Frequent Asked Questions on Mathematics

Frequent Asked Questions on Mathematics
By Terence Tao

Compiled by Alexander Arbieto

Does one have to be a genius to do maths?

Better beware of notions like genius and inspiration; they are a sort of magic wand and should be used sparingly by anybody who wants to see things clearly. (José Ortega y Gasset, “Notes on the novel”)

Does one have to be a genius to do mathematics?

The answer is an emphatic NO. In order to make good and useful contributions to mathematics, one does need to work hard, learn one’s field well, learn other fields and tools, ask questions, talk to other mathematicians, and think about the “big picture”. And yes, a reasonable amount of intelligence, patience, and maturity is also required. But one does not need some sort of magic “genius gene” that spontaneously generates ex nihilo deep insights, unexpected solutions to problems, or other supernatural abilities.

The popular image of the lone (and possibly slightly mad) genius - who ignores the literature and other conventional wisdom and manages by some inexplicable inspiration (enhanced, perhaps, with a liberal dash of suffering) to come up with a breathtakingly original solution to a problem that confounded all the experts - is a charming and romantic image, but also a wildly inaccurate one, at least in the world of modern mathematics. We do have spectacular, deep and remarkable results and insights in this subject, of course, but they are the hard-won and cumulative achievement of years, decades, or even centuries of steady work and progress of many good and great mathematicians; the advance from one stage of understanding to the next can be highly non-trivial, and sometimes rather unexpected, but still builds upon the foundation of earlier work rather than starting totally anew. (This is for instance the case with Wiles‘ work on Fermat’s last theorem, or Perelman’s work on the Poincaré conjecture.)

Actually, I find the reality of mathematical research today - in which progress is obtained naturally and cumulatively as a consequence of hard work, directed by intuition, literature, and a bit of luck - to be far more satisfying than the romantic image that I had as a student of mathematics being advanced primarily by the mystic inspirations of some rare breed of “geniuses”. This “cult of genius” in fact causes a number of problems, since nobody is able to produce these (very rare) inspirations on anything approaching a regular basis, and with reliably consistent correctness. (If someone affects to do so, I advise you to be very sceptical of their claims.) The pressure to try to behave in this impossible manner can cause some to become overly obsessed with “big problems” or “big theories”, others to lose any healthy scepticism in their own work or in their tools, and yet others still to become too discouraged to continue working in mathematics. Also, attributing success to innate talent (which is beyond one’s control) rather than effort, planning, and education (which are within one’s control) can lead to some other problems as well.

Of course, even if one dismisses the notion of genius, it is still the case that some mathematicians are faster, more experienced, more knowledgeable, more efficient, more careful, or more creative than others. This does not imply, though, that only the “best” mathematicians should do mathematics; this is the common error of mistaking absolute advantage for comparative advantage. The number of interesting mathematical research areas and problems to work on is vast - far more than can be covered in detail just by the “best” mathematicians, and sometimes the set of tools or ideas that you have will find something that other good mathematicians have overlooked, especially given that even the very best mathematicians still have weaknesses in some aspects of mathematical research. As long as you have education, interest, and a reasonable amount of talent, there will be some part of mathematics where you can make a solid and useful contribution. It might not be the most glamorous part of mathematics, but actually this tends to be a healthy thing; in many cases the mundane nuts-and-bolts of a subject turn out to actually be more important than any fancy applications. Also, it is necessary to “cut one’s teeth” on the non-glamorous parts of a field before one really has any chance at all to tackle the famous problems in the area; take a look at the early publications of any of today’s great mathematicians to see what I mean by this.

In some cases, an abundance of raw talent may end up (somewhat perversely) to actually be harmful for one’s long-term mathematical development; if solutions to problems come too easily, for instance, one may not put as much energy into working hard, asking dumb questions, or increasing one’s range, and thus may eventually cause one’s skills to stagnate. Also, if one is accustomed to easy success, one may not develop the patience necessary to deal with truly difficult problems. Talent is important, of course; but how one develops and nurtures it is even more so.

