1 asking in succession what effect will each have upon the particular phenomenon. The following fragment of such a table will show what I mean:-What will be the effect of gravity, pressure, motion, heat, light, electricity, magnetism, chemical affinity; and of varying time of action, direction, and strength of each of these; also the effect of conduction, radiation, refraction, reflection, and polarisation of heat upon it. And so on through all the chief phenomena of all the forces of nature in succession; and also asking what will be the effect of different classes of elementary substances, metals, metalloids, &c., and all the separate elementary substances and their compounds in succession. Instead of such a table, a copious index of any good book on physical and chemical science may be employed for the purpose. In this way even a student of science may suggest a large number of new questions respecting any phenomenon. Having obtained a collection of new ideas and hypotheses in this way, the investigator can proceed no farther without experiment, because hypotheses are unverified ideas and may be true or untrue, and those which are true can only be found by actual trial or observation. To the solid ground of nature, trusts the mind that builds for all.' Schönbein made ozone the study of his life; but as he did not make sufficiently numerous experiments upon that substance, it is not to him so much as to other investigators that we are chiefly indebted for our knowledge respecting it. 6 New hypothetical questions having been suggested, it is of service to write them out in the clearest form, and make sketches of their anticipated operation and effects, for in the absence of the actual object no man can so vividly realise and perfect his ideas as when they are put upon paper. Writing also enables a man to fix his mind more strongly and continuously on a subject, and to carry FORMATION OF NEW HYPOTHESES. 371 on the necessary process of reasoning. The use of symbolic language (as in chemical equations, &c.), and the presence of the actual substances and apparatus required for the experiments, also afford additional aid. Sometimes one man raises an hypothesis and another tests it; thus Cassini suggested the mode of measuring the velocity of light by means of the eclipses of the moons of Jupiter, and Röemer tested it and found it correct. Halley suggested, and succeeding astronomers evolved, the discovery of the method of ascertaining the sun's distance from the earth by means of the transit of Venus. ghens, in the year 1678, suggested the theory of the existence of an universal ether pervading all bodies and all space, and Young and Fresnel tested it. Also Odling's hypothesis that in ozone the oxygen was condensed one half was partly proved by Brodie in 1871.1 Huy Sometimes, also, one man tries unsuccessfully to imagine the true conception which another afterwards succeeds in conceiving. Malus sought in vain the formula determining the angle at which a transparent surface polarises light; Sir D. Brewster, with a happy sagacity, discovered the formula to be simply this, that the index of refraction is the tangent of the angle of polarisation.”2 1 Brodie, Proceedings of Royal Society, 1872, vol. xx. p. 472; Odling, 'History of Ozone,' Proceedings of Royal Institution, 1872. 2 Whewell, Philosophy of the Inductive Sciences, vol. ii. p. 542. PART IV. ACTUAL WORKING IN ORIGINAL RESEARCH. CHAPTER XXXVIII. SELECTION OF A SUBJECT OF INVESTIGATION. One science only will one genius fit, But oft in those confined to single parts. ANY man who wishes to discover new truth must be content usually to confine his search to one subject at a time. The selection of a good subject of examination is a difficult problem; the difficulty usually arises not from scarcity of subjects, but from the impracticability of determining which is the most suitable one. An investigator cannot, to any great degree, pick and choose discoveries, but must, to a large extent, be content to accept those he can find. In the selection of a subject of research he has to consider what subjects are intrinsically important, and that is often a difficult question.1 In con 1 See Chap. XIX. SELECTION OF A SUBJECT OF INVESTIGATION. 373 sequence of our very imperfect power of prediction we are very apt to value wrongly the importance of an unmade research; some of the greatest truths have been ultimately disclosed by investigating what previously appeared to be most trivial phenomena. The discovery of static electricity is said to have arisen from the circumstance that a bit of amber, by being rubbed, acquired the property of attracting a feather. That of magnetism was probably equally simple, and is said to have been first observed in a piece of loadstone. That of voltaic electricity also arose from an apparently trivial circumstance, which has already been described in this book. There are, however, cases where the investigator knows beforehand, with considerable certainty, from the nature of his proposed question and the conditions of his experiment, that if the hoped-for positive results are obtained, they must necessarily be important. The successful search by Faraday for magneto-electric induction, and his unsuccessful one for an experimental connection between gravity and the other physical forces, were instances of this kind. And there are other cases where the investigator knows beforehand that he is nearly certain to produce some new results, but is unable to foretell what they will be. In the first of these cases he wishes to know what conditions will render evident a particular new and important effect; and in the second, what effects will result from a particular cause or class of circumstances. The investigator, in selecting his subject, has also to consider whether the conditions of the proposed research are sufficiently ripe, and that is another very knotty point. Even Newton himself could not discover the universal action of gravity when he first attempted to do so, because he made his first endeavour before the conditions were ready, and that could not have been ascertained without a trial. The ripening of a subject for research is affected by the length of time which has elapsed since the subject was last examined. The longer period of time a particular branch of science has been neglected, the more ready usually it is for a new investigation, because collateral branches of science have advanced and left it behind; several portions of inorganic chemistry, that of the fluorides for example, have been neglected, and are in this condition. Some investigators avoid examining a subject which has been recently and extensively investigated; it is, nevertheless, evident that however recently a subject has been examined, if from any cause it is likely to yield new results, it is in a fit state for further investigation. Great discoveries ripen very slowly. Now that the great discovery of spectrum analysis is a well-known truth, we can easily perceive that the conditions of it were maturing by means of successive researches, from the year 1802, when Wollaston detected lines in the solar spectrum, and the year 1815, when Fraunhofer measured their positions, until 1859, when Kirchoff and Bunsen discovered the composition of the sun's atmosphere, and thus suddenly made known its greatness. Another very uncertain point in selecting a subject is the degree of probability of success in making the research. In making new experiments, all kinds of obstacles and new effects arise which we cannot foresee, and from that and other causes, such as our limited means of detecting effects, we rarely obtain from such experiments the expected results. An investigator has not unfrequently to advance some distance into a preliminary research before he can determine whether or not he has really a definite and new question upon which to work; and he often finds, after much expenditure of time and trouble, that the supposed new phenomenon is only an old one in a |