August 14, 1882] 



NATURE 



401 



the limitation!; to which our methods are necessarily subject, and 

 as far as possible to estimate the extent to which our results are 

 uncertain. The comparison of estimates of uncertainty made 

 before and af;er the execution of a set of mea urements may 

 sometimes be humiliating, but it is always instructive. 



Even when our results show no greater discrepancies than we 

 were originally prepared for, it is well to err on the side of 

 modesty in estimating their trustworthiness. The history of 

 science teaches only too plainly the lesson that no single method 

 is absolutely to be relied upon, that sources of error lurk where 

 they are least expected, and that they may escape the notice of 

 the most experienced and conscientious worker. It is only by 

 the concurrence of evidence of various kinds and from various 

 sources that practical certainty may at last be attained, and com 

 plete confidence justified. Perhaps I may be allowed to illustrate 

 my meaning by reference to a subject which has engaged a good 

 deal of iny attention for the last two years — the absolute measure- 

 ment of electrical resistance. The unit commonly employed in 

 this country is founded upon experiments made about twenty 

 years ago by a distinguished committee of this Association, and 

 was intended to represent an absolute resistance of io' J . C.G.S., 

 i.e. one ohm. The method employed by the committee at the 

 recommendation of Sir W. Thomson (it had been originally 

 proposed by Weber) consisted in observing the deflection from 

 the magnetic meridian of a needle suspended at the centre of a 

 coil of insulated wire, which formed a closed circuit, and was 

 made to revolve with uniform and known speed about a vertical 

 axis. From the speed and deflection in combination with the 

 m an radius of the coil and the number of its turns, the abso- 

 lute resistance of the coil, and thence of any other standard, 

 can be determined. 



About ten years later Kohlrausch attacked the problem by 

 another method, which it would take too long to explain, and 

 arrived at the result that the B.A, unit was equal to 1-02 ohms 

 — about two per cent, too large. Rowland, in America, by a 

 comparison between the steady battery current flouing in a 

 primary coil with the transient current developed in a secondary 

 coil when the primary current is reversed, found that the B.A. 

 unit was '991 ohm-. I.orentz, using a different method again, 

 found '980, while II. Weber, from di-tinct experiments, arrived 

 at the conclusion that the B.A. unit was correct. It will be seen 

 that the results obtained by these highly competent observers 

 range over about four per cent. Two new determinations have 

 lately been made in the Cavendish laboratory at Cambridge, one 

 by myself with the method of the revolving coil, and another 

 by Mr. Glazebrook, who used a modification of the method 

 followed by Rowland, with the result that the B.A. unit is '0,86 

 ohms. I am now engaged upon a third determination, using a 

 method which is a modification of that of Lorentz. 



In another important part of the field of experimental science, 

 where the suhject-matter is ill understood, and the wotk is 

 qualitative rather than quantitative, success depends more di- 

 rectly upon sagacity and genius. It must be admit ed that much 

 labour spent in this kind of work is ill-directed. Bulky records 

 of crude and uninterpreted observations are not science, nor 

 even in many cases the raw material out of which science will be 

 constructed. The door of experiment stands always open ; and 

 when the question is ripe, and the man is found, he will nine 

 times out of ten find it necessary to go through the w>rk again. 

 Observations made by the way, and under favourable conditions, 

 may often give rise to valuable suggestion--, but these must be 

 tested by experiment, in which the conditions are simplified to 

 the utmost, before they can lay claim to acceptance. 



When an unexpected effect is observed, the question will arise 

 whether or not an explanation can be found upon admitted 

 principles. Sometimes the answer can be quickly given ; but 

 more often it will hippen that an assertion of what ought to 

 have been expected can only be made as the result of an elaborate 

 discussion of the circumstances of the case, and this discussion 

 mu t generally be mathematical in its spirit, if not in its form. 

