Continually aim just beyond your current range

A successful individual typically sets his next goal somewhat but not too much above his last achievement. In this way he steadily raises his level of aspiration.

Kurt Lewin

Among chess players, it is generally accepted that one of the most effective ways to improve one’s skill is to continually play against opponents which are slightly higher rated than you are. In mathematics, the opponents are unsolved or imperfectly understood mathematical problems, concepts, and theories, rather than other mathematicians; but the principle is broadly the same.

Every mathematician, at any given point in time, has a “range”; a region of mathematics which one can effectively handle using one’s existing knowledge, intuition, experience, and “bag of tricks”. Problems within this range may not necessarily be trivial, easy, or routine for this mathematician, but it will be clear to him or her how one should get started on the problem, what the main difficulties are, where in the literature one should look for guidance, which methods are reasonably likely to work and which ones are not, and so forth. In contrast, with problems which are well out of range, it will be much less obvious how to compare the feasibility of various competing approaches, or even how to come up with an approach at all.

It is often tempting for a research mathematician to get into the comfortable habit of only tackling problems which are well within range; this assures a steady stream of unexceptional but decent publications, and spares one the effort of having to learn new fields, new points of view, new developments, or new techniques. But while there is certainly merit in practicing the skills that one have already acquired, and there is undeniably short-term value to one’s career in writing publishable papers, there is a long-term opportunity cost to pursuing such a conservative approach exclusively; mathematical understanding and technology continually progresses, and eventually new ideas from other fields or other approaches will play increasingly important roles in one’s own field of expertise, especially if the field you work in is of particular interest to others. If one does not acknowledge and adapt to these developments, for instance by learning the new tools, there is the long-term danger that one’s bag of tricks may slowly become obsolete, or that one’s results may lose relevance and be increasingly perceived as “boring”.

At the other extreme, there is the temptation to forego the tedious process of incremental improvements and refinements to existing research, and instead jump straight to the really famous or difficult unsolved problems, or to develop some radical new theory, hoping for the mathematical equivalent of “winning the lottery”. A certain amount of ambition in these directions is healthy; for instance, if a promising new technique in the field has just been developed by you or your colleagues, it does make sense to revisit problems or concepts that were previously considered to be too difficult to touch, and see if there is now some potential for dramatic progress. But in many cases, working towards such ambitious goals is premature, especially if one is not familiar enough with the existing literature to know the limitations of certain approaches, or to know what partial results are already known, which are feasible, and which would represent substantial new progress. Working solely on the most difficult problems can also be frustrating, and also fraught with the risk of excitedly announcing an erroneous solution to the problem, followed ultimately by an embarrassing retraction of that high-profile announcement.

Occasionally, one sees a strong mathematician who achieved some spectacular result early in his or her career, but then feels obliged to continually “top” that result, and so from that point onwards only works on the really high-profile problems, disdaining the more incremental work that would steadily increase his or her range. This, I feel, can be an inefficient way to develop a promising talent; there is no shame in making useful and steady progress instead, and in the long term this is at least as valuable as the splashy breakthroughs.

I believe that the optimal way to develop one’s talents is to invest in the middle ground between these two extremes, thus adding new challenges and difficulties to your research program in carefully controlled amounts. Examples of such research objectives include:

• Looking at the easiest problems of interest that you can’t quite completely handle with your existing tools, for instance by taking an unsolved problem and making various assumptions to “turn off” all but one of the difficulties;
• Taking a known result and reproving it by “tying one hand behind your back”, by forbidding yourself to use a method which is effective for that result, but does not extend well to more difficult problems; or
• Taking a known result and generalising it to a situation in which most of the steps in the standard proof of the existing result look like they will extend, but which have just one or two parts which look tricky and will require some modest new idea, trick or insight.

(See also “ask yourself dumb questions”.) Never mind if the resulting project looks so trivial that you’d be embarrassed to publish it (though these sorts of things tend to make wonderful expository notes, which I recommend making available); this is not about the short-term goal of publishing a paper, but about the long-term goal of expanding your range. This is somewhat analogous to exploiting the power of compound interest in long-term investing; imagine, for instance, what your mathematical abilities would be like in a couple decades if you were able to improve your range by, say, 10% a year.

To continue the investment analogy, it also makes prudent sense to have a diversified “research portfolio”, with some fraction of one’s research time going into the “low risk, low reward” category of research problems that are well within one’s range, a larger fraction in the “medium risk, medium reward” category of problems just outside one’s range, and a small fraction in the “high risk, high reward” category of problems well outside one’s range.

Another excellent way to extend one’s range, which I highly recommend, is to collaborate with someone in an adjacent field; I myself have been introduced to many different fields of mathematics in this way. This seems to work particularly well if the collaborator has comparable experience to you, so that you see things at roughly the same level, and thus each of you can easily communicate your insights, intuition and knowledge to each other. (See also “Attend talks and conferences, even those not directly related to your own work”.)

A third approach, which I also find very effective, is to teach a course on a topic which you only partially understand, so that it forces you to get a much better grip on it by the time you actually have to lecture it to your students. (Of course, one has to allow some flexibility in one’s syllabus if it turns out that some topic becomes too difficult, too technical, or too dependent on some external subject matter to be easily teachable in your class.) Investing time into writing lecture notes for this class can be very valuable, both to yourself, to your students, and to other mathematicians who want to understand the topic in the future. (See also “Don’t be afraid to learn things outside your field”.)

In a similar vein: when trying to solve a challenging problem using a given set of techniques, I recommend first replacing the problem with a simpler problem (such as a special case, or a toy model of the problem, or an informal version of the problem in which various non-rigorous “cheats” are enabled, e.g., ignoring any terms that you believe to be negligible, that certain probabilistic heuristics are in fact theorems, or assuming that any plausible algebraic identity that you could in principle work out, is in fact true), with the aim of moving to the simplest version of the problem that isn’t immediately solvable by the techniques you have in mind, but which you believe should still be amenable to those techniques. This tends to focus one’s attention on exactly what one needs to extend the reach of these techniques, and then one can work backwards back up to the original problem. A particularly good model problem to apply this method to is a problem which seems just out of reach of your intended technique, but can still be solved by a different method; in such cases the proof by the other method can provide valuable clues about how to proceed with your intended method, and can also save time by ruling out proof strategies that cannot possibly work because they contradict the conclusions coming from that other method.