maximum both in rising and falling, and take the mean time as that of high water. But this mode of proceeding unfortunately does not give a correct result, because the tide follows different laws in rising and in falling. There is a difficulty again in selecting the highest spring tide, another object of much importance in tidology. Laplace discovered that the tide of the second day preceding the conjunction of the sun and moon is nearly equal to that of the fifth day following; and, believing that the increase and decrease of the tides proceeded in a nearly symmetrical manner, he decided that the highest tide would occur about thirty-six hours after the conjunction, that is half-way between the second day before and the fifth day after.[274]
[274] Airy *On Tides and Waves*, Encycl. Metrop. pp. 364*-366*.
This method is also employed in determining the time of passage of the middle or densest point of a stream of meteors. The earth takes two or three days in passing completely through the November stream; but astronomers need for their calculations to have some definite point fixed within a few minutes if possible. When near to the middle they observe the numbers of meteors which come within the sphere of vision in each half hour, or quarter hour, and then, assuming that the law of variation is symmetrical, they select a moment for the passage of the centre equidistant between times of equal frequency.
The eclipses of Jupiter’s satellites are not only of great interest as regards the motions of the satellites themselves, but were, and perhaps still are, of use in determining longitudes, because they are events occurring at fixed moments of absolute time, and visible in all parts of the planetary system at the same time, allowance being made for the interval occupied by the light in travelling. But, as is explained by Herschel,[275] the moment of the event is wanting in definiteness, partly because the long cone of Jupiter’s shadow is surrounded by a penumbra, and partly because the satellite has itself a sensible disc, and takes time in entering the shadow. Different observers using different telescopes would usually select different moments for that of the eclipse. But the increase of light in the emersion will proceed according to a law the reverse of that observed in the immersion, so that if an observer notes the time of both events with the same telescope, he will be as much too soon in one observation as he is too late in the other, and the mean moment of the two observations will represent with considerable accuracy the time when the satellite is in the middle of the shadow. Error of judgment of the observer is thus eliminated, provided that he takes care to act at the emersion as he did at the immersion.
[275] *Outlines of Astronomy*, 4th edition, § 538.Return to passage
XVII. THE LAW OF ERROR
To bring error itself under law might seem beyond human power. He who errs surely diverges from law, and it might be deemed hopeless out of error to draw truth. One of the most remarkable achievements of the human intellect is the establishment of a general theory which not only enables us among discrepant results to approximate to the truth, but to assign the degree of probability which fairly attaches to this conclusion. It would be a mistake indeed to suppose that this law is necessarily the best guide under all circumstances. Every measuring instrument and every form of experiment may have its own special law of error; there may in one instrument be a tendency in one direction and in another in the opposite direction. Every process has its peculiar liabilities to disturbance, and we are never relieved from the necessity of providing against special difficulties. The general Law of Error is the best guide only when we have exhausted all other means of approximation, and still find discrepancies, which are due to unknown causes. We must treat such residual differences in some way or other, since they will occur in all accurate experiments, and as their origin is assumed to be unknown, there is no reason why we should treat them differently in different cases. Accordingly the ultimate Law of Error must be a uniform and general one.
It is perfectly recognised by mathematicians that in each case a special Law of Error may exist, and should be discovered if possible. “Nothing can be more unlikely than that the errors committed in all classes of observations should follow the same law,”[276] and the special Laws of Error which will apply to certain instruments, as for instance the repeating circle, have been investigated by Bravais.[277] He concludes that every distinct cause of error gives rise to a curve of possibility of errors, which may have any form,--a curve which we may either be able or unable to discover, and which in the first case may be determined by *à priori* considerations on the peculiar nature of this cause, or which may be determined *à posteriori* by observation. Whenever it is practicable and worth the labour, we ought to investigate these special conditions of error; nevertheless, when there are a great number of different sources of minute error, the general resultant will always tend to obey that general law which we are about to consider.
[276] *Philosophical Magazine*, 3rd Series, vol. xxxvii. p. 324.
[277] *Letters on the Theory of Probabilities*, by Quetelet, translated by O. G. Downes, Notes to Letter XXVI. pp. 286–295.
*Establishment of the Law of Error.*
Mathematicians agree far better as to the form of the Law of Error than they do as to the manner in which it can be deduced and proved. They agree that among a number of discrepant results of observation, that mean quantity is probably the best approximation to the truth which makes the sum of the squares of the errors as small as possible. But there are three principal ways in which this law has been arrived at respectively by Gauss, by Laplace and Quetelet, and by Sir John Herschel. Gauss proceeds much upon assumption; Herschel rests upon geometrical considerations; while Laplace and Quetelet regard the Law of Error as a development of the doctrine of combinations. A number of other mathematicians, such as Adrain of New Brunswick, Bessel, Ivory, Donkin, Leslie Ellis, Tait, and Crofton have either attempted independent proofs or have modified or commented on those here to be described. For full accounts of the literature of the subject the reader should refer either to Mr. Todhunter’s *History of the Theory of Probability* or to the able memoir of Mr. J. W. L. Glaisher.[278]
[278] *On the Law of Facility of Errors of Observations, and on the Method of Least Squares*, Memoirs of the Royal Astronomical Society, vol. xxxix. p. 75.
According to Gauss the Law of Error expresses the comparative probability of errors of various magnitude, and partly from experience, partly from *à priori* considerations, we may readily lay down certain conditions to which the law will certainly conform. It may fairly be assumed as a first principle to guide us in the selection of the law, that large errors will be far less frequent and probable than small ones. We know that very large errors are almost impossible, so that the probability must rapidly decrease as the amount of the error increases. A second principle is that positive and negative errors shall be equally probable, which may certainly be assumed, because we are supposed to be devoid of any knowledge as to the causes of the residual errors. It follows that the probability of the error must be a function of an even power of the magnitude, that is of the square, or the fourth power, or the sixth power, otherwise the probability of the same amount of error would vary according as the error was positive or negative. The even powers *x*^{2}, *x*^{4}, *x*^{6}, &c., are always intrinsically positive, whether *x* be positive or negative. There is no *à priori* reason why one rather than another of these even powers should be selected. Gauss himself allows that the fourth or sixth power would fulfil the conditions as well as the second;[279] but in the absence of any theoretical reasons we should prefer the second power, because it leads to formulæ of great comparative simplicity. Did the Law of Error necessitate the use of the higher powers of the error, the complexity of the necessary calculations would much reduce the utility of the theory.
[279] *Méthode des Moindres Carrés. Mémoires sur la Combinaison des Observations, par Ch. Fr. Gauss. Traduit en Français par J. Bertrand*, Paris, 1855, pp. 6, 133, &c.
By mathematical reasoning which it would be undesirable to attempt to follow in this book, it is shown that under these conditions, the facility of occurrence, or in other, words, the probability of error is expressed by a function of the general form ε^{–*h*^{2} *x*^{2}}, in which *x* represents the variable amount of errors. From this law, to be more fully described in the following sections, it at once follows that the most probable result of any observations is that which makes the sum of the squares of the consequent errors the least possible. Let *a*, *b*, *c*, &c., be the results of observation, and *x* the quantity selected as the most probable, that is the most free from unknown errors: then we must determine *x* so that (*a* - *x*)^{2} + (*b* - *x*)^{2} + (*c* - *x*)^{2} + ... shall be the least possible quantity. Thus we arrive at the celebrated *Method of Least Squares*, as it is usually called, which appears to have been first distinctly put in practice by Gauss in 1795, while Legendre first published in 1806 an account of the process in his work, entitled, *Nouvelles Méthodes pour la Détermination des Orbites des Comètes*. It is worthy of notice, however, that Roger Cotes had long previously recommended a method of equivalent nature in his tract, “Estimatio Erroris in Mixta Mathesi.”[280]
[280] De Morgan, *Penny Cyclopædia*, art. *Least Squares*.
*Herschel’s Geometrical Proof.*
A second way of arriving at the Law of Error was proposed by Herschel, and although only applicable to geometrical cases, it is remarkable as showing that from whatever point of view we regard the subject, the same principle will be detected. After assuming that some general law must exist, and that it is subject to the principles of probability, he supposes that a ball is dropped from a high point with the intention that it shall strike a given mark on a horizontal plane. In the absence of any known causes of deviation it will either strike that mark, or, as is infinitely more probable, diverge from it by an amount which we must regard as error of unknown origin. Now, to quote the words of Herschel,[281] “the probability of that error is the unknown function of its square, *i.e.* of the sum of the squares of its deviations in any two rectangular directions. Now, the probability of any deviation depending solely on its magnitude, and not on its direction, it follows that the probability of each of these rectangular deviations must be the same function of *its* square. And since the observed oblique deviation is equivalent to the two rectangular ones, supposed concurrent, and which are essentially independent of one another, and is, therefore, a compound event of which they are the simple independent constituents, therefore its probability will be the product of their separate probabilities. Thus the form of our unknown function comes to be determined from this condition, viz., that the product of such functions of two independent elements is equal to the same function of their sum. But it is shown in every work on algebra that this property is the peculiar characteristic of, and belongs only to, the exponential or antilogarithmic function. This, then, is the function of the square of the error, which expresses the probability of committing that error. That probability decreases, therefore, in geometrical progression, as the square of the error increases in arithmetical.”
[281] *Edinburgh Review*, July 1850, vol. xcii. p. 17. Reprinted *Essays*, p. 399. This method of demonstration is discussed by Boole, *Transactions of Royal Society of Edinburgh*, vol. xxi. pp. 627–630.
*Laplace’s and Quetelet’s Proof of the Law.*
However much presumption the modes of determining the Law of Error, already described, may give in favour of the law usually adopted, it is difficult to feel that the arguments are satisfactory. The law adopted is chosen rather on the grounds of convenience and plausibility, than because it can be seen to be the necessary law. We can however approach the subject from an entirely different point of view, and yet get to the same result.
Let us assume that a particular observation is subject to four chances of error, each of which will increase the result one inch if it occurs. Each of these errors is to be regarded as an event independent of the rest and we can therefore assign, by the theory of probability, the comparative probability and frequency of each conjunction of errors. From the Arithmetical Triangle (pp. 182–188) we learn that no error at all can happen only in one way; an error of one inch can happen in 4 ways; and the ways of happening of errors of 2, 3 and 4 inches respectively, will be 6, 4 and 1 in number.
We may infer that the error of two inches is the most likely to occur, and will occur in the long run in six cases out of sixteen. Errors of one and three inches will be equally likely, but will occur less frequently; while no error at all, or one of four inches will be a comparatively rare occurrence. If we now suppose the errors to act as often in one direction as the other, the effect will be to alter the average error by the amount of two inches, and we shall have the following results:--
Negative error of 2 inches 1 way. Negative error of 1 inch 4 ways. No error at all 6 ways. Positive error of 1 inch 4 ways. Positive error of 2 inches 1 way.
We may now imagine the number of causes of error increased and the amount of each error decreased, and the arithmetical triangle will give us the frequency of the resulting errors. Thus if there be five positive causes of error and five negative causes, the following table shows the numbers of errors of various amount which will be the result:--
+----------------------+-------------------+---+-------------------+ | Direction of Error. | Positive Error. | | Negative Error. | +----------------------+-------------------+---+-------------------+ | Amount of Error. |5, 4, 3, 2, 1| 0 | 1, 2, 3, 4, 5| +----------------------+-------------------+---+-------------------+ |Number of such Errors.|1, 10, 45, 120, 210|252|210, 120, 45, 10, 1| +----------------------+-------------------+---+-------------------+
It is plain that from such numbers I can ascertain the probability of any particular amount of error under the conditions supposed. The probability of a positive error of exactly one inch is 210/1024, in which fraction the numerator is the number of combinations giving one inch positive error, and the denominator the whole number of possible errors of all magnitudes. I can also, by adding together the appropriate numbers get the probability of an error not exceeding a certain amount. Thus the probability of an error of three inches or less, positive or negative, is a fraction whose numerator is the sum of 45 + 120 + 210 + 252 + 210 + 120 + 45, and the denominator, as before, giving the result 1002/1024. We may see at once that, according to these principles, the probability of small errors is far greater than of large ones: the odds are 1002 to 22, or more than 45 to 1, that the error will not exceed three inches; and the odds are 1022 to 2 against the occurrence of the greatest possible error of five inches.
If any case should arise in which the observer knows the number and magnitude of the chief errors which may occur, he ought certainly to calculate from the Arithmetical Triangle the special Law of Error which would apply. But the general law, of which we are in search, is to be used in the dark, when we have no knowledge whatever of the sources of error. To assume any special number of causes of error is then an arbitrary proceeding, and mathematicians have chosen the least arbitrary course of imagining the existence of an infinite number of infinitely small errors, just as, in the inverse method of probabilities, an infinite number of infinitely improbable hypotheses were submitted to calculation (p. 255).
The reasons in favour of this choice are of several different kinds.
1. It cannot be denied that there may exist infinitely numerous causes of error in any act of observation.
2. The law resulting from the hypothesis of a moderate number of causes of error, does not appreciably differ from that given by the hypothesis of an infinite number of causes of error.
3. We gain by the hypothesis of infinity a general law capable of ready calculation, and applicable by uniform rules to all problems.
4. This law, when tested by comparison with extensive series of observations, is strikingly verified, as will be shown in a later section.