It’s also good to remember that professional mathematics is not a sport (in sharp contrast to mathematics competitions). The objective in mathematics is not to obtain the highest ranking, the highest “score”, or the highest number of prizes and awards; instead, it is to increase understanding of mathematics (both for yourself, and for your colleagues and students), and to contribute to its development and applications. For these tasks, mathematics needs all the good people it can get.

Work hard

Every mathematician worthy of the name has experienced … the state of lucid exaltation in which one thought succeeds another as if miraculously… this feeling may last for hours at a time, even for days. Once you have experienced it, you are eager to repeat it but unable to do it at will, unless perhaps by dogged work… (André Weil, “The Apprenticeship of a Mathematician”)

Relying on intelligence alone to pull things off at the last minute may work for a while, but generally speaking at the graduate level or higher it doesn’t. One needs to do a serious amount of reading and writing, and not just thinking, in order to get anywhere serious in mathematics; contrary to public opinion, mathematical breakthroughs are not powered solely (or even primarily) by “Eureka” moments of genius, but are in fact largely a product of hard work, directed of course by experience and intuition. (See also “the cult of genius“.)

The devil is often in the details; if you think you understand a piece of mathematics, you should be able to back that up by having read all the relevant literature and having written down at least a sketch of how that piece of mathematics goes, and then ultimately writing up a complete and detailed treatment of the topic. (See also “learn and relearn your field“.)

It would be very pleasant if one could just dream up the grand ideas and let some “lesser mortals” fill in the details, but, trust me, it doesn’t work like that at all in mathematics; past experience has shown that it is only worth paying one’s time and attention to papers in which a substantial amount of detail and other supporting evidence (or at least a “proof-of-concept”) has already been carefully gathered to support one’s “grand idea”. If the originator of the idea is unwilling to do this, chances are that no-one else will do so either.

In short, there is no royal road to mathematics; to get to the “post-rigorous” stage in which your intuition matches well with what one can establish rigorously, one has to first invest real effort in learning and relearning the field, learning the strengths and weaknesses of tools, learning what else is going on in mathematics, learning how to solve problems rigorously, and answering lots of dumb questions, and so forth. This all requires hard work.

Of course, to work hard, it really helps if you enjoy your work. It is also important to direct your effort in a fruitful direction rather than a fruitless one; in particular, spend some time thinking ahead, and don’t obsess on a single “big problem” or “big theory”.

Learn and relearn your field

Even fairly good students, when they have obtained the solution of the problem and written down neatly the argument, shut their books and look for something else. Doing so, they miss an important and instructive phase of the work. … A good teacher should understand and impress on his students the view that no problem whatever is completely exhausted.
One of the first and foremost duties of the teacher is not to give his students the impression that mathematical problems have little connection with each other, and no connection at all with anything else. We have a natural opportunity to investigate the connections of a problem when looking back at its solution. (George Pólya, “How to Solve It“)

Learning never really stops in this business, even in your chosen specialty; for instance I am still learning surprising things about basic harmonic analysis ten years after writing my thesis in the topic. Just because you know a statement and proof of Fundamental Lemma X, you shouldn’t take that lemma for granted; instead, you should dig deeper until you really understand what the lemma is all about:

• 
  Can you find alternate proofs?
  
• 
  Do you know why each of the hypotheses are necessary?
  
• 
  What kind of generalizations are known/conjectured/heuristic?
  
• 
  Are there weaker and simpler versions which can suffice for some applications?
  
• 
  What are some model examples demonstrating that lemma in action?
  
• 
  When is it a good idea to use the lemma, and when isn’t it?
  
• 
  What kind of problems can it solve, and what kind of problems are beyond its ability to assist with?
  
• 
  Are there analogues of that lemma in other areas of mathematics?
  
• 
  Does the lemma fit into a wider paradigm or program?
  

It is particularly useful to lecture on your field, or write lecture notes or other expository material, even if it is just for your own personal use. You will eventually be able to internalise even very difficult results 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 material.

Don’t be afraid to learn things outside your field

Try to learn something about everything and everything about something. (Thomas Huxley)

Maths phobia is a pervasive problem in the wider community. Unfortunately, it sometimes also exists among professional mathematicians (together with its distant cousin, maths snobbery).

