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SCIENCE 



[Vol. LV, No. 1428 



picture of what would have happened if 

 Pasteur had, at the behest of some supervising 

 agency, undertaken as a first problem some- 

 thing else than the isomerism of tartaric acids, 

 and thereby missed the germ theory of disease, 

 it must lie in the belief that a man of Pasteur's 

 timber would have done great things in another 

 field. But such a consideration does not 

 answer the argument that his early work, prac- 

 tical or not, was a necessary training in order 

 that his maturer work might be valuable. 



Doubtless the case of Pasteur can be dupli- 

 cated by that of other eminent scientists whose 

 first research seemed to . bear no relation to 

 their later high attainments. Perhaps that is 

 regularly true, except in the small number of 

 eases in which by the laws of chance it is to be 

 espected that preliminary work and eventual 

 important discoveries shall lie in the same field. 

 The fields in which the accomplishments of 

 great investigators lie may thus appear to be 

 matters of accident; but then, an accident is 

 but the inevitable consequence of other acci- 

 dents that have gone before. 



If it is not fatal, but sometimes even useful, 

 to start the new investigator on his way with 

 a problem whose solution promises no practical 

 improvements in human affairs, what is to be 

 said of those who are mature in research? 

 Probably most of these trained workers would 

 be better satisfied with their showing to their 

 fellow men, even if not more content with 

 themselves, if they could be perpetually en- 

 gaged on practical projects. Even if it be 

 granted, as has been done in the introductory 

 remarks of this address for the sake of limiting 

 the discussion, that practically useful investi- 

 gations are the only ones desirable, is it pos- 

 sible to maintain a system of research in which 

 only practical things are attempted, and make 

 it work? For various reasons the practical 

 problem that suggests itself to an investigator 

 may be one which he can not undertake. Lack 

 of facilities readily accounts for many such 

 cases, geographical position for others. The 

 problem that seems most feasible may not seem 

 highly important even from the pure science 

 point of view. What is the investigator to do 

 under these circumstances? Refrain from 

 undertaking a problem which he feels sure is 



not of great value? Even if that means doing 

 no research at all? Perhaps. But if he de- 

 cides to keep on working, he may take comfort 

 in the story of the foolish virgins, and reflect 

 that in his small way he is keeping his lamp 

 trimmed and burning even at the cost of some 

 oil which seems wasted, until the bridegroom 

 Cometh with a problem that is more worth 

 while. For nothing is so quickly fatal to re- 

 search as interruption of it. This university 

 furnished, for valuable war work, some inves- 

 tigators whose previous work was regarded 

 even by themselves as of small value. I am not 

 speaking of any of you here present. The 

 gentlemen to whom I refer are in their labora- 

 tories to-night. They find the labors to which 

 the great conflict introduced them so pleasur- 

 able, nay, even enthralling, that they have no 

 time to listen to mere presidential addresses. 

 The life of any eminent scientist of the present 

 generation would probably furnish a further 

 example of the ad interim value of unimport- 

 ant research. At least this is true of those in 

 my own field upon whom I have taken the 

 trouble to reflect. They have engaged in con- 

 tinuous investigation, the continuity being due 

 in part, in every case, to insignificant produc- 

 tions. It is very seldom, and then only under 

 unusual circumstances, that a serious interrup- 

 tion is followed by a return to high produc- 

 tivity. 



Nor must it be forgotten that many men 

 who are engaged in research of minor value 

 are the trainers of new investigators who may 

 be more "lucky" than themselves. I think with 

 profound respect of the professor of physics 

 in a small western college who keeps working 

 in a small way, who has never made a striking 

 contribution, practical or otherwise, to his 

 science, but who every year or two sends to a 

 great eastern university a graduate student. 

 Although these students are most of them still 

 young men, they have done creditable things, 

 some of them practical. Is it likely that the 

 professor in the small college could thus inspire 

 his students to a career of learning without the 

 stimulus that comes from his own research? 

 You may answer this question to your own 

 liking, as I am doing. In a vicarious way, this 

 man seems likely to exert upon his science an 