When we imagine the existence of any large number of causes of error, for instance one hundred, the numbers of combinations become impracticably large, as may be seen to be the case from a glance at the Arithmetical Triangle, which proceeds only up to the seventeenth line. Quetelet, by suitable abbreviating processes, calculated out a table of probability of errors on the hypothesis of one thousand distinct causes;[282] but mathematicians have generally proceeded on the hypothesis of infinity, and then, by the devices of analysis, have substituted a general law of easy treatment. In mathematical works upon the subject, it is shown that the standard Law of Error is expressed in the formula
*y* = *Y*ε^{-*cx*^{2}},
[282] *Letters on the Theory of Probabilities*, Letter XV. and Appendix, note pp. 256–266.
in which *x* is the amount of the error, *Y* the maximum ordinate of the curve of error, and *c* a number constant for each series of observations, and expressing the amount of the tendency to error, varying between one series of observations and another. The letter ε is the mathematical constant, the sum of ratios between the numbers of permutations and combinations, previously referred to (p. 330).
To show the close correspondence of this general law with the special law which might be derived from the supposition of a moderate number of causes of error, I have in the accompanying figure drawn a curved line representing accurately the variation of *y* when *x* in the above formula is taken equal 0, 1/2, 1, 3/2, 2, &c., positive or negative, the arbitrary quantities *Y* and *c* being each assumed equal to unity, in order to simplify the calculations. In the same figure are inserted eleven dots, whose heights above the base line are proportional to the numbers in the eleventh line of the Arithmetical Triangle, thus representing the comparative probabilities of errors of various amounts arising from ten equal causes of error. The correspondence of the general and the special Law of Error is almost as close as can be exhibited in the figure, and the assumption of a greater number of equal causes of error would render the correspondence far more close.
It may be explained that the ordinates NM, *nm*, *n′m′*, represent values of *y* in the equation expressing the Law of Error. The occurrence of any one definite amount of error is infinitely improbable, because an infinite number of such ordinates might be drawn. But the probability of an error occurring between certain limits is finite, and is represented by a portion of the *area* of the curve. Thus the probability that an error, positive or negative, not exceeding unity will occur, is represented by the area M*mnn′m′*, in short, by the area standing upon the line *nn′*. Since every observation must either have some definite error or none at all, it follows that the whole area of the curve should be considered as the unit expressing certainty, and the probability of an error falling between particular limits will then be expressed by the ratio which the area of the curve between those limits bears to the whole area of the curve.
The mere fact that the Law of Error allows of the possible existence of errors of every assignable amount shows that it is only approximately true. We may fairly say that in measuring a mile it would be impossible to commit an error of a hundred miles, and the length of life would never allow of our committing an error of one million miles. Nevertheless the general Law of Error would assign a probability for an error of that amount or more, but so small a probability as to be utterly inconsiderable and almost inconceivable. All that can, or in fact need, be said in defence of the law is, that it may be made to represent the errors in any special case to a very close approximation, and that the probability of large and practically impossible errors, as given by the law, will be so small as to be entirely inconsiderable. And as we are dealing with error itself, and our results pretend to nothing more than approximation and probability, an indefinitely small error in our process of approximation is of no importance whatever.
*Logical Origin of the Law of Error.*
It is worthy of notice that this Law of Error, abstruse though the subject may seem, is really founded upon the simplest principles. It arises entirely out of the difference between permutations and combinations, a subject upon which I may seem to have dwelt with unnecessary prolixity in previous pages (pp. 170, 189). The order in which we add quantities together does not affect the amount of the sum, so that if there be three positive and five negative causes of error in operation, it does not matter in which order they are considered as acting. They may be intermixed in any arrangement, and yet the result will be the same. The reader should not fail to notice how laws or principles which appeared to be absurdly simple and evident when first noticed, reappear in the most complicated and mysterious processes of scientific method. The fundamental Laws of Identity and Difference gave rise to the Logical Alphabet which, after abstracting the character of the differences, led to the Arithmetical Triangle. The Law of Error is defined by an infinitely high line of that triangle, and the law proves that the mean is the most probable result, and that divergencies from the mean become much less probable as they increase in amount. Now the comparative greatness of the numbers towards the middle of each line of the Arithmetical Triangle is entirely due to the indifference of order in space or time, which was first prominently pointed out as a condition of logical relations, and the symbols indicating them (pp. 32–35), and which was afterwards shown to attach equally to numerical symbols, the derivatives of logical terms (p. 160).
*Verification of the Law of Error.*
The theory of error which we have been considering rests entirely upon an assumption, namely that when known sources of disturbances are allowed for, there yet remain an indefinite, possibly an infinite number of other minute sources of error, which will as often produce excess as deficiency. Granting this assumption, the Law of Error must be as it is usually taken to be, and there is no more need to verify it empirically than to test the truth of one of Euclid’s propositions mechanically. Nevertheless, it is an interesting occupation to verify even the propositions of geometry, and it is still more instructive to try whether a large number of observations will justify our assumption of the Law of Error.
Encke has given an excellent instance of the correspondence of theory with experience, in the case of observations of the differences of Right Ascension of the sun and two stars, namely α Aquilæ and α Canis minoris. The observations were 470 in number, and were made by Bradley and reduced by Bessel, who found the probable error of the final result to be only about one-fourth part of a second (0·2637). He then compared the numbers of errors of each magnitude from 0·1 second upwards, as actually given by the observations, with what should occur according to the Law of Error.
The results were as follow:--[283]
+-------------------------+--------------------------+ | | Number of errors of each | | Magnitude of the errors | magnitude according to | | in parts of a second. +-------------+------------+ | | Observation.| Theory. | +-------------------------+-------------+------------+ | 0·0 to 0·1 | 94 | 95 | | ·1 " ·2 | 88 | 89 | | ·2 " ·3 | 78 | 78 | | ·3 " ·4 | 58 | 64 | | ·4 " ·5 | 51 | 50 | | ·5 " ·6 | 36 | 36 | | ·6 " ·7 | 26 | 24 | | ·7 " ·8 | 14 | 15 | | ·8 " ·9 | 10 | 9 | | ·9 " 1·0 | 7 | 5 | | above 1·0 | 8 | 5 | +-------------------------+-------------+------------+
[283] Encke, *On the Method of Least Squares*, Taylor’s *Scientific Memoirs*, vol. ii. pp. 338, 339.
The reader will remark that the correspondence is very close, except as regards larger errors, which are excessive in practice. It is one objection, indeed, to the theory of error, that, being expressed in a continuous mathematical function, it contemplates the existence of errors of every magnitude, such as could not practically occur; yet in this case the theory seems to under-estimate the number of large errors.
Another comparison of the law with observation was made by Quetelet, who investigated the errors of 487 determinations in time of the Right Ascension of the Pole-Star made at Greenwich during the four years 1836–39. These observations, although carefully corrected for all known causes of error, as well as for nutation, precession, &c., are yet of course found to differ, and being classified as regards intervals of one-half second of time, and then proportionately increased in number, so that their sum may be one thousand, give the following results as compared with what Quetelet’s theory would lead us to expect:--[284]
+------------+--------------------+------------+--------------------+ |Magnitude of| Number of Errors |Magnitude of| Number of Errors | | error +------------+-------+ error +------------+-------+ | in tenths | by | by | in tenths | by | by | |of a second.|Observation.|Theory.|of a second.|Observation.|Theory.| +------------+------------+-------+------------+------------+-------+ | 0·0 | 168 | 163 | -- | -- | -- | | +0·5 | 148 | 147 | -0·5 | 150 | 152 | | +1·0 | 129 | 112 | -1·0 | 126 | 121 | | +1·5 | 78 | 72 | -1·5 | 74 | 82 | | +2·0 | 33 | 40 | -2·0 | 43 | 46 | | +2·5 | 10 | 19 | -2·5 | 25 | 22 | | +3·0 | 2 | 10 | -3·0 | 12 | 10 | | -- | -- | -- | -3·5 | 2 | 4 | +------------+------------+-------+------------+------------+-------+
[284] Quetelet, *Letters on the Theory of Probabilities*, translated by Downes, Letter XIX. p. 88. See also Galton’s *Hereditary Genius*, p. 379.
In this instance also the correspondence is satisfactory, but the divergence between theory and fact is in the opposite direction to that discovered in the former comparison, the larger errors being less frequent than theory would indicate. It will be noticed that Quetelet’s theoretical results are not symmetrical.
*The Probable Mean Result.*
One immediate result of the Law of Error, as thus stated, is that the mean result is the most probable one; and when there is only a single variable this mean is found by the familiar arithmetical process. An unfortunate error has crept into several works which allude to this subject. Mill, in treating of the “Elimination of Chance,” remarks in a note[285] that “the mean is spoken of as if it were exactly the same thing as the average. But the mean, for purposes of inductive inquiry, is not the average, or arithmetical mean, though in a familiar illustration of the theory the difference may be disregarded.” He goes on to say that, according to mathematical principles, the most probable result is that for which the sums of the squares of the deviations is the least possible. It seems probable that Mill and other writers were misled by Whewell, who says[286] that “The method of least squares is in fact a method of means, but with some peculiar characters.... The method proceeds upon this supposition: that all errors are not equally probable, but that small errors are more probable than large ones.” He adds that this method “removes much that is arbitrary in the method of means.” It is strange to find a mathematician like Whewell making such remarks, when there is no doubt whatever that the Method of Means is only an application of the Method of Least Squares. They are, in fact, the same method, except that the latter method may be applied to cases where two or more quantities have to be determined at the same time. Lubbock and Drinkwater say,[287] “If only one quantity has to be determined, this method evidently resolves itself into taking the mean of all the values given by observation.” Encke says,[288] that the expression for the probability of an error “not only contains in itself the principle of the arithmetical mean, but depends so immediately upon it, that for all those magnitudes for which the arithmetical mean holds good in the simple cases in which it is principally applied, no other law of probability can be assumed than that which is expressed by this formula.”
[285] *System of Logic*, bk. iii. chap. 17, § 3. 5th ed. vol. ii. p. 56.
[286] *Philosophy of the Inductive Sciences*, 2nd ed. vol. ii. pp. 408, 409.
[287] *Essay on Probability*, Useful Knowledge Society, 1833, p. 41.
[288] Taylor’s *Scientific Memoirs*, vol. ii. p. 333.
*The Probable Error of Results.*
When we draw a conclusion from the numerical results of observations we ought not to consider it sufficient, in cases of importance, to content ourselves with finding the simple mean and treating it as true. We ought also to ascertain what is the degree of confidence we may place in this mean, and our confidence should be measured by the degree of concurrence of the observations from which it is derived. In some cases the mean may be approximately certain and accurate. In other cases it may really be worth little or nothing. The Law of Error enables us to give exact expression to the degree of confidence proper in any case; for it shows how to calculate the probability of a divergence of any amount from the mean, and we can thence ascertain the probability that the mean in question is within a certain distance from the true number. The *probable error* is taken by mathematicians to mean the limits within which it is as likely as not that the truth will fall. Thus if 5·45 be the mean of all the determinations of the density of the earth, and ·20 be approximately the probable error, the meaning is that the probability of the real density of the earth falling between 5·25 and 5·65 is 1/2. Any other limits might have been selected at will. We might calculate the limits within which it was one hundred or one thousand to one that the truth would fall; but there is a convention to take the even odds one to one, as the quantity of probability of which the limits are to be estimated.
Many books on probability give rules for making the calculations, but as, in the progress of science, persons ought to become more familiar with these processes, I propose to repeat the rules here and illustrate their use. The calculations, when made in accordance with the directions, involve none but arithmetic or logarithmic operations.
The following are the rules for treating a mean result, so as thoroughly to ascertain its trustworthiness.
1. Draw the mean of all the observed results.
2. Find the excess or defect, that is, the error of each result from the mean.
3. Square each of these reputed errors.
4. Add together all these squares of the errors, which are of course all positive.
5. Divide by one less than the number of observations. This gives the *square of the mean error*.
6. Take the square root of the last result; it is the *mean error of a single observation*.
7. Divide now by the square root of the number of observations, and we get the *mean error of the mean result*.
8. Lastly, multiply by the natural constant 0·6745 (or approximately by 0·674, or even by 2/3), and we arrive at the *probable error of the mean result*.
Suppose, for instance, that five measurements of the height of a hill, by the barometer or otherwise, have given the numbers of feet as 293, 301, 306, 307, 313; we want to know the probable error of the mean, namely 304. Now the differences between this mean and the above numbers, *paying no regard to direction*, are 11, 3, 2, 3, 9; their squares are 121, 9, 4, 9, 81, and the sum of the squares of the errors consequently 224. The number of observations being 5, we divide by 1 less, or 4, getting 56. This is the square of the mean error, and taking its square root we have 7·48 (say 7-1/2), the mean error of a single observation. Dividing by 2·236, the square root of 5, the number of observations, we find the mean error of the *mean* result to be 3·35, or say 3-1/3, and lastly, multiplying by ·6745, we arrive at the *probable error of the mean result*, which is found to be 2·259, or say 2-1/4. The meaning of this is that the probability is one half, or the odds are even that the true height of the mountain lies between 301-3/4 and 306-1/4 feet. We have thus an exact measure of the degree of credibility of our mean result, which mean indicates the most likely point for the truth to fall upon.
The reader should observe that as the object in these calculations is only to gain a notion of the degree of confidence with which we view the mean, there is no real use in carrying the calculations to any great degree of precision; and whenever the neglect of decimal fractions, or even the slight alteration of a number, will much abbreviate the computations, it may be fearlessly done, except in cases of high importance and precision. Brodie has shown how the law of error may be usefully applied in chemical investigations, and some illustrations of its employment may be found in his paper.[289]
[289] *Philosophical Transactions*, 1873, p. 83.
The experiments of Benzenberg to detect the revolution of the earth, by the deviation of a ball from the perpendicular line in falling down a deep pit, have been cited by Encke[290] as an interesting illustration of the Law of Error. The mean deviation was 5·086 lines, and its probable error was calculated by Encke to be not more than ·950 line, that is, the odds were even that the true result lay between 4·136 and 6·036. As the deviation, according to astronomical theory, should be 4·6 lines, which lies well within the limits, we may consider that the experiments are consistent with the Copernican system of the universe.
