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

DIFFICULTIES IN SELECTING A SUBJECT OF RESEARCH. 375

disguised form, and that his hypotheses therefore respecting it are all wrong.

Every investigator also soon rejects questions which are beyond his powers. We are often much better able to judge of the degree of importance of a proposed research than of our ability to carry it out. Our ability to discover is, in most cases, inversely proportional to the degree of intrinsic importance of the desired issue. Many researches might easily be selected which we know beforehand must yield positive, new, and distinct effects, but such investigations are nearly always of a comparatively unimportant kind, because the results of them are generally only additional instances of a similar class to some already known; for instance, most of our tables of constants might be largely extended. It would be hardly possible to suggest a research which would be certain to yield a perfectly anomalous phenomenon. Perhaps the most probable way to suggest a research which would be likely to yield one would be to assume an hypothesis that any substance which is known to behave in an anomalous manner with regard to one force would also behave similarly with regard to another force.

The embarrassment of selection is usually caused partly by a desire to obtain valuable discoveries at little trouble and expense, and partly by our being so little able to predict successfully new important effects. We know so little about what is termed the 'internal resistance' of substances, which is believed to determine largely the special effects of different forces upon them, or of the molecular structures and motions which form essential portions of nearly all physical and chemical phenomena, that the selection of a subject of research is, to some extent, in many cases a leap in the dark.' Those experiments, however, are usually rejected which appear extremely un

certain, unless they can easily be made, and would, if successful, probably yield important results.

A very good plan, and one which I have adopted on various occasions with perfect success, has been to devise an arrangement, and select a research, in which matter or its forces was placed under new conditions, and trust implicitly to the general truth that every new arrangement of matter or force must produce new results.

In other cases the difficulty is usually overcome by selecting from a stock of hypothetical suggestions and questions those which appear to have the greatest degrees of importance, probability, and ripeness, and adopt the most suitable one. Particular researches are sometimes selected, because they are less expensive. In some cases, however, a research is not, strictly speaking, selected at all, but the investigator is led on from a previous inquiry to another by questions which arise at the time, and, having all the materials and apparatus more ready at hand than if he commenced an entirely different subject, he prefers the former; for instance, Faraday appears to have been led on to his discovery of the important law of definite electro-chemical action from his immediately preceding experiments on electrolysis and electric conduction.'

Whilst one scientific man expends his time upon comparatively trifling matters, another slowly and persistently works out a great idea. Most of the ablest of discoverers appear to have acted, to a large extent, upon the plan of exerting the greater part of their strength upon important subjects, and have selected those questions and experiments which, if they can be solved, or can be made to yield a positive result at all, must yield one of

Life of Faraday, by Dr. H. B. Jones, vol. ii. pp. 20-35.

MODE OF CONDUCTING AN ORIGINAL RESEARCH.

377

importance; such, for instance, as definite experiments to test the existence of a new relation between two forces. Oersted acted upon this plan; he asked the question, 'Are electricity and magnetism really related to each other?' and ultimately discovered electro-magnetism; and Faraday in particular employed it, and found, after many trials, magneto-electric induction, and the relation of magnetism to light. Andrews also appears to have acted upon it in his researches on the continuity of the liquid and vaporous states of matter.

CHAPTER XXXIX.

OUTLINE OF A MODE OF CONDUCTING AN ORIGINAL
RESEARCH.

As it may be of service to young experimentalists, I give the following condensed outline of the chief steps to be taken in carrying out one of the commonest forms of original qualitative research in physics or chemistry.

As discoveries are originated in a great variety of ways, it is assumed that in this case the investigator is already acquainted with some phenomenon or mode of working, original or otherwise, which he believes may, by his taking the requisite trouble, yield some new results.

The first step to be taken is to prepare the necessary substances and apparatus; and if it is a chemical research, to ensure at the outset the highest attainable degree of purity of the substances. If apparatus is required, it is necessary to consider carefully first its general plan (aided by a sketch) and its proper magnitude, then each part of it in succession, so as to secure what appear to be the essential conditions of its action, and to exclude those

which would probably prevent or diminish the expected effect; and then to arrange the most delicate means of detecting, and, if necessary, also measuring the effect.

These being provided, a few preliminary experiments may now be made, and as many conclusions drawn from the results of them, and from comparisons of the results with each other, as are proved by the evidence. During these experiments as many hypotheses as possible should be raised by studying the results and conclusions, and notes be kept of all the results, conclusions, remarks, and hypotheses for future reference.

The sources of error and interference should now be excluded, and the phenomenon be obtained, or the method of working be arrived at, in a pure or perfect state and free from unessential conditions, as soon as possible. This is effected by selecting those hypotheses which bear upon the particular points, and testing them by additional experiments and observations, in which each condition is excluded, one only at a time; and this usually requires very varied experiments and considerable thought and trouble.

Having at length obtained, by means of these additional experiments, an approximately perfect form of the phenomenon or method of working, the next step is to make a systematic and comparatively exhaustive examination of each condition of the phenomenon or method, and also to make the experiment with, or employ the method upon, every suitable substance. By making the experiment with every possible substance, the greatest number of conspicuous and exceptional cases will be included; exhaustive researches also generally yield the greatest discoveries, because it is the exceptional cases of the exceptional ones which disclose in the greatest degree the most hidden conditions. During this examination every logical conclusion possible should be drawn from the