Excerpts from “On Some Tendencies in Geometric Investigations” by Corrado Segre

In 1904, Corrado Segre published On Some Tendencies in Geometric Investigations. In this essay, he sought to encourage young mathematicians, attracted to the then-trendy field of algebraic geometry, to pursue deeper investigations of important problems and to seek broader understanding of other, less popular, areas of mathematics. I have included excerpts from the English translation by J. W. Young (with minor edits), which I believe may be useful to fellow researchers in the now-trendy field of machine learning.


… Thus, owing to the exceeding growth of geometric research as well as of methods of transformation, grew also proportionately the facility mentioned by the great French geometer [Michel Chasles] of increasing without limit the number of new propositions, of generalizing and creating in geometry. And this facility which, at least apparently, is greater in this science than in analysis, in mathematical physics, etc., induces many young men, especially in Italy, to give geometry the preference over other branches of mathematics, some of which indeed are very sadly neglected by our students. 

But facility is a bad counsellor; and often the work to which it leads the beginner, while it may serve as training, as preparation for original research, will not deserve to see the light. In the innumerable multitude of scientific publications, geometric writings are not rare in which one would seek in vain for an idea at all novel, for a result which sooner or later might be of service, for anything in fact which might be destined to survive in the science. And one finds instead treatises on trivial problems or investigations on special forms which have absolutely no use, no importance, which have their origin not in the science itself but purely in the caprice of the author; or one finds applications of known methods which have already been made thousands of times; or generalizations from known results which are so easily made that the knowledge of the latter suffices to give at once the former; etc. 

Now such work is not merely useless: it is actually harmful because it produces a real incumbrance in the science and an embarrassment for more serious investigators, and because often it crowds out certain lines of thought which might well have deserved to be studied. Better, far better, that the student, instead of producing rapidly a long series of papers of such a nature, should work hard for a long time on the solution of a single problem, provided it is important: better one result fit to live than a thousand doomed to die at birth!1


But when is a question important? When does it deserve to be made the object of study? 

It is impossible to give a precise answer to this question. The importance of a result is largely relative, is judged differently by different men, and changes with the times and circumstances. It has often happened that great importance has been attached to a problem merely on account of the difficulties which it has presented; and indeed if for its solution it has been necessary to invent new methods, noteworthy artifices, etc., the science has gained more perhaps through these than through the final result. In general we may call important all investigations relating to things which in themselves are important; all those which have a large degree of generality, or which unite under a single point of view subjects apparently distinct, simplifying or elucidating them; all those which lead to results that promise to be the source of numerous consequences; etc. 

The study of the great masters is perhaps the best thing to recommend to the student who wishes to prepare himself to judge of the importance of problems. For it is precisely in the choice of these that the great minds have always shown themselves masters; and even when they have taken up very special problems, they have shown in what way those could become important. And here, in corroboration of the preceding, I will quote the words of Beltrami: “Students should learn to study at an early stage the great works of the great masters instead of making their minds sterile through the everlasting exercises of college, which are of no use whatever, except to produce a new Arcadia where indolence is veiled under the form of useless activity…. Hard study on the great models has ever brought out the strong; and of such must be our new scientific generation if it is to be worthy of the era to which it is born and of the struggles to which it is destined.” 

In such studies one should ever keep before him this other object: to broaden as much as possible his own knowledge. He who is interested only in works relating to the limited field which he is studying, will in the end give undue weight to questions which do not seem so important to another, who with broader knowledge looks at the subject from a higher point of view. It should be the aim of the student by an extended study of the best works in all branches, to attain a wider horizon with regard to the whole science.

1To students who are looking toward the doctorate in mathematics it is well to say frankly that science should not be thought of as a profession in which all can succeed. Though it be true that genius is no longer essential to produce useful results, still a certain aptitude is necessary; and he who knows himself to be without it should, with that veneration and sacrifice which science demands, renounce scientific research. Why should a young man, who could perhaps teach successfully the elementary mathematics and study thoroughly the numerous and important pedagogical questions which present themselves in his teaching, neglect such studies, in order to take up researches in higher mathematics which are not adapted to his type of mind?


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