[290] Taylor’s *Scientific Memoirs*, vol. ii. pp. 330, 347, &c.
It will of course be understood that the probable error has regard only to those causes of errors which in the long run act as much in one direction as another; it takes no account of constant errors. The true result accordingly will often fall far beyond the limits of probable error, owing to some considerable constant error or errors, of the existence of which we are unaware.
*Rejection of the Mean Result.*
We ought always to bear in mind that the mean of any series of observations is the best, that is, the most probable approximation to the truth, only in the absence of knowledge to the contrary. The selection of the mean rests entirely upon the probability that unknown causes of error will in the long run fall as often in one direction as the opposite, so that in drawing the mean they will balance each other. If we have any reason to suppose that there exists a tendency to error in one direction rather than the other, then to choose the mean would be to ignore that tendency. We may certainly approximate to the length of the circumference of a circle, by taking the mean of the perimeters of inscribed and circumscribed polygons of an equal and large number of sides. The length of the circular line undoubtedly lies between the lengths of the two perimeters, but it does not follow that the mean is the best approximation. It may in fact be shown that the circumference of the circle is *very nearly* equal to the perimeter of the inscribed polygon, together with one-third part of the difference between the inscribed and circumscribed polygons of the same number of sides. Having this knowledge, we ought of course to act upon it, instead of trusting to probability.
We may often perceive that a series of measurements tends towards an extreme limit rather than towards a mean. In endeavouring to obtain a correct estimate of the apparent diameter of the brightest fixed stars, we find a continuous diminution in estimates as the powers of observation increased. Kepler assigned to Sirius an apparent diameter of 240 seconds; Tycho Brahe made it 126; Gassendi 10 seconds; Galileo, Hevelius, and J. Cassini, 5 or 6 seconds. Halley, Michell, and subsequently Sir W. Herschel came to the conclusion that the brightest stars in the heavens could not have real discs of a second, and were probably much less in diameter. It would of course be absurd to take the mean of quantities which differ more than 240 times; and as the tendency has always been to smaller estimates, there is a considerable presumption in favour of the smallest.[291]
[291] Quetelet, *Letters*, &c. p. 116.
In many experiments and measurements we know that there is a preponderating tendency to error in one direction. The readings of a thermometer tend to rise as the age of the instrument increases, and no drawing of means will correct this result. Barometers, on the other hand, are likely to read too low instead of too high, owing to the imperfection of the vacuum and the action of capillary attraction. If the mercury be perfectly pure and no appreciable error be due to the measuring apparatus, the best barometer will be that which gives the highest result. In determining the specific gravity of a solid body the chief danger of error arises from bubbles of air adhering to the body, which would tend to make the specific gravity too small. Much attention must always be given to one-sided errors of this kind, since the multiplication of experiments does not remove the error. In such cases one very careful experiment is better than any number of careless ones.
When we have reasonable grounds for supposing that certain experimental results are liable to grave errors, we should exclude them in drawing a mean. If we want to find the most probable approximation to the velocity of sound in air, it would be absurd to go back to the old experiments which made the velocity from 1200 to 1474 feet per second; for we know that the old observers did not guard against errors arising from wind and other causes. Old chemical experiments are valueless as regards quantitative results. The old chemists found the atmosphere in different places to differ in composition nearly ten per cent., whereas modern accurate experimenters find very slight variations. Any method of measurement which we know to avoid a source of error is far to be preferred to others which trust to probabilities for the elimination of the error. As Flamsteed says,[292] “One good instrument is of as much worth as a hundred indifferent ones.” But an instrument is good or bad only in a comparative sense, and no instrument gives invariable and truthful results. Hence we must always ultimately fall back upon probabilities for the selection of the final mean, when other precautions are exhausted.
[292] Baily, *Account of Flamsteed*, p. 56.
Legendre, the discoverer of the method of Least Squares, recommended that observations differing very much from the results of his method should be rejected. The subject has been carefully investigated by Professor Pierce, who has proposed a criterion for the rejection of doubtful observations based on the following principle:[293]′“--observations should be rejected when the probability of the system of errors obtained by retaining them is less than that of the system of errors obtained by their rejection multiplied by the probability of making so many and no more abnormal observations.” Professor Pierce’s investigation is given nearly in his own words in Professor W. Chauvenet’s “Manual of Spherical and Practical Astronomy,” which contains a full and excellent discussion of the methods of treating numerical observations.[294]
[293] Gould’s *Astronomical Journal*, Cambridge, Mass., vol. ii. p. 161.
[294] Philadelphia (London, Trübner) 1863. Appendix, vol. ii. p. 558.
Very difficult questions sometimes arise when one or more results of a method of experiment diverge widely from the mean of the rest. Are we or are we not to exclude them in adopting the supposed true mean result of the method? The drawing of a mean result rests, as I have frequently explained, upon the assumption that every error acting in one direction will probably be balanced by other errors acting in an opposite direction. If then we know or can possibly discover any causes of error not agreeing with this assumption, we shall be justified in excluding results which seem to be affected by this cause.
In reducing large series of astronomical observations, it is not uncommon to meet with numbers differing from others by a whole degree or half a degree, or some considerable integral quantity. These are errors which could hardly arise in the act of observation or in instrumental irregularity; but they might readily be accounted for by misreading of figures or mistaking of division marks. It would be absurd to trust to chance that such mistakes would balance each other in the long run, and it is therefore better to correct arbitrarily the supposed mistake, or better still, if new observations can be made, to strike out the divergent numbers altogether. When results come sometimes too great or too small in a regular manner, we should suspect that some part of the instrument slips through a definite space, or that a definite cause of error enters at times, and not at others. We should then make it a point of prime importance to discover the exact nature and amount of such an error, and either prevent its occurrence for the future or else introduce a corresponding correction. In many researches the whole difficulty will consist in this detection and avoidance of sources of error. Professor Roscoe found that the presence of phosphorus caused serious and almost unavoidable errors in the determination of the atomic weight of vanadium.[295] Herschel, in reducing his observations of double stars at the Cape of Good Hope, was perplexed by an unaccountable difference of the angles of position as measured by the seven-feet equatorial and the twenty-feet reflector telescopes, and after a careful investigation was obliged to be contented with introducing a correction experimentally determined.[296]
[295] Bakerian Lecture, *Philosophical Transactions* (1868), vol. clviii. p. 6.
[296] *Results of Observations at the Cape of Good Hope*, p. 283.
When observations are sufficiently numerous it seems desirable to project the apparent errors into a curve, and then to observe whether this curve exhibits the symmetrical and characteristic form of the curve of error. If so, it may be inferred that the errors arise from many minute independent sources, and probably compensate each other in the mean result. Any considerable irregularity will indicate the existence of one-sided or large causes of error, which should be made the subject of investigation.
Even the most patient and exhaustive investigations will sometimes fail to disclose any reason why some results diverge from others. The question again recurs--Are we arbitrarily to exclude them? The answer should be in the negative as a general rule. The mere fact of divergence ought not to be taken as conclusive against a result, and the exertion of arbitrary choice would open the way to the fatal influence of bias, and what is commonly known as the “cooking” of figures. It would amount to judging fact by theory instead of theory by fact. The apparently divergent number may prove in time to be the true one. It may be an exception of that valuable kind which upsets our false theories, a real exception, exploding apparent coincidences, and opening a way to a new view of the subject. To establish this position for the divergent fact will require additional research; but in the meantime we should give it some weight in our mean conclusions, and should bear in mind the discrepancy as one demanding attention. To neglect a divergent result is to neglect the possible clue to a great discovery.
*Method of Least Squares.*
When two or more unknown quantities are so involved that they cannot be separately determined by the Simple Method of Means, we can yet obtain their most probable values by the Method of Least Squares, without more difficulty than arises from the length of the arithmetical computations. If the result of each observation gives an equation between two unknown quantities of the form
*ax* + *by* = *c*
then, if the observations were free from error, we should need only two observations giving two equations; but for the attainment of greater accuracy, we may take many observations, and reduce the equations so as to give only a pair with mean coefficients. This reduction is effected by (1.), multiplying the coefficients of each equation by the first coefficient, and adding together all the similar coefficients thus resulting for the coefficients of a new equation; and (2.), by repeating this process, and multiplying the coefficients of each equation by the coefficient of the second term. Meaning by (sum of *a*^{2}) the sum of all quantities of the same kind, and having the same place in the equations as *a*^{2}, we may briefly describe the two resulting mean equations as follows:--
(sum of *a*^{2}) . *x* + (sum of *ab*) . *y* = (sum of *ac*), (sum of *ab*) . *x* + (sum of *b*^{2}) . *y* = (sum of *bc*).
When there are three or more unknown quantities the process is exactly the same in nature, and we get additional mean equations by multiplying by the third, fourth, &c., coefficients. As the numbers are in any case approximate, it is usually unnecessary to make the computations with accuracy, and places of decimals may be freely cut off to save arithmetical work. The mean equations having been computed, their solution by the ordinary methods of algebra gives the most probable values of the unknown quantities.
*Works upon the Theory of Probability.*
Regarding the Theory of Probability and the Law of Error as most important subjects of study for any one who desires to obtain a complete comprehension of scientific method as actually applied in physical investigations, I will briefly indicate the works in one or other of which the reader will best pursue the study.
The best popular, and at the same time profound English work on the subject is De Morgan’s “Essay on Probabilities and on their Application to Life Contingencies and Insurance Offices,” published in the *Cabinet Cyclopædia*, and to be obtained (in print) from Messrs. Longman. Mr. Venn’s work on *The Logic of Chance* can now be procured in a greatly enlarged second edition;[297] it contains a most interesting and able discussion of the metaphysical basis of probability and of related questions concerning causation, belief, design, testimony, &c.; but I cannot always agree with Mr. Venn’s opinions. No mathematical knowledge beyond that of common arithmetic is required in reading these works. Quetelet’s *Letters* form a good introduction to the subject, and the mathematical notes are of value. Sir George Airy’s brief treatise *On the Algebraical and Numerical Theory of Errors of Observations and the Combination of Observations*, contains a complete explanation of the Law of Error and its practical applications. De Morgan’s treatise “On the Theory of Probabilities” in the *Encyclopædia Metropolitana*, presents an abstract of the more abstruse investigations of Laplace, together with a multitude of profound and original remarks concerning the theory generally. In Lubbock and Drinkwater’s work on *Probability*, in the Library of Useful Knowledge, we have a concise but good statement of a number of important problems. The Rev. W. A. Whitworth has given, in a work entitled *Choice and Chance*, a number of good illustrations of calculations both in combinations and probabilities. In Mr. Todhunter’s admirable History we have an exhaustive critical account of almost all writings upon the subject of probability down to the culmination of the theory in Laplace’s works. The Memoir of Mr. J. W. L. Glaisher has already been mentioned (p. 375). In spite of the existence of these and some other good English works, there seems to be a want of an easy and yet pretty complete mathematical introduction to the study of the theory.
[297] *The Logic of Chance*, an Essay on the Foundations and Province of the Theory of Probability, with especial reference to its Logical Bearings and its Application to Moral and Social Science. (Macmillan), 1876.
Among French works the Traité *Élémentaire du Calcul des Probabilités*, by S. E. Lacroix, of which several editions have been published, and which is not difficult to obtain, forms probably the best elementary treatise. Poisson’s *Recherches sur la Probabilité des Jugements* (Paris 1837), commence with an admirable investigation of the grounds and methods of the theory. While Laplace’s great *Théorie Analytique des Probabilités* is of course the “Principia” of the subject; his *Essai Philosophique sur les Probabilités* is a popular discourse, and is one of the most profound and interesting essays ever published. It should be familiar to every student of logical method, and has lost little or none of its importance by lapse of time.
*Detection of Constant Errors.*
The Method of Means is absolutely incapable of eliminating any error which is always the same, or which always lies in one direction. We sometimes require to be roused from a false feeling of security, and to be urged to take suitable precautions against such occult errors. “It is to the observer,” says Gauss,[298] “that belongs the task of carefully removing the causes of constant errors,” and this is quite true when the error is absolutely constant. When we have made a number of determinations with a certain apparatus or method of measurement, there is a great advantage in altering the arrangement, or even devising some entirely different method of getting estimates of the same quantity. The reason obviously consists in the improbability that the same error will affect two or more different methods of experiment. If a discrepancy is found to exist, we shall at least be aware of the existence of error, and can take measures for finding in which way it lies. If we can try a considerable number of methods, the probability becomes great that errors constant in one method will be balanced or nearly so by errors of an opposite effect in the others. Suppose that there be three different methods each affected by an error of equal amount. The probability that this error will in all fall in the same direction is only 1/4; and with four methods similarly 1/8. If each method be affected, as is always the case, by several independent sources of error, the probability becomes much greater that in the mean result of all the methods some of the errors will partially compensate the others. In this case as in all others, when human vigilance has exhausted itself, we must trust the theory of probability.
[298] Gauss, translated by Bertrand, p. 25.
In the determination of a zero point, of the magnitude of the fundamental standards of time and space, in the personal equation of an astronomical observer, we have instances of fixed errors; but as a general rule a change of procedure is likely to reverse the character of the error, and many instances may be given of the value of this precaution. If we measure over and over again the same angular magnitude by the same divided circle, maintained in exactly the same position, it is evident that the same mark in the circle will be the criterion in each case, and any error in the position of that mark will equally affect all our results. But if in each measurement we use a different part of the circle, a new mark will come into use, and as the error of each mark cannot be in the same direction, the average result will be nearly free from errors of division. It will be better still to use more than one divided circle.
