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*Concerns of Young Mathematicians*

Volume 5, Issue 6

5 March 1997

 
An electronically distributed digest for discussions
of the issues of concern to mathematicians at the
beginning of their careers.

Getting Started in Research

In the 19 February 1997 issue of CoYM, Kevin Knudson asked how do you make the transition from graduate student to budding research mathematician? Specifically, how do you go from working on a problem for several years with your advisor's attention and counsel, to independently seeking out and solving your own problems? Anecdotal evidence and advice I have been given point to this being a critical transition, one which many (most?) young mathematicians do not make.

I don't have the answer. Mathematical research is a personal pursuit, and what works for one may not work for another. However, I think I have made that transition, and I have thought a lot about it and have some observations, which I share here. I will refer to events in my career, and this won't apply to everyone, but hopefully it will either stimulate discussion, or help someone.

I managed to prove a new result within two months of starting my first job. While I was fortunate to get so quickly started in new directions, I feel that it was absolutely necessary; you can't go very far extending your thesis or living off ideas that your advisor sends your way. The key is to generate your own ideas. One way to do this is to attend lots of talks and conferences and talk mathematics with as many people as possible. Continually ask yourself questions. I recommend casting a wide net for potential problems; not only are you more likely to find something to your liking, but you will learn more along the way. You don't have to work on problems similar to your thesis for the rest of your career.

That said, you should publish the main results from your thesis. I didn't do this for about a year, and the delay later cost me a lot of time. Instead, right after I finished my Ph.D., I moved to a new city for my first job. I had heard of people who moved, got settled in, then their first term started and they got caught up in their new responsibilities. After a couple of terms, they hadn't done any research and found it difficult to get started.

To avoid this fate, as soon as I arrived and set up my household, I started to think about two ideas I had earlier in my graduate career, but unrelated to my thesis. These ideas were vague, and I didn't get too far with them. One was cut short by the appearance of a manuscript - by someone with whom I had shared my partial understanding the previous spring. I still think the other is interesting, but school quickly started, and by the time I had the time again, I had other ideas.

The first week of any academic term is a time to organize your classes and your schedule and to see your colleagues after a break. It isn't a good time for research. In a new job, there is more dislocation: adjusting to new responsibilities, a new town, new department, and new people. It took me several weeks before I was able to do much else, and by then I had other responsibilities: I was scheduled to give a seminar at my home institution, and then speak at a regional conference the next weekend.

Giving and attending talks is an important component of my research activity. I use talks, particularly at my home institution, to help me organize my ideas or cast them in a new light. It is a challenge to present a coherent explanation of your work in any format. The choices of what to present and how to do it coherently always leads to improvements in how I think about my work. Giving a talk introduces you to your audience, and such introductions lead to worthwhile interactions. This is also a reason to attend seminars, colloquia and to travel to conferences. I recommend footing the bill for some travel yourself if no outside support is available. After all, this is a vital part of the mathematical enterprise.

Another responsibility was a grant application, which turned out to be one of the better uses of my time. In a grant application, you must convince other mathematicians that your good ideas are worth supporting. The exercise of writing one forces you to generate new ideas of what to work on. To assist my thinking, I contacted several people at other institutions and started a dialogue. I have recently written two joint papers with people I first contacted at that time, almost 30 months ago. The value of those contacts isn't these recent papers, but how they helped my thinking about mathematics to evolve.

How do you make contacts with others when you are a fresh Ph.D? I already mentioned giving talks and attending conferences. When I travel or when the department has visitors, I socialize and ask questions that come to mind. It is easiest to meet people who live nearby. I met one of my recent coauthors when I learned that he had also just moved to the same town.

One way I have met other mathematicians is by distributing copies of my papers. When I complete a manuscript and get ready to send it to a journal, I make a list of other mathematicians who may be interested in these results and send them copies with a cover letter describing the main results and why they might be interested. This list consists of people whose papers I have read or cited, people who I have heard speak or heard about, people who have asked me for copies of my work, and my local colleagues. I am not shy about this; at worst, they won't read my paper. I also put my papers on electronic preprint servers. I have met several people this way, some of whom have had me visit or give a talk and one with whom I just wrote a paper.

When writing that grant application, one person I contacted pointed me to a conjecture (in algebra) in one of her papers. After finishing the grant application, I hadn't done any new work in the several months since I handed in my dissertation. Rather than get started, I traveled to the Midwest to give a seminar, visit a friend, and attend a weekend conference. While there, I had a flash of insight one morning in the shower (really!). I realized how it should be possible to prove the afore-mentioned conjecture using geometry.

Generating ideas is necessary, but then you need to bring them to fruition. Research, like other quality pursuits, requires quality time. Discipline may be the most important part of my doing mathematics. I impose deadlines on myself, reserve time solely for research, and try to use my time efficiently. I jealously guard my research time; otherwise it evaporates as there are many other demands on my time. In short, hard, dedicated work is essential.

When I returned home after that trip, I arranged my schedule to give myself some uninterrupted blocks of time. This was a matter of changing when I did my class preparation and other necessary tasks (email, meeting with my TA's, grading homework, lunch, etc.) so that I would have these periods. Then I used this time to try and prove this conjecture. After a very dedicated few weeks, I did it. After a couple of hours of euphoria, I began the hard part - writing up this result and its obvious extensions. I find that I spend more time writing than research, and it is not nearly as fun. It is absolutely necessary to spend this time - if my papers are not carefully written and if I do not make every effort to improve the exposition and clean up the arguments, then few will read my papers. Remember, your readership is a monotone decreasing function of line number.

While writing up this result, I started to work with a coauthor on a further extension, which would have been a fantastic result. After six months of my doing nothing else, we gave up. This failure to get results is quite common, a lot of promising lines of my research fizzle. When this happens, don't let it keep you from trying. When working on a problem, you inevitably learn some new mathematics or get some ideas, or obtain partial results.

Partial results are not necessarily second-class; the problem might be harder than you thought. If the partial results are interesting and lead somewhere, then they are publishable. Only last summer, my coauthor and I came back to this work and wrote a paper whose genesis was the successes we had among our many failures. I think this is the best paper I have written, and we have several more planned. While we have yet to solve the original problem , this has become my most interesting line of research.

During the last half of that first year, I did other things as well; In particular, attended an instructional conference in an area that I am only now just beginning to work in. There I met someone who was very enthusiastic about my thesis and gave me the encouragement I needed to write it up, and who has now become an important mentor. I also met a student there whose research gave me an idea of an application of some of my work. Now we are writing a joint paper on those applications.

At the end of my first year out, while I had failed even to massage my thesis into a preprint and had only solved one new problem, I think that I was on the right track: I had made serious work a habit, I was in regular contact with a number of other mathematicians, and I was thinking about a number of different problems.

Frank Sottile <sottile@msri.org>