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“.)

## 14 comments

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21 September, 2007 at 12:39 pm

Another advice page, and an open thread « What’s new[…] Friday, September 21st, 2007 in admin I have added another essay to my career advice page, inspired partly by some earlier blog discussion, entitled “Continually aim just beyond one’s current range“. […]

24 September, 2007 at 2:22 pm

AdamDear Terry,

In the first paragraph, I would add the following sentence:

In applied mathematics, from time to time there come up

new theories. Due to their “up for grabs” nature, interested

parties play everybody against each other, like in simultaneous

chess (where no clocks are used). After the dust settles, the

few that remain in the game become leaders, and hard open

problems are left out as opponents for mathematics. If you

want to become one of such players, beware of the pitfalls.

If you are already in the game and are bored of your opponents,

see if the spectators can provide any challenge.

2 November, 2007 at 9:54 am

What I’ve Learned So Far » Blog Archive » Career building: Terence Tao offers his version of the Medawar Zone.[…] Tao, who is a mathematician, doesn’t call it the Medawar Zone, but as I read this post, that’s what I kept thinking of. Continually aim just beyond your current range […]

4 November, 2007 at 6:54 pm

Jonathan Vos PostRobert Browning’s “Andrea del Sarto” [1855], lines 97-98:

“A man’s reach should exceed his grasp, else what’s a heaven for?”

There, my double B.S. in Math and English from Caltech [1973] finally paid off.

11 May, 2009 at 11:36 am

How to Choose a Research Topic « Successful Researcher[…] have already defended one, indeed) or, more broadly, beyond your current area of research (see e.g. this post of Terence […]

5 July, 2009 at 2:31 pm

nikDear Terry,

it is a nice idea to switch the field or check other problems from time to time. But I don’t know how to quickly and efficiently learn a new field. It can be difficult to get the complex structure of technical results within a reasonable amount of time. What strategy would you suggest for doing this? Reading reviews? Talking to experts?

Best

25 August, 2011 at 9:15 am

The Collatz conjecture, Littlewood-Offord theory, and powers of 2 and 3 « What’s new[…] mathematicians tend to spend the majority of their time on more productive research areas that are only just beyond the range of current techniques. Nevertheless, it can still be diverting to spend a day or two each year on these sorts of […]

28 August, 2011 at 1:42 am

Principles: randomness/structure or emergent from a common cause? | chorasimilarity[…] is a very profound and mysterious one, the second part (Structure) is only an illusion created by psychological choices (I guess). Indeed, both (Lie) smooth structure and nilpotence are just “noncommutative […]

24 December, 2011 at 10:09 pm

AnonymousMy complaint has always been that, in math, unlike other fields, there ARE no problems just slightly above one’s current abilities. Math problems (at least for me) always seem to fall into 2 distinct categories: the extremely trivial vs the extremely hard (the big open problems). I have practically never spent any real hard time tackling the big open problems, other than maybe a fleeting 5 minutes once a year, pondering, for example, the binary Goldbach Conjecture by playing around with elementary means, nor do I intend to – because I have always followed Dr Tao’s advice, having quite consciously known that. Instead, I have sought those “intermediate” level math problems to exercise and stretch my skills, but all the ones I find fall back to being elementary problems, I find.

I have always believed in and followed my (deceased) father’s advice of “learn by doing” – in physical as well as mental activities. However, math itself does not care about human wisdom or our humility or arrogance towards it. So, while learn by doing, specifically by doing slightly beyond one’s reach, has worked in, for example, learning mechanical skills, fixing things – with math, I keep finding myself hitting plateaus, above which I perceive never to rise. On the other hand, I have no outside guide to examine my work and tell me otherwise.

14 November, 2012 at 9:42 am

Expanding polynomials over finite fields of large characteristic, and a regularity lemma for definable sets « What’s new[…] found this project to be particularly educational for me, as it forced me to wander outside of my usual range by quite a bit in order to pick up the tools from algebraic geometry and Riemann surfaces that I […]

27 March, 2013 at 11:38 pm

Learn and relearn your field -Terence Tao | Readings for the Distinguishing Palatte[…] using efficient mental shorthand; this not only allows you to use these results effortlessly, and improve your own ability in the field, but also frees up mental space to learn even more […]

3 April, 2013 at 10:14 pm

Success as a Scientist: Rules of Thumb | The Limitless Project[…] Aim for Rough Water. This perhaps coincides with Geoff Colvin’s deep practice explained in “Talent is Overrated”. To achieve mastery, you have to continually move out of your comfort zone into the learning zone (and of course, avoid the panic zone). The roughest waters are possibly the learning zone for some (and the panic zone for most) but that is where you will learn and become better at your craft. J.D Watson says avoid dumb people and go with people brighter than you are. Possibly a call for aiming towards rough water. In the post “Continually aim just beyond your current range” by Terrance Tao, he calls unsolved or not well-understood problems opponents that are better than you but warns against diving into a big problem hoping for a jackpot. Again, I would see this as a learning zone versus a panic zone kind of thing. https://terrytao.wordpress.com/career-advice/continually-aim-just-beyond-your-current-range/ […]

4 April, 2013 at 8:31 am

Thursday thought | simpleimages2[…] https://terrytao.wordpress.com/career-advice/continually-aim-just-beyond-your-current-range/#comment-… […]

8 June, 2016 at 2:36 pm

AnonymousSometimes, a (too strong) conviction in good (but still imperfect) knowledge of the limitations of existing approaches can “blind” even an experienced mathematician from seeing (via “dumb questions”) simple key ideas !