Even when we have no perception of the points at which error is likely to enter, we may with advantage vary the construction of our apparatus in the hope that we shall accidentally detect some latent cause of error. Baily’s purpose in repeating the experiments of Michell and Cavendish on the density of the earth was not merely to follow the same course and verify the previous numbers, but to try whether variations in the size and substance of the attracting balls, the mode of suspension, the temperature of the surrounding air, &c., would yield different results. He performed no less than 62 distinct series, comprising 2153 experiments, and he carefully classified and discussed the results so as to disclose the utmost differences. Again, in experimenting upon the resistance of the air to the motion of a pendulum, Baily employed no less than 80 pendulums of various forms and materials, in order to ascertain exactly upon what conditions the resistance depends. Regnault, in his exact researches upon the dilatation of gases, made arbitrary changes in the magnitude of parts of his apparatus. He thinks that if, in spite of such modification, the results are unchanged, the errors are probably of inconsiderable amount;[299] but in reality it is always possible, and usually likely, that we overlook sources of error which a future generation will detect. Thus the pendulum experiments of Baily and Sabine were directed to ascertain the nature and amount of a correction for air resistance, which had been entirely misunderstood in the experiments by means of the seconds pendulum, upon which was founded the definition of the standard yard, in the Act of 5th George IV. c. 74. It has already been mentioned that a considerable error was discovered in the determination of the standard metre as the ten-millionth part of the distance from the pole to the equator (p. 314).
[299] Jamin, *Cours de Physique*, vol. ii. p. 60.Return to passage
We shall return in Chapter XXV. to the further consideration of the methods by which we may as far as possible secure ourselves against permanent and undetected sources of error. In the meantime, having completed the consideration of the special methods requisite for treating quantitative phenomena, we must pursue our principal subject, and endeavour to trace out the course by which the physicist, from observation and experiment, collects the materials of knowledge, and then proceeds by hypothesis and inverse calculation to induce from them the laws of nature.
XVIII. OBSERVATION
ALL knowledge proceeds originally from experience. Using the name in a wide sense, we may say that experience comprehends all that we *feel*, externally or internally--the aggregate of the impressions which we receive through the various apertures of perception--the aggregate consequently of what is in the mind, except so far as some portions of knowledge may be the reasoned equivalents of other portions. As the word experience expresses, we *go through* much in life, and the impressions gathered intentionally or unintentionally afford the materials from which the active powers of the mind evolve science.
No small part of the experience actually employed in science is acquired without any distinct purpose. We cannot use the eyes without gathering some facts which may prove useful. A great science has in many cases risen from an accidental observation. Erasmus Bartholinus thus first discovered double refraction in Iceland spar; Galvani noticed the twitching of a frog’s leg; Oken was struck by the form of a vertebra; Malus accidentally examined light reflected from distant windows with a double refracting substance; and Sir John Herschel’s attention was drawn to the peculiar appearance of a solution of quinine sulphate. In earlier times there must have been some one who first noticed the strange behaviour of a loadstone, or the unaccountable motions produced by amber. As a general rule we shall not know in what direction to look for a great body of phenomena widely different from those familiar to us. Chance then must give us the starting point; but one accidental observation well used may lead us to make thousands of observations in an intentional and organised manner, and thus a science may be gradually worked out from the smallest opening.
*Distinction of Observation and Experiment.*
It is usual to say that the two sources of experience are Observation and Experiment. When we merely note and record the phenomena which occur around us in the ordinary course of nature we are said *to observe*. When we change the course of nature by the intervention of our muscular powers, and thus produce unusual combinations and conditions of phenomena, we are said *to experiment*. Herschel justly remarked[300] that we might properly call these two modes of experience *passive and active observation*. In both cases we must certainly employ our senses to observe, and an experiment differs from a mere observation in the fact that we more or less influence the character of the events which we observe. Experiment is thus observation *plus* alteration of conditions.
[300] *Preliminary Discourse on the Study of Natural Philosophy*, p. 77.
It may readily be seen that we pass upwards by insensible gradations from pure observation to determinate experiment. When the earliest astronomers simply noticed the ordinary motions of the sun, moon, and planets upon the face of the starry heavens, they were pure observers. But astronomers now select precise times and places for important observations of stellar parallax, or the transits of planets. They make the earth’s orbit the basis of a well arranged *natural experiment*, as it were, and take well considered advantage of motions which they cannot control. Meteorology might seem to be a science of pure observation, because we cannot possibly govern the changes of weather which we record. Nevertheless we may ascend mountains or rise in balloons, like Gay-Lussac and Glaisher, and may thus so vary the points of observation as to render our procedure experimental. We are wholly unable either to produce or prevent earth-currents of electricity, but when we construct long lines of telegraph, we gather such strong currents during periods of disturbance as to render them capable of easy observation.
The best arranged systems of observation, however, would fail to give us a large part of the facts which we now possess. Many processes continually going on in nature are so slow and gentle as to escape our powers of observation. Lavoisier remarked that the decomposition of water must have been constantly proceeding in nature, although its possibility was unknown till his time.[301] No substance is wholly destitute of magnetic or diamagnetic powers; but it required all the experimental skill of Faraday to prove that iron and a few other metals had no monopoly of these powers. Accidental observation long ago impressed upon men’s minds the phenomena of lightning, and the attractive properties of amber. Experiment only could have shown that phenomena so diverse in magnitude and character were manifestations of the same agent. To observe with accuracy and convenience we must have agents under our control, so as to raise or lower their intensity, to stop or set them in action at will. Just as Smeaton found it requisite to create an artificial and governable supply of wind for his investigation of windmills, so we must have governable supplies of light, heat, electricity, muscular force, or whatever other agents we are examining.
[301] Lavoisier’s *Elements of Chemistry*, translated by Kerr, 3rd ed. p. 148.
It is hardly needful to point out too that on the earth’s surface we live under nearly constant conditions of gravity, temperature, and atmospheric pressure, so that if we are to extend our inferences to other parts of the universe where conditions are widely different, we must be prepared to imitate those conditions on a small scale here. We must have intensely high and low temperatures; we must vary the density of gases from approximate vacuum upwards; we must subject liquids and solids to pressures or strains of almost unlimited amount.
*Mental Conditions of Correct Observation.*
Every observation must in a certain sense be true, for the observing and recording of an event is in itself an event. But before we proceed to deal with the supposed meaning of the record, and draw inferences concerning the course of nature, we must take care to ascertain that the character and feelings of the observer are not to a great extent the phenomena recorded. The mind of man, as Francis Bacon said, is like an uneven mirror, and does not reflect the events of nature without distortion. We need hardly take notice of intentionally false observations, nor of mistakes arising from defective memory, deficient light, and so forth. Even where the utmost fidelity and care are used in observing and recording, tendencies to error exist, and fallacious opinions arise in consequence.
It is difficult to find persons who can with perfect fairness register facts for and against their own peculiar views. Among uncultivated observers the tendency to remark favourable and forget unfavourable events is so great, that no reliance can be placed upon their supposed observations. Thus arises the enduring fallacy that the changes of the weather coincide in some way with the changes of the moon, although exact and impartial registers give no countenance to the fact. The whole race of prophets and quacks live on the overwhelming effect of one success, compared with hundreds of failures which are unmentioned and forgotten. As Bacon says, “Men mark when they hit, and never mark when they miss.” And we should do well to bear in mind the ancient story, quoted by Bacon, of one who in Pagan times was shown a temple with a picture of all the persons who had been saved from shipwreck, after paying their vows. When asked whether he did not now acknowledge the power of the gods, “Ay,” he answered; “but where are they painted that were drowned after their vows?”
If indeed we could estimate the amount of *bias* existing in any particular observations, it might be treated like one of the forces of the problem, and the true course of external nature might still be rendered apparent. But the feelings of an observer are usually too indeterminate, so that when there is reason to suspect considerable bias, rejection is the only safe course. As regards facts casually registered in past times, the capacity and impartiality of the observer are so little known that we should spare no pains to replace these statements by a new appeal to nature. An indiscriminate medley of truth and absurdity, such as Francis Bacon collected in his *Natural History*, is wholly unsuited to the purposes of science. But of course when records relate to past events like eclipses, conjunctions, meteoric phenomena, earthquakes, volcanic eruptions, changes of sea margins, the existence of now extinct animals, the migrations of tribes, remarkable customs, &c., we must make use of statements however unsatisfactory, and must endeavour to verify them by the comparison of independent records or traditions.
When extensive series of observations have to be made, as in astronomical, meteorological, or magnetical observatories, trigonometrical surveys, and extensive chemical or physical researches, it is an advantage that the numerical work should be executed by assistants who are not interested in, and are perhaps unaware of, the expected results. The record is thus rendered perfectly impartial. It may even be desirable that those who perform the purely routine work of measurement and computation should be unacquainted with the principles of the subject. The great table of logarithms of the French Revolutionary Government was worked out by a staff of sixty or eighty computers, most of whom were acquainted only with the rules of arithmetic, and worked under the direction of skilled mathematicians; yet their calculations were usually found more correct than those of persons more deeply versed in mathematics.[302] In the Indian Ordnance Survey the actual measurers were selected so that they should not have sufficient skill to falsify their results without detection.
[302] Babbage, *Economy of Manufactures*, p. 194.
Both passive observation and experimentation must, however, be generally conducted by persons who know for what they are to look. It is only when excited and guided by the hope of verifying a theory that the observer will notice many of the most important points; and, where the work is not of a routine character, no assistant can supersede the mind-directed observations of the philosopher. Thus the successful investigator must combine diverse qualities; he must have clear notions of the result he expects and confidence in the truth of his theories, and yet he must have that candour and flexibility of mind which enable him to accept unfavourable results and abandon mistaken views.
*Instrumental and Sensual Conditions of Observation.*
In every observation one or more of the senses must be employed, and we should ever bear in mind that the extent of our knowledge may be limited by the power of the sense concerned. What we learn of the world only forms the lower limit of what is to be learned, and, for all that we can tell, the processes of nature may infinitely surpass in variety and complexity those which are capable of coming within our means of observation. In some cases inference from observed phenomena may make us indirectly aware of what cannot be directly felt, but we can never be sure that we thus acquire any appreciable fraction of the knowledge that might be acquired.
It is a strange reflection that space may be filled with dark wandering stars, whose existence could not have yet become in any way known to us. The planets have already cooled so far as to be no longer luminous, and it may well be that other stellar bodies of various size have fallen into the same condition. From the consideration, indeed, of variable and extinguished stars, Laplace inferred that there probably exist opaque bodies as great and perhaps as numerous as those we see.[303] Some of these dark stars might ultimately become known to us, either by reflecting light, or more probably by their gravitating effects upon luminous stars. Thus if one member of a double star were dark, we could readily detect its existence, and even estimate its size, position, and motions, by observing those of its visible companion. It was a favourite notion of Huyghens that there may exist stars and vast universes so distant that their light has never yet had time to reach our eyes; and we must also bear in mind that light may possibly suffer slow extinction in space, so that there is more than one way in which an absolute limit to the powers of telescopic discovery may exist.
[303] *System of the World*, translated by Harte, vol. ii. p. 335.
There are natural limits again to the power of our senses in detecting undulations of various kinds. It is commonly said that vibrations of more than 38,000 strokes per second are not audible as sound; and as some ears actually do hear sounds of much higher pitch, even two octaves higher than what other ears can detect, it is exceedingly probable that there are incessant vibrations which we cannot call sound because they are never heard. Insects may communicate by such acute sounds, constituting a language inaudible to us; and the remarkable agreement apparent among bodies of ants or bees might thus perhaps be explained. Nay, as Fontenelle long ago suggested in his scientific romance, there may exist unlimited numbers of senses or modes of perception which we can never feel, though Darwin’s theory would render it probable that any useful means of knowledge in an ancestor would be developed and improved in the descendants. We might doubtless have been endowed with a sense capable of feeling electric phenomena with acuteness, so that the positive or negative state of charge of a body could be at once estimated. The absence of such a sense is probably due to its comparative uselessness.
Heat undulations are subject to the same considerations. It is now apparent that what we call light is the affection of the eye by certain vibrations, the less rapid of which are invisible and constitute the dark rays of radiant heat, in detecting which we must substitute the thermometer or the thermopile for the eye. At the other end of the spectrum, again, the ultra-violet rays are invisible, and only indirectly brought to our knowledge in the phenomena of fluorescence or photo-chemical action. There is no reason to believe that at either end of the spectrum an absolute limit has yet been reached.
Just as our knowledge of the stellar universe is limited by the power of the telescope and other conditions, so our knowledge of the minute world has its limit in the powers and optical conditions of the microscope. There was a time when it would have been a reasonable induction that vegetables are motionless, and animals alone endowed with power of locomotion. We are astonished to discover by the microscope that minute plants are if anything more active than minute animals. We even find that mineral substances seem to lose their inactive character and dance about with incessant motion when reduced to sufficiently minute particles, at least when suspended in a non-conducting medium.[304] Microscopists will meet a natural limit to observation when the minuteness of the objects examined becomes comparable to the length of light undulations, and the extreme difficulty already encountered in determining the forms of minute marks on Diatoms appears to be due to this cause. According to Helmholtz the smallest distance which can be accurately defined depends upon the interference of light passing through the centres of the bright spaces. With a theoretically perfect microscope and a dry lense the smallest visible object would not be less than one 80,000th part of an inch in red light.
