204 



SCIENCE 



[N. S. Vol. XLIX, No. 1261 



results are expected and even demanded. In 

 purchasing laboratory equipment for research 

 it has indeed happened sometimes, — so I am 

 told, — that research apparatus has been pur- 

 chased under the false pretense that it was 

 needed in teaching! If botanical research is 

 one of our responsibilities as botanists, I sub- 

 mit that this anomaly demands some serious 

 attention. 



The other striking characteristic of much 

 of our scientific research is this, that most of 

 the published work appears to be done by 

 apprentices. I refer to publications by begin- 

 ners, like dissertations for the doctorate of 

 philosophy in our universities. I can think of 

 no other line of important human activity in 

 which the work of apprentices looms so large 

 as it does in botanical and other sciences. 

 This state of affairs would not be so bad if 

 the leaders imder whose guidance the work 

 has been done could take enough part in it to 

 save the publications from the verge of futil- 

 ity. As would be expected of apprentice work, 

 these publications frequently show poor plan- 

 ning and more frequently poor interpretation. 

 The gathering of data may be well done, 

 within the limits set by the plans. There 

 seem to be some possible ways out of this 

 difficulty, but I shall not take time here to 

 mention even the ones I have had in mind. — I 

 turn now to my three phases or aspects of 

 research. 



(a) The Planning of Research. — It has 

 seemed to me that the planning of scientific 

 investigation deserves very much more at- 

 tention than it generally receives. Wot having 

 any clear aims, we are apt to be misled to 

 the erroneous idea that all sorts of research 

 are of equal importance. Perhaps it is not 

 any longer fashionable to tell students that 

 the mere gathering of facts in any field con- 

 stitutes valuable scientific work, but we surely 

 have not passed far beyond the conception that 

 a personal and capricious interest is a proi)er 

 and respectable guide in the choosing of a 

 problem and in determining how it is to be 

 carried out. It often seems that each worker 

 brings forward his contributions without any 

 notion as to how they are to fit into the struc- 



ture of the science as a whole. It is some- 

 what as though each of us brought what he 

 happened to have and threw it on a large and 

 heterogeneous pile, hoping that a rational 

 structure might, by some tmknown means, be 

 builded therefrom. We seem to feel little or no 

 responsibility in the building itself, we bring 

 contributions that can not be used at present 

 and we let the building operations stop at 

 many points because we do not bring the ma- 

 terials that are immediately needed. 



A well-selected problem does not always 

 mean a well-planned investigation, however; 

 and an opportune problem has often led to 

 great waste of time and work simply because 

 the method of attack was hurriedly decided 

 upon. As you have surely observed, experi- 

 mental and observational investigation, as it 

 is published, frequently shows what almost 

 seems to be a genius for omitting the needed 

 experimental controls. Again, things that are 

 of relatively small importance are often dwelt 

 on with great care, while the most outstanding 

 points are woefully neglected. ISTeeds that 

 should have been cared for in the preliminary 

 plan are often not appreciated until the ex- 

 perimental or observational work is completed, 

 when it is too late to mend matters. 



I have been led to think that this condition 

 of affairs is largely due to a still more or less 

 prevalent and very insidious fallacy, to the 

 effect that a scientific investigator can not 

 hope to find out what he sets out to find out, 

 but has to drift with winds and currents and 

 gather in the observations and results that he 

 happens to run across. It is sometimes the 

 business of a pioneer explorer to work in this 

 way, but I think we should hardly call that 

 sort of work scientific research in the modern 

 sense. Discoveries of facts may be made now 

 and then by chance and intuition, but discov- 

 eries of relations (with which our science now 

 mostly deals) are largely to be made by taking 

 serious thought as to just what we need to do 

 in order to find out just what we set about find- 

 ing out. 



, You have been Warned earlier in this ad- 

 dress of the fact that I regard cooperation as 

 the touchstone by which we may hope to cure, 