If it turns out that in order to make progress on your problem, you have to learn some external piece of mathematics, this is a good thing – your own mathematical range will increase, you will have acquired some new tools, and your work will become more interesting, both to people in your field and also to people in the external field.

If an area of mathematics has a lot of activity in it, it is usually worth learning why it is so interesting, what kind of problems people try to work on there, and what are the “cool” or surprising insights, phenomena, results that that field has generated. (See also my discussion on what good mathematics is.) That way if you encounter a similar problem, obstruction, or phenomenon in your own work, you know where to turn for the resolution.

One good way to learn things outside your field is by attending talks and conferences outside your field.

Learn the power of other mathematicians’ tools

I suppose it is tempting, if the only tool you have is a hammer, to treat everything as if it were a nail. (Abraham Maslow, “Psychology of Science”)

You will find, when listening to talks or reading papers, that there will be problems which interest you which were solved using an unfamiliar tool, but seem out of reach of your own personal “bag of tricks”. When this happens, you should try to see whether your own tools can in fact accomplish a similar task, but you should also try to work out what made the other tool so effective - for instance, to locate the simplest model case in which that tool does something non-trivial.

Once you have a good comparison of the strengths and weaknesses of the new tool in relation to the old, you will be prepared to recall it whenever a situation comes up in the future in which the tool would be useful; given enough practice, you will then be able to add that tool permanently to your repertoire. Thus it is worth investing some time in learning about other tools, even if they are outside your field.

Ask yourself dumb questions – and answer them!

Don’t just read it; fight it! Ask your own questions, look for your own examples, discover your own proofs. Is the hypothesis necessary? Is the converse true? What happens in the classical special case? What about the degenerate cases? Where does the proof use the hypothesis? (Paul Halmos, “I want to be a mathematician”)

When you learn mathematics, whether in books or in lectures, you generally only see the end product – very polished, clever and elegant presentations of a mathematical topic.

However, the process of discovering new mathematics is much messier, full of the pursuit of directions which were naïve, fruitless or uninteresting.

While it is tempting to just ignore all these “failed” lines of inquiry, actually they turn out to be essential to one’s deeper understanding of a topic, and (via the process of elimination) finally zeroing in on the correct way to proceed.

So one should be unafraid to ask “stupid” questions, challenging conventional wisdom on a subject; the answers to these questions will occasionally lead to a surprising conclusion, but more often will simply tell you why the conventional wisdom is there in the first place, which is well worth knowing.

For instance, given a standard lemma in a subject, you can ask what happens if you delete a hypothesis, or attempt to strengthen the conclusion; if a simple result is usually proven by method X, you can ask whether it can be proven by method Y instead; the new proof may be less elegant than the original, or may not work at all, but in either case it tends to illuminate the relative power of methods X and Y, which can be useful when the time comes to prove less standard lemmas.

It’s also acceptable, when listening to a seminar, to ask “dumb” but constructive questions to help clarify some basic issue in the talk (e.g. whether statement X implied statement Y in the argument, or vice versa; whether a terminology introduced by the speaker is related to a very similar sounding terminology that you already knew about; and so forth). If you don’t ask, you might be lost for the remainder of the talk; and usually speakers appreciate the feedback (it shows that at least one audience member is paying attention!) and the opportunity to explain things better, both to you and to the rest of the audience. However, questions which do not immediately enhance the flow of the talk are probably best left to after the end of the talk.

Attend talks and conferences, even those not directly related to your work

Know how to listen, and you will profit even from those who talk badly. (Plutarch)

Modern mathematics is very much a collaborative activity rather than an individual one. You need to know what’s going on elsewhere in mathematics, and what other mathematicians find interesting; this will often give valuable perspectives on your own work. This is true not just for talks in your immediate field, but also in nearby fields. (For much the same reason, I recommend studying at different places.)  An inspiring talk can also increase your motivation in your own work and in the field of mathematics in general.

