闻笛赋的BLOG

1 There’s more to mathematics than grades and exams and methods. As an undergraduate, there is 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.  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!

2 There’s more to mathematics than rigour and proofs. As an undergraduate one is often first taught mathematics in an informal, intuitive manner (e.g. describing derivatives and integrals in terms of slopes and areas), but then told a little later that to do things “properly” one needs to work and think in a much more precise and formal manner (e.g. using epsilons and deltas to describe derivatives).  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.  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.  The ideal state to reach is when every heuristic argument naturally suggests its rigorous counterpart, and vice versa.

3 Work hard.  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.  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.

4 Enjoy your work.  This is in some ways a corollary to the previous; 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 (see below).

5 Don’t base career decisions on glamour or fame.  Going into a field or department simply because it is glamorous is not a good idea, nor is focusing on the most famous problems (or mathematicians) within a field, solely because they are famous – honestly, there isn’t that much fame or glamour in mathematics overall, and it is not worth chasing these things as your primary goal.  Anything glamorous is likely to be highly competitive, and only those with the most solid of backgrounds (in particular, lots of experience with less glamorous aspects of the field) are likely to get anywhere.  A famous unsolved problem is almost never solved ab nihilo.  One has to first spend much time working on simpler (and much less famous) model problems, acquiring techniques, intuition, partial results, context, and literature, thus enabling fruitful approaches to the problem and ruling out fruitless ones, before having any real chance of solving any really big problem in the area.  (Occasionally, one of these problems falls relatively easily, simply because the right group of people with the right set of tools hadn’t had a chance to look at the problem before, but this is usually not the case for the very intensively studied problems – particularly those which already have a substantial body of “no go” theorems and counterexamples which rule out entire strategies of attack.)  For similar reasons, one should never make prizes or recognition a primary reason for pursuing mathematics; it is a better strategy in the long-term to just produce good mathematics and contribute to your field, and the prizes and recognition will eventually take care of themselves (and be well-earned).

6 Learn and relearn your field.  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 – 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 to 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 internalize even very difficult results using efficient mental shorthand which not only allows you to use them effortlessly, but also frees up mental space to learn even more material.  (See also "ask yourself dumb questions".)

7 Don’t be afraid to learn things outside your field.  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, 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.

8 Learn the limitations of your tools.  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.

9 Learn the power of other mathematician's tools.  This is a corollary of the previous.  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 repetoire.

10 Ask yourself dumb questions – and answer them! 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 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.

11 Be sceptical of your own work.  If you unexpectedly find a problem solving itself almost effortlessly, and you can’t quite see why, you should try to analyse your solution more sceptically.  In particular, the method may also be able to prove much stronger statements which are known to be false, which would imply that there is a flaw in the method.  In a related spirit, if you are trying to prove some ambitious claim, you might try to first look for a counterexample; either you find one, which saves you a lot of time and may well be publishable in its own right, or else you encounter some obstruction, which should give some clue as to what one has to do in order to establish the claim positively (in particular, it can “identify the enemy” that has to be neutralised in order to conclude the proof).  Actually, it’s not a bad idea to apply this type of scepticism to other mathematician’s claims also; if nothing else, they can give you a sense of why that claim is true and how powerful it is.

12 Think ahead.  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, ask yourself – 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).

13 Attend talks and conferences, even those not directly related to your work.  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.  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.  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.)  See also Tom Korner's "How to listen to a maths lecture".

14 Study at different places.  It is a very good idea to do your graduate study at a different institution as your undergraduate study, and to take a postdoctoral position at a different place from where you did your graduate study.  Even the best mathematics departments do not have strengths in every field, so being at several mathematics departments will broaden your education and expose you to a variety of mathematical cultures.  Furthermore, the act of moving will help you make the (substantial) psychological transition from an undergraduate student to a graduate student, or from a graduate student to a postdoctoral researcher.

15 Talk to your advisor.  This is self-evident – your advisor knows your situation well and is the best source of guidance you have.  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; in particular, 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.