Mat 14, 1920] 



SCIENCE 



477 



facilities, equipment, etc., and it is always to 

 be remembered that the problems on -whicli 

 they worked, and the results they achieved 

 were not such as would have enabled them to 

 win in advance either financial support or 

 substantial recognition by the general public 

 or their scientific colleagues. Pasteur could 

 win his institute only by achieved results, not 

 on an advance program for laying the founda- 

 tions of a new science of bacteriology. Dar- 

 win oould hardly have made the origin of spe- 

 cies seem a promising and feasible field of 

 research before he had the evidence of the efii- 

 ciency of selection which made the whole sub- 

 ject of evolution a new and vital one. It is 

 hardly conceivable that Darwin himself would 

 have been able or willing to attempt to formu- 

 late in advance a project which would have 

 covered the main field of his researches. He 

 was working out into lines of thought and ex- 

 perimentation where clearness and feasibility 

 became obvious after, and not before the event. 

 In these days when in certain quarters it is 

 assumed that every research must be outlined 

 and made to appear reasonable in advance, it 

 is worth while to remember that really new 

 fields of study are very likely to look unprom- 

 ising if not hopeless or ridiculous to the execu- 

 tive mind. If we require for every research 

 project that it appear promising and workable 

 within a so-called reasonable time, we put a 

 premium on problems of the easy and less 

 fundamental tyx)e. There is also a psycholog- 

 ical factor here. The man who conceives 

 vaguely at first a great new possibility in the 

 advance of knowledge, is sometimes quite dis- 

 inclined to talk about it merely because it 

 seems so vague, hopeless, and perhaps even 

 ridiculous. If we organize research to such a 

 degree that it shall become the customary, if 

 not the inevitable routine for every worker in 

 an experiment station or research institute to 

 feel that he can only work on problems which 

 can be made to appear plausible and possible 

 of solution in advance, we shall, as in so many 

 socializing schemes, put a premium on medioc- 

 rity, and penalize real originality of the kind 

 which has led in the past to many of the really 

 great advances in knowledge. 



It is, however, always to be remembered that 

 there is probably a greater practical danger of 

 our institutions of research becoming the 

 refuges of incompetents and visionaries than 

 that their methods will nip incipient genius 

 in the bud. The illustrations I have used are, 

 of course, extreme cases, and represent the ex- 

 ceptions rather than the rule as to the mass 

 of scientific work now being done and which 

 has been done in the past. It may well be said 

 that the Darwins and Pasteurs will take care 

 of themselves and that our plans and organi- 

 zations should be for the average run of sci- 

 entific workers. Still this objection overlooks 

 the jwssibility that the case of the scientists, 

 like that of other matters of heredity, can not 

 be adequately analyzed on the basis of the 

 simple assumption of " presence and absence " 

 - — in this case of genius. There are many 

 grades of research ability. I have attempted 

 to differentiate two classes of problems: first, 

 those clearly conceived, and appearing more 

 or less readily capable of solution ; and second, 

 those which, though obviously of vast impor- 

 tance if solved, are imperfectly conceived, or 

 ■appear hopeless, or even fantastic. Still it is 

 obvious enough that many if not most scien- 

 tific problems lie somewhere between these ex- 

 tremes. Any problem which is worthy of 

 serious effort will probably involve in its solu- 

 tion many lines of effort which were not fore- 

 seen at the beginning, and many important 

 problems will seem, even to their projectors, too 

 hopeless of solution to have any wide a.jypea.1, 

 or to win adequate cooperative support, or 

 even the approval of colleagues or superiors in 

 attacking them. 



In considering the whole problem of the 

 stimulation of research we should recognize 

 the limitations of controlled and directed 

 effort, and learn if possible whether in our 

 schemes provision can not also be made for 

 that free and untrammeled environment where 

 personal inclination and initiative are the 

 major factors. Control and executive super- 

 vision become necessary in direct proportion 

 as research is paid for directly as such. This 

 is inevitable if government bureaus and re- 

 search institutions are to be sure of some 