[304] This curious phenomenon, which I propose to call *pedesis*, or the *pedetic movement*, from πηδόω, to jump, is carefully described in my paper published in the *Quarterly Journal of Science* for April, 1878, vol. viii. (N.S.) p. 167. See also *Proceedings of the Literary and Philosophical Society of Manchester*, 25th January, 1870, vol. ix. p. 78, *Nature*, 22nd August, 1878, vol. xviii. p. 440, or the *Quarterly Journal of Science*, vol. viii. (N.S.) p. 514.
Of the errors likely to arise in estimating quantities by the senses I have already spoken, but there are some cases in which we actually see things differently from what they are. A jet of water appears to be a continuous thread, when it is really a wonderfully organised succession of small and large drops, oscillating in form. The drops fall so rapidly that their impressions upon the eye run into each other, and in order to see the separate drops we require some device for giving an instantaneous view.
One insuperable limit to our powers of observation arises from the impossibility of following and identifying the ultimate atoms of matter. One atom of oxygen is probably undistinguishable from another atom; only by keeping a certain volume of oxygen safely inclosed in a bottle can we assure ourselves of its identity; allow it to mix with other oxygen, and we lose all power of identification. Accordingly we seem to have no means of directly proving that every gas is in a constant state of diffusion of every part into every part. We can only infer this to be the case from observing the behaviour of distinct gases which we can distinguish in their course, and by reasoning on the grounds of molecular theory.[305]
[305] Maxwell, *Theory of Heat*, p. 301.
*External Conditions of Correct Observation.*
Before we proceed to draw inferences from any series of recorded facts, we must take care to ascertain perfectly, if possible, the external conditions under which the facts are brought to our notice. Not only may the observing mind be prejudiced and the senses defective, but there may be circumstances which cause one kind of event to come more frequently to our notice than another. The comparative numbers of objects of different kinds existing may in any degree differ from the numbers which come to our notice. This difference must if possible be taken into account before we make any inferences.
There long appeared to be a strong presumption that all comets moved in elliptic orbits, because no comet had been proved to move in any other kind of path. The theory of gravitation admitted of the existence of comets moving in hyperbolic orbits, and the question arose whether they were really non-existent or were only beyond the bounds of easy observation. From reasonable suppositions Laplace calculated that the probability was at least 6000 to 1 against a comet which comes within the planetary system sufficiently to be visible at the earth’s surface, presenting an orbit which could be discriminated from a very elongated ellipse or parabola in the part of its orbit within the reach of our telescopes.[306] In short, the chances are very much in favour of our seeing elliptic rather than hyperbolic comets. Laplace’s views have been confirmed by the discovery of six hyperbolic comets, which appeared in the years 1729, 1771, 1774, 1818, 1840, and 1843,[307] and as only about 800 comets altogether have been recorded, the proportion of hyperbolic ones is quite as large as should be expected.
[306] Laplace, *Essai Philosophique*, p. 59. Todhunter’s *History*, pp. 491–494.
[307] Chambers’ *Astronomy*, 1st ed. p. 203.
When we attempt to estimate the numbers of objects which may have existed, we must make large allowances for the limited sphere of our observations. Probably not more than 4000 or 5000 comets have been seen in historical times, but making allowance for the absence of observers in the southern hemisphere, and for the small probability that we see any considerable fraction of those which are in the neighbourhood of our system, we must accept Kepler’s opinion, that there are more comets in the regions of space than fishes in the depths of the ocean. When like calculations are made concerning the numbers of meteors visible to us, it is astonishing to find that the number of meteors entering the earth’s atmosphere in every twenty-four hours is probably not less than 400,000,000, of which 13,000 exist in every portion of space equal to that filled by the earth.
Serious fallacies may arise from overlooking the inevitable conditions under which the records of past events are brought to our notice. Thus it is only the durable objects manufactured by former races of men, such as flint implements, which can have come to our notice as a general rule. The comparative abundance of iron and bronze articles used by an ancient nation must not be supposed to be coincident with their comparative abundance in our museums, because bronze is far the more durable. There is a prevailing fallacy that our ancestors built more strongly than we do, arising from the fact that the more fragile structures have long since crumbled away. We have few or no relics of the habitations of the poorer classes among the Greeks or Romans, or in fact of any past race; for the temples, tombs, public buildings, and mansions of the wealthier classes alone endure. There is an immense expanse of past events necessarily lost to us for ever, and we must generally look upon records or relics as exceptional in their character.
The same considerations apply to geological relics. We could not generally expect that animals would be preserved unless as regards the bones, shells, strong integuments, or other hard and durable parts. All the infusoria and animals devoid of mineral framework have probably perished entirely, distilled perhaps into oils. It has been pointed out that the peculiar character of some extinct floras may be due to the unequal preservation of different families of plants. By various accidents, however, we gain glimpses of a world that is usually lost to us--as by insects embedded in amber, the great mammoth preserved in ice, mummies, casts in solid material like that of the Roman soldier at Pompeii, and so forth.
We should also remember, that just as there may be conjunctions of the heavenly bodies that can have happened only once or twice in the period of history, so remarkable terrestrial conjunctions may take place. Great storms, earthquakes, volcanic eruptions, landslips, floods, irruptions of the sea, may, or rather must, have occurred, events of such unusual magnitude and such extreme rarity that we can neither expect to witness them nor readily to comprehend their effects. It is a great advantage of the study of probabilities, as Laplace himself remarked, to make us mistrust the extent of our knowledge, and pay proper regard to the probability that events would come within the sphere of our observations.
*Apparent Sequence of Events.*
De Morgan has excellently pointed out[308] that there are no less than four modes in which one event may seem to follow or be connected with another, without being really so. These involve mental, sensual, and external causes of error, and I will briefly state and illustrate them.
[308] *Essay on Probabilities*, Cabinet Cyclopædia, p. 121.
Instead of A causing B, it may be *our perception of A that causes B*. Thus it is that prophecies, presentiments, and the devices of sorcery and witchcraft often work their own ends. A man dies on the day which he has always regarded as his last, from his own fears of the day. An incantation effects its purpose, because care is taken to frighten the intended victim, by letting him know his fate. In all such cases the mental condition is the cause of apparent coincidence.
In a second class of cases, *the event A may make our perception of B follow, which would otherwise happen without being perceived*. Thus it was believed to be the result of investigation that more comets appeared in hot than cold summers. No account was taken of the fact that hot summers would be comparatively cloudless, and afford better opportunities for the discovery of comets. Here the disturbing condition is of a purely external character. Certain ancient philosophers held that the moon’s rays were cold-producing, mistaking the cold caused by radiation into space for an effect of the moon, which is more likely to be visible at a time when the absence of clouds permits radiation to proceed.
In a third class of cases, *our perception of A may make our perception of B follow*. The event B may be constantly happening, but our attention may not be drawn to it except by our observing A. This case seems to be illustrated by the fallacy of the moon’s influence on clouds. The origin of this fallacy is somewhat complicated. In the first place, when the sky is densely clouded the moon would not be visible at all; it would be necessary for us to see the full moon in order that our attention should be strongly drawn to the fact, and this would happen most often on those nights when the sky is cloudless. Mr. W. Ellis,[309] moreover, has ingeniously pointed out that there is a general tendency for clouds to disperse at the commencement of night, which is the time when the full moon rises. Thus the change of the sky and the rise of the full moon are likely to attract attention mutually, and the coincidence in time suggests the relation of cause and effect. Mr. Ellis proves from the results of observations at the Greenwich Observatory that the moon possesses no appreciable power of the kind supposed, and yet it is remarkable that so sound an observer as Sir John Herschel was convinced of the connection. In his “Results of Observations at the Cape of Good Hope,”[310] he mentions many evenings when a full moon occurred with a peculiarly clear sky.
[309] *Philosophical Magazine*, 4th Series (1867), vol. xxxiv. p. 64.
[310] See *Notes to Measures of Double Stars*, 1204, 1336, 1477, 1686, 1786, 1816, 1835, 1929, 2081, 2186, pp. 265, &c. See also Herschel’s *Familiar Lectures on Scientific Subjects*, p. 147, and *Outlines of Astronomy*, 7th ed. p. 285.
There is yet a fourth class of cases, in which *B is really the antecedent event, but our perception of A, which is a consequence of B, may be necessary to bring about our perception of B*. There can be no doubt, for instance, that upward and downward currents are continually circulating in the lowest stratum of the atmosphere during the day-time; but owing to the transparency of the atmosphere we have no evidence of their existence until we perceive cumulous clouds, which are the consequence of such currents. In like manner an interfiltration of bodies of air in the higher parts of the atmosphere is probably in nearly constant progress, but unless threads of cirrous cloud indicate these motions we remain ignorant of their occurrence.[311] The highest strata of the atmosphere are wholly imperceptible to us, except when rendered luminous by auroral currents of electricity, or by the passage of meteoric stones. Most of the visible phenomena of comets probably arise from some substance which, existing previously invisible, becomes condensed or electrified suddenly into a visible form. Sir John Herschel attempted to explain the production of comet tails in this manner by evaporation and condensation.[312]
[311] Jevons, *On the Cirrous Form of Cloud*, Philosophical Magazine, July, 1857, 4th Series, vol. xiv. p. 22.
[312] *Astronomy*, 4th ed. p. 358.
*Negative Arguments from Non-observation.*
From what has been suggested in preceding sections, it will plainly appear that the non-observation of a phenomenon is not generally to be taken as proving its non-occurrence. As there are sounds which we cannot hear, rays of heat which we cannot feel, multitudes of worlds which we cannot see, and myriads of minute organisms of which not the most powerful microscope can give us a view, we must as a general rule interpret our experience in an affirmative sense only. Accordingly when inferences have been drawn from the non-occurrence of particular facts or objects, more extended and careful examination has often proved their falsity. Not many years since it was quite a well credited conclusion in geology that no remains of man were found in connection with those of extinct animals, or in any deposit not actually at present in course of formation. Even Babbage accepted this conclusion as strongly confirmatory of the Mosaic accounts.[313] While the opinion was yet universally held, flint implements had been found disproving such a conclusion, and overwhelming evidence of man’s long-continued existence has since been forthcoming. At the end of the last century, when Herschel had searched the heavens with his powerful telescopes, there seemed little probability that planets yet remained unseen within the orbit of Jupiter. But on the first day of this century such an opinion was overturned by the discovery of Ceres, and more than a hundred other small planets have since been added to the lists of the planetary system.
[313] Babbage, *Ninth Bridgewater Treatise*, p. 67.
The discovery of the Eozoön Canadense in strata of much greater age than any previously known to contain organic remains, has given a shock to groundless opinions concerning the origin of organic forms; and the oceanic dredging expeditions under Dr. Carpenter and Sir Wyville Thomson have modified some opinions of geologists by disclosing the continued existence of forms long supposed to be extinct. These and many other cases which might be quoted show the extremely unsafe character of negative inductions.
But it must not be supposed that negative arguments are of no force and value. The earth’s surface has been sufficiently searched to render it highly improbable that any terrestrial animals of the size of a camel remain to be discovered. It is believed that no new large animal has been encountered in the last eighteen or twenty centuries,[314] and the probability that if existent they would have been seen, increases the probability that they do not exist. We may with somewhat less confidence discredit the existence of any large unrecognised fish, or sea animals, such as the alleged sea-serpent. But, as we descend to forms of smaller size negative evidence loses weight from the less probability of our seeing smaller objects. Even the strong induction in favour of the four-fold division of the animal kingdom into Vertebrata, Annulosa, Mollusca, and Cœlenterata, may break down by the discovery of intermediate or anomalous forms. As civilisation spreads over the surface of the earth, and unexplored tracts are gradually diminished, negative conclusions will increase in force; but we have much to learn yet concerning the depths of the ocean, almost wholly unexamined as they are, and covering three-fourths of the earth’s surface.
[314] Cuvier, *Essay on the Theory of the Earth*, translation, p. 61, &c.
In geology there are many statements to which considerable probability attaches on account of the large extent of the investigations already made, as, for instance, that true coal is found only in rocks of a particular geological epoch; that gold occurs in secondary and tertiary strata only in exceedingly small quantities,[315] probably derived from the disintegration of earlier rocks. In natural history negative conclusions are exceedingly treacherous and unsatisfactory. The utmost patience will not enable a microscopist or the observer of any living thing to watch the behaviour of the organism under all circumstances continuously for a great length of time. There is always a chance therefore that the critical act or change may take place when the observer’s eyes are withdrawn. This certainly happens in some cases; for though the fertilisation of orchids by agency of insects is proved as well as any fact in natural history, Mr. Darwin has never been able by the closest watching to detect an insect in the performance of the operation. Mr. Darwin has himself adopted one conclusion on negative evidence, namely, that the *Orchis pyramidalis* and certain other orchidaceous flowers secrete no nectar. But his caution and unwearying patience in verifying the conclusion give an impressive lesson to the observer. For twenty-three consecutive days, as he tells us, he examined flowers in all states of the weather, at all hours, in various localities. As the secretion in other flowers sometimes takes place rapidly and might happen at early dawn, that inconvenient hour of observation was specially adopted. Flowers of different ages were subjected to irritating vapours, to moisture, and to every condition likely to bring on the secretion; and only after invariable failure of this exhaustive inquiry was the barrenness of the nectaries assumed to be proved.[316]
[315] Murchison’s *Siluria*, 1st ed. p. 432.
[316] Darwin’s *Fertilisation of Orchids*, p. 48.
In order that a negative argument founded on the non-observation of an object shall have any considerable force, it must be shown to be probable that the object if existent would have been observed, and it is this probability which defines the value of the negative conclusion. The failure of astronomers to see the planet Vulcan, supposed by some to exist within Mercury’s orbit, is no sufficient disproof of its existence. Similarly it would be very difficult, or even impossible, to disprove the existence of a second satellite of small size revolving round the earth. But if any person make a particular assertion, assigning place and time, then observation will either prove or disprove the alleged fact. If it is true that when a French observer professed to have seen a planet on the sun’s face, an observer in Brazil was carefully scrutinising the sun and failed to see it, we have a negative proof. False facts in science, it has been well said, are more mischievous than false theories. A false theory is open to every person’s criticism, and is ever liable to be judged by its accordance with facts. But a false or grossly erroneous assertion of a fact often stands in the way of science for a long time, because it may be extremely difficult or even impossible to prove the falsity of what has been once recorded.