You also need to know who’s who, both in your field and in neighboring ones, and to acquaint yourself with your colleagues. This way you will be much better prepared when it does turn out that your work has some new connections to other areas of mathematics, or when it becomes natural to work in collaboration with another mathematician.  Talks and conferences are an excellent way to acquaint yourself with your mathematical community.

(Yes, it is possible to solve a major problem after working in isolation for years – but only after you first talk to other mathematicians and learn all the techniques, intuition, and other context necessary to crack such problems.)

Oh, and don’t expect to understand 100% of any given talk, especially if it is in a field you are not familiar with; as long as you learn something, the effort is not wasted, and the next time you go to a talk in that subject you will understand more. (One can always bring some of your own work to quietly work on once one is no longer getting much out of the talk.)

Think ahead

Worse than being blind, is to see and have no vision. (Helen Keller)

It is really easy to get bogged down in the details of some work and not recall the purpose of what one is actually doing; thus it is good to pause every now and then and recall why one is pursuing a particular goal.

For instance, if one is trying to prove a lemma for one reason or another, take a few moments to ask yourself questions such as

• 
  If the lemma were proven, how would it be used?
  
• 
  What features of the lemma are most important for you?
  
• 
  Would a weaker lemma suffice?
  
• 
  Is there a simpler formulation of the lemma?
  
• 
  Is it worth trying to omit a hypothesis of the lemma, if that hypothesis seems hard to obtain in practice?
  

Often, the exact statement of the lemma is not yet clear before one actually proves it, but you should still be able to get some partial answers to these questions just from knowing the form of the lemma even if the details are not yet complete. These questions can help you reformulate your lemma to its optimal form before sinking too much time into trying to prove it, thus enabling you to use your research time more efficiently.

The same type of principle applies at scales smaller than lemmas (e.g. when trying to prove a small claim, or to perform a lengthy computation) and at scales larger than lemmas (e.g. when trying to prove a theorem, solve a research problem, or pursue a research goal).

Be patient

If I have ever made any valuable discoveries, it has been owing more to patient attention, than to any other talent. (Isaac Newton)

Any given problem generally requires months in order to make satisfactory progress. While it is possible for routine or unexpectedly easy problems to fall within weeks, this is the exception rather than the rule. Thus it is not uncommon for months to pass with no visible progress; however by patiently eliminating fruitless avenues of attack, you are setting things up so that when the breakthrough does come, one can conclude the problem in relatively short order. (But be sceptical of any breakthrough which was “too easy” and somehow failed to address the key difficulty.)

In some cases, you (or the mathematical field in general) are simply not ready to tackle the problem yet; in this case, setting it aside (but not forgetting it entirely), building up some skill on other related problems, and returning back to the original problem in a couple years is often the optimal strategy. This is particularly likely to be the case for any really famous problem.

Incidentally, most problems are solved primarily by this sort of patient, thoughtful attack; there are remarkably few “Eureka!” moments in this business, and don’t be discouraged if they don’t magically appear for you (they certainly don’t for me).

There’s more to mathematics than rigour and proofs

The history of every major galactic civilization tends to pass through three distinct and recognizable phases, those of Survival, Inquiry and Sophistication, otherwise known as the How, Why, and Where phases. For instance, the first phase is characterized by the question ‘How can we eat?’, the second by the question ‘Why do we eat?’ and the third by the question, ‘Where shall we have lunch?’ (Douglas Adams, “The Hitchhiker’s Guide to the Galaxy“)

One can roughly divide mathematical education into three stages:

1. 
   The “pre-rigorous” stage, in which mathematics is taught in an informal, intuitive manner, based on examples, fuzzy notions, and hand-waving. (For instance, calculus is usually first introduced in terms of slopes, areas, rates of change, and so forth.) The emphasis is more on computation than on theory. This stage generally lasts until the early undergraduate years.
   
2. 
   The “rigorous” stage, in which one is now taught that in order to do maths “properly”, one needs to work and think in a much more precise and formal manner (e.g. re-doing calculus by using epsilons and deltas all over the place). The emphasis is now primarily on theory. This stage usually occupies the later undergraduate and early graduate years.
   