 In repeating, at the beginning of the century, the well-known 

 experiment of the inaudibility of a bell rung in vacuo, Leslie 

 made the interesting observation that the presence of hydrogen 

 was inimical to the production of sound, so that not merely was the 

 sound less in hydrogen than in air of equal pressure, but that 

 the actual addition of hydrogen to rarefied air caused a diminu- 

 tion in the intensity of sound. How is this remarkable fact to 

 he explained ? Does it prove that, as Herschel was inclined to 

 think, a mixture of gases of widely different densities differs in 

 its acoustical properties from a single gas? These questions 



could scarcely be answered satisfactorily but by a mathematical 

 investigation of the process by which vibrations are communi- 

 cated from a vibrating solid body to the surrounding gas. Such 

 an investigation, founded exclu-ively upon principles well esta- 

 blished before the date of Leslie's observation, was undertaken 

 years afterwards by Stokes, who proved that w hat Leslie ob- 

 served was exactly what ought to have been expected. The 

 addition of hydrogen to attenuated atr increases the wave-length 

 of vibrations of given pitch, and consequently the facility with 

 which the gas can pass round the edge of the bell from the 

 advancing to the retreating face, and thus escape those rare- 

 factions and condensations which are essential to the formation 

 of a complete sound wave. There remains no reason for sup- 

 posing that the phenomenon depends upon any o'her elements 

 than the density and pressure of the gaseous atmosphere, and a 

 direct trial, e.g. a comparison between air and a mixture of car- 

 bonic anhydride and h)drogen of like density, is almost su- 

 perfluous. 



Examples such as this, which might be multiplied ad libitum, 

 show how difficult it often is for an experimenter rightly to 

 interpret his results without the aid of mathematics. It is 

 eminently desirable that the experimenter himself should be in 

 a position to make the calculations, to which his work gives 

 occasion, and from which in return he would often receive 

 valuable hints for further experiment. I should like to see a 

 course of mathematical instruction arranged with e-i ecial 

 reference to physics, with n which those whose be t was plainly 

 towards experiment might, more or less completely, confine them- 

 selves. Probably a) ear spent judiciously on such a course would 

 do more to quabfy the student for actual work than two or three 

 years of the usual mathe 1 atical curriculum. On the other side, 

 it must be remembered that the human mind is limited, and that 

 few can carry the weight of a complete mathematical armament 

 without some repression of their energies in other directions. 

 With many of us difficulty of remember, ng, if not want of time 

 for acquiring, would imp 'se an early limit. Here, as elsewhere, 

 the natural advantages of a division of lab air will assert them- 

 selves. Innate dexterity and facility of contrivance, backed by 

 unflinching perseverance, may often conduct to successful dis- 

 covery or invention a man who has little taste for speculation j 

 and on the other hand the mathematician, endowed with genius 

 and insight, may find a sufficient field for his energies in inter- 

 preting and systemati-ing the work of others. 



The different habits of mind of the two schools of physicists 

 sometimes lead them to the adoption of antagonistic views on 

 doubtful and difficult questions. The tendency of the purely 

 experimental school is to rely almost exclusively upon direct 

 evidence, even when it is obviously imperfect, and to disregard 

 arguments which they stigmatise as theoretical. The tendency 

 of the mathematician is to overrate the solidity of his theoretical 

 structures, and to forget the narrowness of the experimental 

 foundation upon which many of them rest. 



By direct observation, one of the most .experienced and suc- 

 cessful experimenters of the last generation convinced himself 

 that light of definite refrangibility was capable of further analysis 

 by absorption. It has happened to myself, in the course of 

 measurements of the absorbing power of various media for the 

 different rays of the spectrum, to come across appearances at 

 first sight strongly confirmatory of Brewster's views, and I can 

 therefore understand the persistency with which he retained his 

 opinion. But the possibility of further analysis of light of 

 definite refrangibility (except by polarisation) is almo-t irre- 

 concilable with the wave theory, which on the strongest grounds 

 had been already accepted by most of Brewster's contemporaries; 

 and in consequence his results, though urgently pressed, failed 

 to convince the se'entific world. Further experiment has fully 

 ju-tified this scepticism, aid in the hands of Airy, Helmholtz, 

 and others, has shown that the phenomena by which Brewster 

 was misled can be explained by the unrecognised inlru ion of 

 diffused light. The anomalies disappear when sufficient pre- 

 caution is taken that the refrangibility of the light observed shall 

 really be definite. 



On similar grounds undulationists early arrived at the con- 

 viction that physically light and invisible radiant heat are both 

 vibrations of ihe same kind, differing n-erely in wave-length ; 

 but this view appears to have been accepted slowly, and almost 

 reluctantly, by the experimental school. 



When the facts which appear to conflict with theory are well 

 defined and lend themselves easily to experiment and repetition, 

 there ought to be no great delay in arriving at a judgment. 