In other sciences the force of a negative argument will often depend upon the number of possible alternatives which may exist. It was long believed that the quality of a musical sound as distinguished from its pitch, must depend upon the form of the undulation, because no other cause of it had ever been suggested or was apparently possible. The truth of the conclusion was proved by Helmholtz, who applied a microscope to luminous points attached to the strings of various instruments, and thus actually observed the different modes of undulation. In mathematics negative inductive arguments have seldom much force, because the possible forms of expression, or the possible combinations of lines and circles in geometry, are quite unlimited in number. An enormous number of attempts were made to trisect the angle by the ordinary methods of Euclid’s geometry, but their invariable failure did not establish the impossibility of the task. This was shown in a totally different manner, by proving that the problem involves an irreducible cubic equation to which there could be no corresponding plane geometrical solution.[317] This is a case of *reductio ad absurdum*, a form of argument of a totally different character. Similarly no number of failures to obtain a general solution of equations of the fifth degree would establish the impossibility of the task, but in an indirect mode, equivalent to a *reductio ad absurdum*, the impossibility is considered to be proved.[318]
[317] Peacock, *Algebre*, vol. ii. p. 344.Return to passage
[318] Ibid, p. 359. Serret, *Algèbre Supérieure*, 2nd ed. p. 304.Return to passage
XIX. EXPERIMENT
We may now consider the great advantages which we enjoy in examining the combinations of phenomena when things are within our reach and capable of being experimented on. We are said *to experiment* when we bring substances together under various conditions of temperature, pressure, electric disturbance, chemical action, &c., and then record the changes observed. Our object in inductive investigation is to ascertain exactly the group of circumstances or conditions which being present, a certain other group of phenomena will follow. If we denote by A the antecedent group, and by X subsequent phenomena, our object will usually be to discover a law of the form A = AX, the meaning of which is that where A is X will happen.
The circumstances which might be enumerated as present in the simplest experiment are very numerous, in fact almost infinite. Rub two sticks together and consider what would be an exhaustive statement of the conditions. There are the form, hardness, organic structure, and all the chemical qualities of the wood; the pressure and velocity of the rubbing; the temperature, pressure, and all the chemical qualities of the surrounding air; the proximity of the earth with its attractive and electric powers; the temperature and other properties of the persons producing motion; the radiation from the sun, and to and from the sky; the electric excitement possibly existing in any overhanging cloud; even the positions of the heavenly bodies must be mentioned. On *à priori* grounds it is unsafe to assume that any one of these circumstances is without effect, and it is only by experience that we can single out those precise conditions from which the observed heat of friction proceeds.
The great method of experiment consists in removing, one at a time, each of those conditions which may be imagined to have an influence on the result. Our object in the experiment of rubbing sticks is to discover the exact circumstances under which heat appears. Now the presence of air may be requisite; therefore prepare a vacuum, and rub the sticks in every respect as before, except that it is done *in vacuo*. If heat still appears we may say that air is not, in the presence of the other circumstances, a requisite condition. The conduction of heat from neighbouring bodies may be a condition. Prevent this by making all the surrounding bodies ice cold, which is what Davy aimed at in rubbing two pieces of ice together. If heat still appears we have eliminated another condition, and so we may go on until it becomes apparent that the expenditure of energy in the friction of two bodies is the sole condition of the production of heat.
The great difficulty of experiment arises from the fact that we must not assume the conditions to be independent. Previous to experiment we have no right to say that the rubbing of two sticks will produce heat in the same way when air is absent as before. We may have heat produced in one way when air is present, and in another when air is absent. The inquiry branches out into two lines, and we ought to try in both cases whether cutting off a supply of heat by conduction prevents its evolution in friction. The same branching out of the inquiry occurs with regard to every circumstance which enters into the experiment.
Regarding only four circumstances, say A, B, C, D, we ought to test not only the combinations ABCD, ABC*d*, AB*c*D, A*b*CD, *a*BCD, but we ought really to go through the whole of the combinations given in the fifth column of the Logical Alphabet. The effect of the absence of each condition should be tried both in the presence and absence of every other condition, and every selection of those conditions. Perfect and exhaustive experimentation would, in short, consist in examining natural phenomena in all their possible combinations and registering all relations between conditions and results which are found capable of existence. It would thus resemble the exclusion of contradictory combinations carried out in the Indirect Method of Inference, except that the exclusion of combinations is grounded not on prior logical premises, but on *à posteriori* results of actual trial.
The reader will perceive, however, that such exhaustive investigation is practically impossible, because the number of requisite experiments would be immensely great. Four antecedents only would require sixteen experiments; twelve antecedents would require 4096, and the number increases as the powers of two. The result is that the experimenter has to fall back upon his own tact and experience in selecting those experiments which are most likely to yield him significant facts. It is at this point that logical rules and forms begin to fail in giving aid. The logical rule is--Try all possible combinations; but this being impracticable, the experimentalist necessarily abandons strict logical method, and trusts to his own insight. Analogy, as we shall see, gives some assistance, and attention should be concentrated on those kinds of conditions which have been found important in like cases. But we are now entirely in the region of probability, and the experimenter, while he is confidently pursuing what he thinks the right clue, may be overlooking the one condition of importance. It is an impressive lesson, for instance, that Newton pursued all his exquisite researches on the spectrum unsuspicious of the fact that if he reduced the hole in the shutter to a narrow slit, all the mysteries of the bright and dark lines were within his grasp, provided of course that his prisms were sufficiently good to define the rays. In like manner we know not what slight alteration in the most familiar experiments may not open the way to realms of new discovery.
Practical difficulties, also, encumber the progress of the physicist. It is often impossible to alter one condition without altering others at the same time; and thus we may not get the pure effect of the condition in question. Some conditions may be absolutely incapable of alteration; others may be with great difficulty, or only in a certain degree, removable. A very treacherous source of error is the existence of unknown conditions, which of course we cannot remove except by accident. These difficulties we will shortly consider in succession.
It is beautiful to observe how the alteration of a single circumstance sometimes conclusively explains a phenomenon. An instance is found in Faraday’s investigation of the behaviour of Lycopodium spores scattered on a vibrating plate. It was observed that these minute spores collected together at the points of greatest motion, whereas sand and all heavy particles collected at the nodes, where the motion was least. It happily occurred to Faraday to try the experiment in the exhausted receiver of an air-pump, and it was then found that the light powder behaved exactly like heavy powder. A conclusive proof was thus obtained that the presence of air was the condition of importance, doubtless because it was thrown into eddies by the motion of the plate, and carried the Lycopodium to the points of greatest agitation. Sand was too heavy to be carried by the air.
*Exclusion of Indifferent Circumstances.*
From what has been already said it will be apparent that the detection and exclusion of indifferent circumstances is a work of importance, because it allows the concentration of attention upon circumstances which contain the principal condition. Many beautiful instances may be given where all the most obvious antecedents have been shown to have no part in the production of a phenomenon. A person might suppose that the peculiar colours of mother-of-pearl were due to the chemical qualities of the substance. Much trouble might have been spent in following out that notion by comparing the chemical qualities of various iridescent substances. But Brewster accidentally took an impression from a piece of mother-of-pearl in a cement of resin and bees’-wax, and finding the colours repeated upon the surface of the wax, he proceeded to take other impressions in balsam, fusible metal, lead, gum arabic, isinglass, &c., and always found the iridescent colours the same. He thus proved that the chemical nature of the substance is a matter of indifference, and that the form of the surface is the real condition of such colours.[319] Nearly the same may be said of the colours exhibited by thin plates and films. The rings and lines of colour will be nearly the same in character whatever may be the nature of the substance; nay, a void space, such as a crack in glass, would produce them even though the air were withdrawn by an air-pump. The conditions are simply the existence of two reflecting surfaces separated by a very small space, though it should be added that the refractive index of the intervening substance has some influence on the exact nature of the colour produced.
[319] *Treatise on Optics*, by Brewster, Cab. Cyclo. p. 117.
When a ray of light passes close to the edge of an opaque body, a portion of the light appears to be bent towards it, and produces coloured fringes within the shadow of the body. Newton attributed this inflexion of light to the attraction of the opaque body for the supposed particles of light, although he was aware that the nature of the surrounding medium, whether air or other pellucid substance, exercised no apparent influence on the phenomena. Gravesande proved, however, that the character of the fringes is exactly the same, whether the body be dense or rare, compound or elementary. A wire produces exactly the same fringes as a hair of the same thickness. Even the form of the obstructing edge was subsequently shown to be a matter of indifference by Fresnel, and the interference spectrum, or the spectrum seen when light passes through a fine grating, is absolutely the same whatever be the form or chemical nature of the bars making the grating. Thus it appears that the stoppage of a portion of a beam of light is the sole necessary condition for the diffraction or inflexion of light, and the phenomenon is shown to bear no analogy the refraction of light, in which the form and nature of the substance are all important.
It is interesting to observe how carefully Newton, in his researches on the spectrum, ascertained the indifference of many circumstances by actual trial. He says:[320] “Now the different magnitude of the hole in the window-shut, and different thickness of the prism where the rays passed through it, and different inclinations of the prism to the horizon, made no sensible changes in the length of the image. Neither did the different matter of the prisms make any: for in a vessel made of polished plates of glass cemented together in the shape of a prism, and filled with water, there is the like success of the experiment according to the quantity of the refraction.” But in the latter statement, as I shall afterwards remark (p. 432), Newton assumed an indifference which does not exist, and fell into an unfortunate mistake.
[320] *Opticks*, 3rd. ed. p. 25.
In the science of sound it is shown that the pitch of a sound depends solely upon the number of impulses in a second, and the material exciting those impulses is a matter of indifference. Whatever fluid, air or water, gas or liquid, be forced into the Siren, the sound produced is the same; and the material of which an organ-pipe is constructed does not at all affect the pitch of its sound. In the science of statical electricity it is an important principle that the nature of the interior of a conducting body is a matter of no importance. The electrical charge is confined to the conducting surface, and the interior remains in a neutral state. A hollow copper sphere takes exactly the same charge as a solid sphere of the same metal.
Some of Faraday’s most elegant and successful researches were devoted to the exclusion of conditions which previous experimenters had thought essential for the production of electrical phenomena. Davy asserted that no known fluids, except such as contain water, could be made the medium of connexion between the poles of a battery; and some chemists believed that water was an essential agent in electro-chemical decomposition. Faraday gave abundant experiments to show that other fluids allowed of electrolysis, and he attributed the erroneous opinion to the very general use of water as a solvent, and its presence in most natural bodies.[321] It was, in fact, upon the weakest kind of negative evidence that the opinion had been founded.
Many experimenters attributed peculiar powers to the poles of a battery, likening them to magnets, which, by their attractive powers, tear apart the elements of a substance. By a beautiful series of experiments,[322] Faraday proved conclusively that, on the contrary, the substance of the poles is of no importance, being merely the path through which the electric force reaches the liquid acted upon. Poles of water, charcoal, and many diverse substances, even air itself, produced similar results; if the chemical nature of the pole entered at all into the question, it was as a disturbing agent.
[321] *Experimental Researches in Electricity*, vol. i. pp. 133, 134.
[322] Ibid. vol i. pp. 127, 162, &c.
It is an essential part of the theory of gravitation that the proximity of other attracting particles is without effect upon the attraction existing between any two molecules. Two pound weights weigh as much together as they do separately. Every pair of molecules in the world have, as it were, a private communication, apart from their relations to all other molecules. Another undoubted result of experience pointed out by Newton[323] is that the weight of a body does not in the least depend upon its form or texture. It may be added that the temperature, electric condition, pressure, state of motion, chemical qualities, and all other circumstances concerning matter, except its mass, are indifferent as regards its gravitating power.
[323] *Principia*, bk. iii. Prop. vi. Corollary i.
As natural science progresses, physicists gain a kind of insight and tact in judging what qualities of a substance are likely to be concerned in any class of phenomena. The physical astronomer treats matter in one point of view, the chemist in another, and the students of physical optics, sound, mechanics, electricity, &c., make a fair division of the qualities among them. But errors will arise if too much confidence be placed in this independence of various kinds of phenomena, so that it is desirable from time to time, especially when any unexplained discrepancies come into notice, to question the indifference which is assumed to exist, and to test its real existence by appropriate experiments.
*Simplification of Experiments.*
One of the most requisite precautions in experimentation is to vary only one circumstance at a time, and to maintain all other circumstances rigidly unchanged. There are two distinct reasons for this rule, the first and most obvious being that if we vary two conditions at a time, and find some effect, we cannot tell whether the effect is due to one or the other condition, or to both jointly. A second reason is that if no effect ensues we cannot safely conclude that either of them is indifferent; for the one may have neutralised the effect of the other. In our symbolic logic AB ꖌ A*b* was shown to be identical with A (p. 97), so that B denotes a circumstance which is indifferently present or absent. But if B always goes together with another antecedent C, we cannot show the same independence, for ABC ꖌ A*bc* is not identical with A and none of our logical processes enables us to reduce it to A.