3. 
   The “post-rigorous” stage, in which one has grown comfortable with all the rigorous foundations of one’s chosen field, and is now ready to revisit and refine one’s pre-rigorous intuition on the subject, but this time with the intuition solidly buttressed by rigorous theory. (For instance, in this stage one would be able to quickly and accurately perform computations in vector calculus by using analogies with scalar calculus, or informal and semi-rigorous use of infinitesimals, big-O notation, and so forth, and be able to convert all such calculations into a rigorous argument whenever required.) The emphasis is now on applications, intuition, and the “big picture”. This stage usually occupies the late graduate years and beyond.
   

The transition from the first stage to the second is well known to be rather traumatic, with the dreaded “proof-type questions” being the bane of many a math undergraduate. (See also “There’s more to maths than grades and exams and methods“.) But the transition from the second to the third is equally important, and should not be forgotten.

It is of course vitally important that you know how to think rigorously, as this gives you the discipline to avoid many common errors and purge many misconceptions. Unfortunately, this has the unintended consequence that “fuzzier” or “intuitive” thinking (such as heuristic reasoning, judicious extrapolation from examples, or analogies with other contexts such as physics) gets deprecated as “non-rigorous”. All too often, one ends up discarding one’s initial intuition and is only able to process mathematics at a formal level, thus getting stalled at the second stage of one’s mathematical education.

The point of rigour is not to destroy all intuition; instead, it should be used to destroy bad intuition while clarifying and elevating good intuition. It is only with a combination of both rigorous formalism and good intuition that one can tackle complex mathematical problems; one needs the former to correctly deal with the fine details, and the latter to correctly deal with the big picture. Without one or the other, you will spend a lot of time blundering around in the dark (which can be instructive, but is highly inefficient). So once you are fully comfortable with rigorous mathematical thinking, you should revisit your intuitions on the subject and use your new thinking skills to test and refine these intuitions rather than discard them. One way to do this is to ask yourself dumb questions; another is to relearn your field.

The ideal state to reach is when every heuristic argument naturally suggests its rigorous counterpart, and vice versa. Then you will be able to tackle maths problems by using both halves of your brain at once - i.e. the same way you already tackle problems in “real life”.

Learn the limitations of your tools

An education isn’t how much you have committed to memory, or even how much you know. It’s being able to differentiate between what you do know and what you don’t. (Anatole France)

Mathematical education (and research papers) tends to focus, naturally enough, on techniques that work. But it is equally important to know when the tools you have don’t work, so that you don’t waste time on a strategy which is doomed from the start, and instead go hunting for new tools to solve the problem (or hunt for a new problem).

Thus, knowing a library of counterexamples, or easily analysed model situations, is very important, as well as knowing the type of obstructions that your tool can deal with, and which ones it has no hope of resolving. Also it is worth knowing under what circumstances your tool of choice can be substituted by other methods, and what the comparative advantages and disadvantages of each approach is.

If you view one of your favorite tools as some sort of “magic wand” which mysteriously solves problems for you, with no other way for you to obtain or comprehend the solution, this is a sign that you need to understand your tool (and its limitations) much better.

Enjoy your work

No profit grows where is no pleasure ta’en;
In brief, sir, study what you most affect.
(William Shakespeare, “The Taming of the Shrew“)

To really get anywhere in mathematics requires hard work. If you don’t enjoy what you are doing, it will be difficult to put in the sustained amounts of energy required to succeed in the long term. It is much better to work in an area of mathematics which you enjoy, than one which you are working in simply because it is fashionable.

Enthusiasm can be infectious; one reason why you should attend talks and conferences is to find out what other exciting things are happening in your field (or in nearby fields), and to be reminded of the higher goals in your area (or in mathematics in general). A good talk can recharge your own interest in mathematics, and inspire your creativity.

Think ahead

Worse than being blind, is to see and have no vision. (Helen Keller)

It is really easy to get bogged down in the details of some work and not recall the purpose of what one is actually doing; thus it is good to pause every now and then and recall why one is pursuing a particular goal.

