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 A student once send me email asking me how one goes about doing research in mathematics. I guess that one of the first thoughts that crossed my mind was, "Boy, did you ever ask the wrong person!" Doing research was for me never easy, and certainly not a thing that I ever thought I knew how to do.

Aside from this, it seemed to me that this was like the perenniel question asked of science fiction writers (and in fact all writers): Where do you get your ideas?

When asked this, Harlan Ellison used to respond that he would send a twenty dollar bill and a self-addressed stamped envelope to a certain address in Schenectady, and a few weeks later he would be sent an idea.

Isaac Asimov used to say that he would get lots of ideas for stories while shaving. (Somehow I suspect that he did not use an electric razor.) I've never heard of any mathematicians who got their ideas by shaving. If there's any merit to this approach, it certainly puts women at a disadvantage.

When Einstein was asked how one gets scientific ideas, he replied, "I wouldn't know. I've only had two or three ideas in my whole life."

A less facetious answer than Harlan Ellison's was given to me by an artist I once knew: "Ideas grow out of other ideas." At its best, I think that that's the way things work. More precisely, sometimes it is one's own past work (or, more often, current work) that one gets ideas from, and sometimes they come from thinking about other mathematicians' work.

For my part, I think that this review of my work will show that my own forte was using other people's ideas, especially for purposes for which they were not originally intended.

In any case, ideas don't come out of nowhere.

In my case, it was usually a matter of scrounging. If there is such a thing as mathematician's block, similar to writer's block, then it is certainly something I have had a great deal of first hand experience with.

How One Learns to Do It

For most mathematicians, the process of learning to do research is fairly standard. One starts out by taking classes in graduate school, and doing a lot of homework problems, almost all of which either require one to prove a certain statement or to given an example of a certain phenomenon. ("Give an example of a ring which is not noetherian but is locally noetherian.")  Solving these homework problems involves taking pieces of reasoning that one has seen in class or in books and using these pieces of reasoning in slightly different ways.

Working on problems like this, a mathematics student starts learning the moves, as an actor might say. Or learning his chops (or his licks) as a jazz musician might say. And then eventually, after taking enough courses and doing enough homework problems, one passes the departmental comprehensive exams and finds a dissertation adviser, who will recommend a journal article for the student to read. (In a few cases, the student will already have some experience reading journal articles, but more typically not.) Somewhere in this article, the advisor believes, there will be ideas that are worth working on and which suggest questions which the student may stand a reasonable chance of solving. Often the advisor will suggest a particular question which seems a promising one to investigate.

Closed-ended Questions and Open-ended Questions

In my experience, there are two types of mathematical questions: the open-ended one, where one doesn't even know for sure what one is looking for, and the closed-end one. A typical closed-ended question might ask, "Is X true?" (or perhaps "Under what conditions is X true?" which is slightly less closed-ended) whereas the typical open-ended question might have the form, "What can you say about Y?"

There is a particular kind of open-ended idea which I call the blue-sky idea. Namely, someone sitting at his desk with his feet up and looking out the window has come up with some concept, and now hopes that he or someone he knows can come up with a good way of using that idea. At conferences one sometimes encounters mathematicians who specialize in this sort of idea, button-holing everyone who can't manage to avoid them and inflicting their most recent blue-sky idea on them. My first advisor, when I was at UCSD, was a mathematician who had done some quite illustrious work in analysis, and now wanted to start doing work in algebra. But, in my opinion, he had no idea how to go about doing this. He gave me a blue sky idea. I had no idea how to work on it, and when I told him this he just more or less waved his hands. One day I was complaining to one of my fellow graduate students that I hadn't made any progress at all on my dissertation, and he asked me, "Are you working forty hours a week on it?" I don't think I gave him any response at all. I was too embarrassed to tell him that I didn't know how to go about working even one hour a week on it.

It was very refreshing when I got to New Mexico State and was able to find an advisor, viz. Fred Richman, who actually had quite a bit of experience doing algebraic research. Working with Richman was an interesting experience. I learned never to stop by his office unless I had the rest of the afternoon free. He would ask me, "Well, what have you done since last week?" And I would reply, "Nothing at all," and then tell him about some of the things I had tried that had turned out to be dead ends. And then he would ask me questions. I'd try my best to answer his questions, because I was too embarrassed to admit that I'd never thought about those things at all. And by the time I left his office, I felt that maybe I was getting somewhere after all.

When one looks at the history of mathematics, it may seem that a lot of the most important developments have come out of blue-sky ideas. But in fact, from what I know, this is almost never the case. Good ideas always arise out of some existing line of thought, and it is only after when has put a lot of effort in that one realizes that there is some gradiose general concept that underlies all one's work.

For instance, I am pretty sure that Eilenberg and Steenrod didn't sit down together over a beer one day and say, "Wouldn't it be neat to draw up a set of axioms for a thing called a category and then invent a concept called a functor, and then see if these would be useful for anything?" It's pretty clear that in fact they noticed that in algebraic topology the same sorts of situations keep coming up over and over again, and one keeps seeing different theorems with different subject matter, where somehow the proofs always turned out to be more or less the same. So they saw (I believe) the need for a vocabulary and a conceptual framework that would enable mathematicians to talk about all this in a unified way. Ergo: category theory.