If we want to prove that oxygen is necessary to life, we must not put a rabbit into a vessel from which the oxygen has been exhausted by a burning candle. We should then have not only an absence of oxygen, but an addition of carbonic acid, which may have been the destructive agent. For a similar reason Lavoisier avoided the use of atmospheric air in experiments on combustion, because air was not a simple substance, and the presence of nitrogen might impede or even alter the effect of oxygen. As Lavoisier remarks,[324] “In performing experiments, it is a necessary principle, which ought never to be deviated from, that they be simplified as much as possible, and that every circumstance capable of rendering their results complicated be carefully removed.” It has also been well said by Cuvier[325] that the method of physical inquiry consists in isolating bodies, reducing them to their utmost simplicity, and bringing each of their properties separately into action, either mentally or by experiment.
[324] Lavoisier’s *Chemistry*, translated by Kerr, p. 103.
[325] Cuvier’s *Animal Kingdom*, introduction, pp. 1, 2.
The electro-magnet has been of the utmost service in the investigation of the magnetic properties of matter, by allowing of the production or removal of a most powerful magnetic force without disturbing any of the other arrangements of the experiment. Many of Faraday’s most valuable experiments would have been impossible had it been necessary to introduce a heavy permanent magnet, which could not be suddenly moved without shaking the whole apparatus, disturbing the air, producing currents by changes of temperature, &c. The electro-magnet is perfectly under control, and its influence can be brought into action, reversed, or stopped by merely touching a button. Thus Faraday was enabled to prove the rotation of the plane of circularly polarised light by the fact that certain light ceased to be visible when the electric current of the magnet was cut off, and re-appeared when the current was made. “These phenomena,” he says, “could be reversed at pleasure, and at any instant of time, and upon any occasion, showing a perfect dependence of cause and effect.”[326]
[326] *Experimental Researches in Electricity*, vol. iii. p. 4.
It was Newton’s omission to obtain the solar spectrum under the simplest conditions which prevented him from discovering the dark lines. Using a broad beam of light which had passed through a round hole or a triangular slit, he obtained a brilliant spectrum, but one in which many different coloured rays overlapped each other. In the recent history of the science of the spectrum, one main difficulty has consisted in the mixture of the lines of several different substances, which are usually to be found in the light of any flame or spark. It is seldom possible to obtain the light of any element in a perfectly simple manner. Angström greatly advanced this branch of science by examining the light of the electric spark when formed between poles of various metals, and in the presence of various gases. By varying the pole alone, or the gaseous medium alone, he was able to discriminate correctly between the lines due to the metal and those due to the surrounding gas.[327]
[327] *Philosophical Magazine*, 4th Series, vol. ix. p. 327.
*Failure in the Simplification of Experiments.*
In some cases it seems to be impossible to carry out the rule of varying one circumstance at a time. When we attempt to obtain two instances or two forms of experiment in which a single circumstance shall be present in one case and absent in another, it may be found that this single circumstance entails others. Benjamin Franklin’s experiment concerning the comparative absorbing powers of different colours is well known. “I took,” he says, “a number of little square pieces of broadcloth from a tailor’s pattern card, of various colours. They were black, deep blue, lighter blue, green, purple, red, yellow, white, and other colours and shades of colour. I laid them all out upon the snow on a bright sunshiny morning. In a few hours the black, being most warmed by the sun, was sunk so low as to be below the stroke of the sun’s rays; the dark blue was almost as low; the lighter blue not quite so much as the dark; the other colours less as they were lighter. The white remained on the surface of the snow, not having entered it at all.” This is a very elegant and apparently simple experiment; but when Leslie had completed his series of researches upon the nature of heat, he came to the conclusion that the colour of a surface has very little effect upon the radiating power, the mechanical nature of the surface appearing to be more influential. He remarks[328] that “the question is incapable of being positively resolved, since no substance can be made to assume different colours without at the same time changing its internal structure.” Recent investigation has shown that the subject is one of considerable complication, because the absorptive power of a surface may be different according to the character of the rays which fall upon it; but there can be no doubt as to the acuteness with which Leslie points out the difficulty. In Well’s investigations concerning the nature of dew, we have, again, very complicated conditions. If we expose plates of various material, such as rough iron, glass, polished metal, to the midnight sky, they will be dewed in various degrees; but since these plates differ both in the nature of the surface and the conducting power of the material, it would not be plain whether one or both circumstances were of importance. We avoid this difficulty by exposing the same material polished or varnished, so as to present different conditions of surface;[329] and again by exposing different substances with the same kind of surface.
[328] *Inquiry into the Nature of Heat*, p. 95.
[329] Herschel, *Preliminary Discourse*, p. 161.
When we are quite unable to isolate circumstances we must resort to the procedure described by Mill under the name of the Joint Method of Agreement and Difference. We must collect as many instances as possible in which a given circumstance produces a given result, and as many as possible in which the absence of the circumstance is followed by the absence of the result. To adduce his example, we cannot experiment upon the cause of double refraction in Iceland spar, because we cannot alter its crystalline condition without altering it altogether, nor can we find substances exactly like calc spar in every circumstance except one. We resort therefore to the method of comparing together all known substances which have the property of doubly-refracting light, and we find that they agree in being crystalline.[330] This indeed is nothing but an ordinary process of perfect or probable induction, already partially described, and to be further discussed under Classification. It may be added that the subject does admit of perfect experimental treatment, since glass, when compressed in one direction, becomes capable of doubly-refracting light, and as there is probably no alteration in the glass but change of elasticity, we learn that the power of double refraction is probably due to a difference of elasticity in different directions.
[330] *System of Logic*, bk. iii. chap. viii. § 4, 5th ed. vol. i. p. 433.
*Removal of Usual Conditions.*
One of the great objects of experiment is to enable us to judge of the behaviour of substances under conditions widely different from those which prevail upon the surface of the earth. We live in an atmosphere which does not vary beyond certain narrow limits in temperature or pressure. Many of the powers of nature, such as gravity, which constantly act upon us, are of almost fixed amount. Now it will afterwards be shown that we cannot apply a quantitative law to circumstances much differing from those in which it was observed. In the other planets, the sun, the stars, or remote parts of the Universe, the conditions of existence must often be widely different from what we commonly experience here. Hence our knowledge of nature must remain restricted and hypothetical, unless we can subject substances to unusual conditions by suitable experiments.
The electric arc is an invaluable means of exposing metals or other conducting substances to the highest known temperature. By its aid we learn not only that all the metals can be vaporised, but that they all give off distinctive rays of light. At the other extremity of the scale, the intensely powerful freezing mixture devised by Faraday, consisting of solid carbonic acid and ether mixed *in vacuo*, enables us to observe the nature of substances at temperatures immensely below any we meet with naturally on the earth’s surface.
We can hardly realise now the importance of the invention of the air-pump, previous to which invention it was exceedingly difficult to experiment except under the ordinary pressure of the atmosphere. The Torricellian vacuum had been employed by the philosophers of the Accademia del Cimento to show the behaviour of water, smoke, sound, magnets, electric substances, &c., *in vacuo*, but their experiments were often unsuccessful from the difficulty of excluding air.[331]
[331] *Essayes of Natural Experiments made in the Accademia del Cimento.* Englished by Richard Waller, 1684, p. 40, &c.
Among the most constant circumstances under which we live is the force of gravity, which does not vary, except by a slight fraction of its amount, in any part of the earth’s crust or atmosphere to which we can attain. This force is sufficient to overbear and disguise various actions, for instance, the mutual gravitation of small bodies. It was an interesting experiment of Plateau to neutralise the action of gravity by placing substances in liquids of exactly the same specific gravity. Thus a quantity of oil poured into the middle of a suitable mixture of alcohol and water assumes a spherical shape; on being made to rotate it becomes spheroidal, and then successively separates into a ring and a group of spherules. Thus we have an illustration of the mode in which the planetary system may have been produced,[332] though the extreme difference of scale prevents our arguing with confidence from the experiment to the conditions of the nebular theory.
[332] Plateau, *Taylor’s Scientific Memoirs*, vol. iv. pp. 16–43.
It is possible that the so-called elements are elementary only to us, because we are restricted to temperatures at which they are fixed. Lavoisier carefully defined an element as a substance which cannot be decomposed *by any known means*; but it seems almost certain that some series of elements, for instance Iodine, Bromine, and Chlorine, are really compounds of a simpler substance. We must look to the production of intensely high temperatures, yet quite beyond our means, for the decomposition of these so-called elements. Possibly in this age and part of the universe the dissipation of energy has so far proceeded that there are no sources of heat sufficiently intense to effect the decomposition.
*Interference of Unsuspected Conditions.*
It may happen that we are not aware of all the conditions under which our researches are made. Some substance may be present or some power may be in action, which escapes the most vigilant examination. Not being aware of its existence, we are unable to take proper measures to exclude it, and thus determine the share which it has in the results of our experiments. There can be no doubt that the alchemists were misled and encouraged in their vain attempts by the unsuspected presence of traces of gold and silver in the substances they proposed to transmute. Lead, as drawn from the smelting furnace, almost always contains some silver, and gold is associated with many other metals. Thus small quantities of noble metal would often appear as the result of experiment and raise delusive hopes.
In more than one case the unsuspected presence of common salt in the air has caused great trouble. In the early experiments on electrolysis it was found that when water was decomposed, an acid and an alkali were produced at the poles, together with oxygen and hydrogen. In the absence of any other explanation, some chemists rushed to the conclusion that electricity must have the power of *generating* acids and alkalies, and one chemist thought he had discovered a new substance called *electric acid*. But Davy proceeded to a systematic investigation of the circumstances, by varying the conditions. Changing the glass vessel for one of agate or gold, he found that far less alkali was produced; excluding impurities by the use of carefully distilled water, he found that the quantities of acid and alkali were still further diminished; and having thus obtained a clue to the cause, he completed the exclusion of impurities by avoiding contact with his fingers, and by placing the apparatus under an exhausted receiver, no acid or alkali being then detected. It would be difficult to meet with a more elegant case of the detection of a condition previously unsuspected.[333]
[333] *Philosophical Transactions* [1826], vol. cxvi. pp. 388, 389. Works of Sir Humphry Davy, vol. v. pp. 1–12.
It is remarkable that the presence of common salt in the air, proved to exist by Davy, nevertheless continued a stumbling-block in the science of spectrum analysis, and probably prevented men, such as Brewster, Herschel, and Talbot, from anticipating by thirty years the discoveries of Bunsen and Kirchhoff. As I pointed out,[334] the utility of the spectrum was known in the middle of the last century to Thomas Melvill, a talented Scotch physicist, who died at the early age of 27 years.[335] But Melvill was struck in his examination of coloured flames by the extraordinary predominance of homogeneous yellow light, which was due to some circumstance escaping his attention. Wollaston and Fraunhofer were equally struck by the prominence of the yellow line in the spectrum of nearly every kind of light. Talbot expressly recommended the use of the prism for detecting the presence of substances by what we now call spectrum analysis, but he found that all substances, however different the light they yielded in other respects, were identical as regards the production of yellow light. Talbot knew that the salts of soda gave this coloured light, but in spite of Davy’s previous difficulties with salt in electrolysis, it did not occur to him to assert that where the light is, there sodium must be. He suggested water as the most likely source of the yellow light, because of its frequent presence; but even substances which were apparently devoid of water gave the same yellow light.[336] Brewster and Herschel both experimented upon flames almost at the same time as Talbot, and Herschel unequivocally enounced the principle of spectrum analysis.[337] Nevertheless Brewster, after numerous experiments attended with great trouble and disappointment, found that yellow light might be obtained from the combustion of almost any substance. It was not until 1856 that Swan discovered that an almost infinitesimal quantity of sodium chloride, say a millionth part of a grain, was sufficient to tinge a flame of a bright yellow colour. The universal diffusion of the salts of sodium, joined to this unique light-producing power, was thus shown to be the unsuspected condition which had destroyed the confidence of all previous experimenters in the use of the prism. Some references concerning the history of this curious point are given below.[338]
[334] *National Review*, July, 1861, p. 13.
[335] His published works are contained in *The Edinburgh Physical and Literary Essays*, vol. ii. p. 34; *Philosophical Transactions* [1753], vol. xlviii. p. 261; see also Morgan’s Papers in *Philosophical Transactions* [1785], vol. lxxv. p. 190.
[336] *Edinburgh Journal of Science*, vol. v. p. 79.
[337] *Encyclopædia Metropolitana*, art. *Light*, § 524; Herschel’s *Familiar Lectures*, p. 266.
[338] Talbot, *Philosophical Magazine*, 3rd Series, vol. ix. p. 1 (1836); Brewster, *Transactions of the Royal Society of Edinburgh* [1823], vol. ix. pp. 433, 455; Swan, ibid. [1856] vol. xxi. p. 411; *Philosophical Magazine*, 4th Series, vol. xx. p. 173 [Sept. 1860]; Roscoe, *Spectrum Analysis*, Lecture III.
In the science of radiant heat, early inquirers were led to the conclusion that radiation proceeded only from the surface of a solid, or from a very small depth below it. But they happened to experiment upon surfaces covered by coats of varnish, which is highly athermanous or opaque to heat. Had they properly varied the character of the surface, using a highly diathermanous substance like rock salt, they would have obtained very different results.[339]
One of the most extraordinary instances of an erroneous opinion due to overlooking interfering agents is that concerning the increase of rainfall near to the earth’s surface. More than a century ago it was observed that rain-gauges placed upon church steeples, house tops, and other elevated places, gave considerably less rain than if they were on the ground, and it has been recently shown that the variation is most rapid in the close neighbourhood of the ground.[340] All kinds of theories have been started to explain this phenomenon; but I have shown[341] that it is simply due to the interference of wind, which deflects more or less rain from all the gauges which are exposed to it.
[339] Balfour Stewart, *Elementary Treatise on Heat*, p. 192.