For instance, if one is trying to prove a lemma for one reason or another, take a few moments to ask yourself questions such as

• 
  If the lemma were proven, how would it be used?
  
• 
  What features of the lemma are most important for you?
  
• 
  Would a weaker lemma suffice?
  
• 
  Is there a simpler formulation of the lemma?
  
• 
  Is it worth trying to omit a hypothesis of the lemma, if that hypothesis seems hard to obtain in practice?
  

Often, the exact statement of the lemma is not yet clear before one actually proves it, but you should still be able to get some partial answers to these questions just from knowing the form of the lemma even if the details are not yet complete. These questions can help you reformulate your lemma to its optimal form before sinking too much time into trying to prove it, thus enabling you to use your research time more efficiently.

The same type of principle applies at scales smaller than lemmas (e.g. when trying to prove a small claim, or to perform a lengthy computation) and at scales larger than lemmas (e.g. when trying to prove a theorem, solve a research problem, or pursue a research goal).

Don’t prematurely obsess on a single “big problem” or “big theory”

Millions long for immortality who do not know what to do with themselves on a rainy Sunday afternoon. (Susan Ertz, “Anger in the Sky”)

There is a particularly dangerous occupational hazard in this subject: one can become focused, to the exclusion of other mathematical activity, on a single really difficult problem in a field (or on some grand unifying theory) before one is really ready (both in terms of mathematical preparation, and also in terms of one’s career) to devote so much of one’s research time to such a project. This is doubly true if one has not yet learnt the limitations of one’s tools or acquired a healthy scepticism of one’s own work.

When one begins to neglect other tasks (such as writing and publishing one’s “lesser” results), hoping to use the eventual “big payoff” of solving a major problem or establishing a revolutionary new theory to compensate for lack of progress in all other areas of one’s career, then this is a strong warning sign that one should rebalance one’s priorities. While it is true that several major problems have been solved, and several important theories introduced, by precisely such an obsessive approach, this has only worked out well when the mathematician involved

1. 
   had a proven track record of reliably producing significant papers in the area already; and
   
2. 
   had a secure career (e.g. a tenured position).
   

If you do not yet have both (1) and (2), and if your ideas on how to solve a big problem still have a significant speculative component (or if your grand theory does not yet have a definite and striking application), I would strongly advocate a more balanced, patient, and flexible approach instead: one can certainly keep the big problems and theories in mind, and tinker with them occasionally, but spend most of your time on more feasible “low-hanging fruit”, which will build up your experience, mathematical power, and credibility for when you are ready to tackle the more ambitious projects.

Write down what you’ve done

Every composer knows the anguish and despair occasioned by forgetting ideas which one had no time to write down. (Hector Berlioz)

There were many occasions early in my career when I read, heard about, or stumbled upon some neat mathematical trick or argument, and thought I understood it well enough that I didn’t need to write it down; and then, say six months later, when I actually needed to recall that trick, I couldn’t reconstruct it at all. Eventually I resolved to write down (preferably on a computer) a sketch of any interesting argument I came across - not necessarily at a publication level of quality, but detailed enough that I could then safely forget about the details, and readily recover the argument from the sketch whenever the need arises.

I recommend that you do this also, as it serves several useful purposes:

1. 
   It makes the argument permanently available to you in the future, and may eventually be helpful in your later research papers, lecture notes, teaching, or research proposals.
   
2. 
   It gives you practice in mathematical writing, both at the technical level (e.g. in learning how to use TeX) and at an expository or pedagogical level.
   
3. 
   It tests whether you have really understood the argument on more than just a superficial level.
   
4. 
   It frees up mental space; you no longer have to remember the exact details of the argument, and so can devote your memory to learning newer topics.
   

Once you have written up such a sketch, you might consider making it available (e.g. on your web site), even if it does not rise to the level of originality and depth required for a publishable paper.

For somewhat similar reasons, if you have an incomplete (or otherwise unsatisfactory) argument for a problem that you are working on, and you are planning to abandon it, you may still wish to write an informal sketch of it just for yourself (giving barely enough details to allow you to readily reconstruct the whole thing later on), and store it somewhere on your computer, just in case you find you have need for it some time in the future.