[340] British Association, Liverpool, 1870. *Report on Rainfall*, p. 176.
[341] *Philosophical Magazine.*, Dec. 1861. 4th Series, vol. xxii. p. 421.
The great magnetic power of iron renders it a source of disturbance in magnetic experiments. In building a magnetic observatory great care must therefore be taken that no iron is employed in the construction, and that no masses of iron are near at hand. In some cases magnetic observations have been seriously disturbed by the existence of masses of iron ore in the neighbourhood. In Faraday’s experiments upon feebly magnetic or diamagnetic substances he took the greatest precautions against the presence of disturbing substances in the copper wire, wax, paper, and other articles used in suspending the test objects. It was his custom to try the effect of the magnet upon the apparatus in the absence of the object of experiment, and without this preliminary trial no confidence could be placed in the results.[342] Tyndall has also employed the same mode for testing the freedom of electro-magnetic coils from iron, and was thus enabled to obtain them devoid of any cause of disturbance.[343] It is worthy of notice that in the very infancy of the science of magnetism, the acute experimentalist Gilbert correctly accounted for the opinion existing in his day that magnets would attract silver, by pointing out that the silver contained iron.
[342] *Experimental Researches in Electricity*, vol. iii. p. 84, &c.
[343] *Lectures on Heat*, p. 21.
Even when we are not aware by previous experience of the probable presence of a special disturbing agent, we ought not to assume the absence of unsuspected interference. If an experiment is of really high importance, so that any considerable branch of science rests upon it, we ought to try it again and again, in as varied conditions as possible. We should intentionally disturb the apparatus in various ways, so as if possible to hit by accident upon any weak point. Especially when our results are more regular than we have fair grounds for anticipating, ought we to suspect some peculiarity in the apparatus which causes it to measure some other phenomenon than that in question, just as Foucault’s pendulum almost always indicates the movement of the axes of its own elliptic path instead of the rotation of the globe.
It was in this cautious spirit that Baily acted in his experiments on the density of the earth. The accuracy of his results depended upon the elimination of all disturbing influences, so that the oscillation of his torsion balance should measure gravity alone. Hence he varied the apparatus in many ways, changing the small balls subject to attraction, changing the connecting rod, and the means of suspension. He observed the effect of disturbances, such as the presence of visitors, the occurrence of violent storms, &c., and as no real alteration was produced in the results, he confidently attributed them to gravity.[344]
[344] Baily, *Memoirs of the Royal Astronomical Society*, vol. xiv. pp. 29, 30.
Newton would probably have discovered the mode of constructing achromatic lenses, but for the unsuspected effect of some sugar of lead which he is supposed to have dissolved in the water of a prism. He tried, by means of a glass prism combined with a water prism, to produce dispersion of light without refraction, and if he had succeeded there would have been an obvious mode of producing refraction without dispersion. His failure is attributed to his adding lead acetate to the water for the purpose of increasing its refractive power, the lead having a high dispersive power which frustrated his purpose.[345] Judging from Newton’s remarks, in the *Philosophical Transactions*, it would appear as if he had not, without many unsuccessful trials, despaired of the construction of achromatic glasses.[346]
[345] Grant, *History of Physical Astronomy*, p. 531.
[346] *Philosophical Transactions*, abridged by Lowthorp, 4th edition, vol. i. p. 202.
The Academicians of Cimento, in their early and ingenious experiments upon the vacuum, were often misled by the mechanical imperfections of their apparatus. They concluded that the air had nothing to do with the production of sounds, evidently because their vacuum was not sufficiently perfect. Otto von Guericke fell into a like mistake in the use of his newly-constructed air-pump, doubtless from the unsuspected presence of air sufficiently dense to convey the sound of the bell.
It is hardly requisite to point out that the doctrine of spontaneous generation is due to the unsuspected presence of germs, even after the most careful efforts to exclude them, and in the case of many diseases, both of animals and plants, germs which we have no means as yet of detecting are doubtless the active cause. It has long been a subject of dispute, again, whether the plants which spring from newly turned land grow from seeds long buried in that land, or from seeds brought by the wind. Argument is unphilosophical when direct trial can readily be applied; for by turning up some old ground, and covering a portion of it with a glass case, the conveyance of seeds by the wind can be entirely prevented, and if the same plants appear within and without the case, it will become clear that the seeds are in the earth. By gross oversight some experimenters have thought before now that crops of rye had sprung up where oats had been sown.
*Blind or Test Experiments.*
Every conclusive experiment necessarily consists in the comparison of results between two different combinations of circumstances. To give a fair probability that A is the cause of X, we must maintain invariable all surrounding objects and conditions, and we must then show that where A is X is, and where A is not X is not. This cannot really be accomplished in a single trial. If, for instance, a chemist places a certain suspected substance in Marsh’s test apparatus, and finds that it gives a small deposit of metallic arsenic, he cannot be sure that the arsenic really proceeds from the suspected substance; the impurity of the zinc or sulphuric acid may have been the cause of its appearance. It is therefore the practice of chemists to make what they call a *blind experiment*, that is to try whether arsenic appears in the absence of the suspected substance. The same precaution ought to be taken in all important analytical operations. Indeed, it is not merely a precaution, it is an essential part of any experiment. If the blind trial be not made, the chemist merely assumes that he knows what would happen. Whenever we assert that because A and X are found together A is the cause of X, we assume that if A were absent X would be absent. But wherever it is possible, we ought not to take this as a mere assumption, or even as a matter of inference. Experience is ultimately the basis of all our inferences, but if we can bring immediate experience to bear upon the point in question we should not trust to anything more remote and liable to error. When Faraday examined the magnetic properties of the bearing apparatus, in the absence of the substance to be experimented on, he really made a blind experiment (p. 431).
We ought, also, to test the accuracy of a method of experiment whenever we can, by introducing known amounts of the substance or force to be detected. A new analytical process for the quantitative estimation of an element should be tested by performing it upon a mixture compounded so as to contain a known quantity of that element. The accuracy of the gold assay process greatly depends upon the precaution of assaying alloys of gold of exactly known composition.[347] Gabriel Plattes’ works give evidence of much scientific spirit, and when discussing the supposed merits of the divining rod for the discovery of subterranean treasure, he sensibly suggests that the rod should be tried in places where veins of metal are known to exist.[348]
[347] Jevons in Watts’ *Dictionary of Chemistry*, vol. ii. pp. 936, 937.
[348] *Discovery of Subterraneal Treasure.* London, 1639, p. 48.
*Negative Results of Experiment.*
When we pay proper regard to the imperfection of all measuring instruments and the possible minuteness of effects, we shall see much reason for interpreting with caution the negative results of experiments. We may fail to discover the existence of an expected effect, not because that effect is really non-existent, but because it is of a magnitude inappreciable to our senses, or confounded with other effects of much greater amount. As there is no limit on *à priori* grounds to the smallness of a phenomenon, we can never, by a single experiment, prove the non-existence of a supposed effect. We are always at liberty to assume that a certain amount of effect might have been detected by greater delicacy of measurement. We cannot safely affirm that the moon has no atmosphere at all. We may doubtless show that the atmosphere, if present, is less dense than the air in the so-called vacuum of an air-pump, as did Du Sejour. It is equally impossible to prove that gravity occupies *no time* in transmission. Laplace indeed ascertained that the velocity of propagation of the influence was at least fifty million times greater than that of light;[349] but it does not really follow that it is instantaneous; and were there any means of detecting the action of one star upon another exceedingly distant star, we might possibly find an appreciable interval occupied in the transmission of the gravitating impulse. Newton could not demonstrate the absence of all resistance to matter moving through empty space; but he ascertained by an experiment with the pendulum (p. 443), that if such resistance existed, it was in amount less than one five-thousandth part of the external resistance of the air.[350]
[349] Laplace, *System of the World*, translated by Harte, vol. ii. p. 322.
[350] *Principia*, bk. ii. sect. 6, Prop. xxxi. Motte’s translation, vol. ii. p. 108.
A curious instance of false negative inference is furnished by experiments on light. Euler rejected the corpuscular theory on the ground that particles of matter moving with the immense velocity of light would possess momentum, of which there was no evidence. Bennet had attempted to detect the momentum of light by concentrating the rays of the sun upon a delicately balanced body. Observing no result, it was considered to be proved that light had no momentum. Mr. Crookes, however, having suspended thin vanes, blacked on one side, in a nearly vacuous globe, found that they move under the influence of light. It is now allowed that this effect can be explained in accordance with the undulatory theory of light, and the molecular theory of gases. It comes to this--that Bennet failed to detect an effect which he might have detected with a better method of experimenting; but if he had found it, the phenomenon would have confirmed, not the corpuscular theory of light, as was expected, but the rival undulatory theory. The conclusion drawn from Bennet’s experiment was falsely drawn, but it was nevertheless true in matter.
Many incidents in the history of science tend to show that phenomena, which one generation has failed to discover, may become accurately known to a succeeding generation. The compressibility of water which the Academicians of Florence could not detect, because at a low pressure the effect was too small to perceive, and at a high pressure the water oozed through their silver vessel,[351] has now become the subject of exact measurement and precise calculation. Independently of Newton, Hooke entertained very remarkable notions concerning the nature of gravitation. In this and other subjects he showed, indeed, a genius for experimental investigation which would have placed him in the first rank in any other age than that of Newton. He correctly conceived that the force of gravity would decrease as we recede from the centre of the earth, and he boldly attempted to prove it by experiment. Having exactly counterpoised two weights in the scales of a balance, or rather one weight against another weight and a long piece of fine cord, he removed his balance to the top of the dome of St. Paul’s, and tried whether the balance remained in equilibrium after one weight was allowed to hang down to a depth of 240 feet. No difference could be perceived when the weights were at the same and at different levels, but Hooke rightly held that the failure arose from the insufficient elevation. He says, “Yet I am apt to think some difference might be discovered in greater heights.”[352] The radius of the earth being about 20,922,000 feet, we can now readily calculate from the law of gravity that a height of 240 would not make a greater difference than one part in 40,000 of the weight. Such a difference would doubtless be inappreciable in the balances of that day, though it could readily be detected by balances now frequently constructed. Again, the mutual gravitation of bodies at the earth’s surface is so small that Newton appears to have made no attempt to demonstrate its existence experimentally, merely remarking that it was too small to fall under the observation of our senses.[353] It has since been successfully detected and measured by Cavendish, Baily, and others.
[351] *Essayes of Natural Experiments*, &c. p. 117.
[352] Hooke’s *Posthumous Works*, p. 182.
[353] *Principia*, bk. iii. Prop. vii. Corollary 1.
The smallness of the quantities which we can sometimes observe is astonishing. A balance will weigh to one millionth part of the load. Whitworth can measure to the millionth part of an inch. A rise of temperature of the 8800th part of a degree centigrade has been detected by Dr. Joule. The spectroscope has revealed the presence of the 10,000,000th part of a gram. It is said that the eye can observe the colour produced in a drop of water by the 50,000,000th part of a gram of fuschine, and about the same quantity of cyanine. By the sense of smell we can probably feel still smaller quantities of odorous matter.[354] We must nevertheless remember that quantitative effects of far less amount than these must exist, and we should state our negative results with corresponding caution. We can only disprove the existence of a quantitative phenomenon by showing deductively from the laws of nature, that if present it would amount to a perceptible quantity. As in the case of other negative arguments (p. 414), we must demonstrate that the effect would appear, where it is by experiment found not to appear.
[354] Keill’s *Introduction to Natural Philosophy*, 3rd ed., London, 1733, pp. 48–54.
*Limits of Experiment.*
It will be obvious that there are many operations of nature which we are quite incapable of imitating in our experiments. Our object is to study the conditions under which a certain effect is produced; but one of those conditions may involve a great length of time. There are instances on record of experiments extending over five or ten years, and even over a large part of a lifetime; but such intervals of time are almost nothing to the time during which nature may have been at work. The contents of a mineral vein in Cornwall may have been undergoing gradual change for a hundred million years. All metamorphic rocks have doubtless endured high temperature and enormous, pressure for inconceivable periods of time, so that chemical geology is generally beyond the scope of experiment.
Arguments have been brought against Darwin’s theory, founded upon the absence of any clear instance of the production of a new species. During an historical interval of perhaps four thousand years, no animal, it is said, has been so much domesticated as to become different in species. It might as well be argued that no geological changes are taking place, because no new mountain has risen in Great Britain within the memory of man. Our actual experience of geological changes is like a point in the infinite progression of time. When we know that rain water falling on limestone will carry away a minute portion of the rock in solution, we do not hesitate to multiply that quantity by millions, and infer that in course of time a mountain may be dissolved away. We have actual experience concerning the rise of land in some parts of the globe and its fall in others to the extent of some feet. Do we hesitate to infer what may thus be done in course of geological ages? As Gabriel Plattes long ago remarked, “The sea never resting, but perpetually winning land in one place and losing in another, doth show what may be done in length of time by a continual operation, not subject unto ceasing or intermission.”[355] The action of physical circumstances upon the forms and characters of animals by natural selection is subject to exactly the same remarks. As regards animals living in a state of nature, the change of circumstances which can be ascertained to have occurred is so slight, that we could not expect to observe any change in those animals whatever. Nature has made no experiment at all for us within historical times. Man, however, by taming and domesticating dogs, horses, oxen, pigeons, &c., has made considerable change in their circumstances, and we find considerable change also in their forms and characters. Supposing the state of domestication to continue unchanged, these new forms would continue permanent so far as we know, and in this sense they are permanent. Thus the arguments against Darwin’s theory, founded on the non-observation of natural changes within the historical period, are of the weakest character, being purely negative.
[355] *Discovery of Subterraneal Treasure*, 1639, p. 52.Return to passage