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

1. 
   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;
   
2. 
   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
   
3. 
   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.

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“.)

There’s more to mathematics than grades and exams and methods

When you have mastered numbers, you will in fact no longer be reading numbers, any more than you read words when reading books. You will be reading meanings. (W. E. B. Du Bois)

When learning mathematics as an undergraduate student, there is often a heavy emphasis on grade averages, and on exams which often emphasize memorisation of techniques and theory than on actual conceptual understanding, or on either intellectual or intuitive thought. There are good reasons for this; there is a certain amount of theory and technique that must be practiced before one can really get anywhere in mathematics (much as there is a certain amount of drill required before one can play a musical instrument well). It doesn’t matter how much innate mathematical talent and intuition you have; if you are unable to, say, compute a multidimensional integral, manipulate matrix equations, understand abstract definitions, or correctly set up a proof by induction, then it is unlikely that you will be able to work effectively with higher mathematics.

However, as you transition to graduate school you will see that there is a higher level of learning (and more importantly, doing) mathematics, which requires more of your intellectual faculties than merely the ability to memorise and study, or to copy an existing argument or worked example. This often necessitates that one discards (or at least revises) many undergraduate study habits; there is a much greater need for self-motivated study and experimentation to advance your own understanding, than to simply focus on artificial benchmarks such as examinations.

Also, whereas at the undergraduate level and below one is mostly taught highly developed and polished theories of mathematics, which were mostly worked out decades or even centuries ago, at the graduate level you will begin to see the cutting-edge, “live” stuff - and it may be significantly different (and more fun) to what you are used to as an undergraduate! (But you can’t skip the undergraduate step - you have to learn to walk before attempting to fly.)

Talk to your advisor

It is the province of knowledge to speak and it is the privilege of wisdom to listen. (Oliver Wendell Holmes, “The Poet at the Breakfast Table”)

Your advisor is one of the best sources of guidance you have; not only in directly assisting you with your research topic, but in directing you (both explicitly and implicitly) to relevant researchers, conferences, publications, open problems, folklore, or other pieces of good mathematics. Your advisor also knows your situation well and can give career advice which is tailored to your specific strengths and weaknesses (unlike the generic advice in these pages).

If things get to the point that you are actively avoiding your advisor (or vice versa), that is a very bad sign. In particular, you should be aware of your advisor’s schedule, and conversely your advisor should be aware of when you will be available in the department, and what you are currently working on.

For similar reasons, you should give your advisor some advance warning if you want to take a long period of time away from your studies.

If your advisor is unavailable, you should regularly discuss mathematical issues with at least one other mathematician instead, preferably an experienced one.  [Also, it is not uncommon for a student to have both a formal advisor, who handles all the official paperwork, and an informal advisor, with which you discuss research and career issues.]

Of course, you should not rely purely on your advisor; you also need to take the initiative when it comes to your mathematical career.

Take the initiative

The best teacher is the one who suggests rather than dogmatizes, and inspires his listener with the wish to teach himself. (Edward Bulwer-Lytton)

While you should talk to your advisor, you should not be completely reliant on him or her; after all, you are going to have to do mathematics primarily on your own once you graduate!

If you feel like you want to learn something, do something, or write something, you don’t have to clear it with your advisor - just go ahead and do it (though in some cases other priorities, such as writing your thesis, may be temporarily more important, and you should of course keep your advisor updated as to what you’re doing mathematically). Research your library or the internet, talk with other graduate students or faculty, read papers and books on your own (both in your field and in nearby fields), attend conferences, and so forth. (See also “ask yourself dumb questions”.)

One specific suggestion I have is to subscribe (either by RSS, or by email) to be notified of new papers which appear on the arXiv in the subject areas that you are interested in.

In a somewhat related spirit, while it is certainly acceptable to have mathematical role models, one should not try to mimic them too slavishly; you need to develop your own personal style, exploiting your own strengths and weaknesses, which will not be identical to those of your role models.  Ultimately, it is better to follow the mathematics than to follow a mathematician.