Every so often, I receive a query asking for advice on mathematical career issues, such as

- What fields in mathematics should one study?
- What mathematical texts should one buy or read?
- What problems should one try to solve?
- How should one approach mathematical problems?
- How should one write mathematical papers?
- What universities should one apply to?
- What strategies should one pursue to increase one’s chances of admission (e.g. to UCLA)?
- More generally, how should one “succeed” in
mathematics?

These requests for advice are of course very flattering. Unfortunately, these questions are too general, and too dependent on one’s specific circumstances, interests, options, and context for me to offer anything other than generic platitudes (see below). Because of this, and because of lack of available time, I am regretfully unable to meaningfully respond to any such queries. I would recommend instead consulting with one’s high school, undergraduate or graduate advisor, who is more attuned to your specific situation and will be able to offer more relevant advice. In particular, I am unable to personally advise anyone other than UCLA graduate students who have already passed their qualifying exams.

**Regarding mathematics
competitions**:
I have not participated in mathematics competitions since 1988, and am
not
familiar with how they work nowadays.
For advice on how to solve mathematical problems, you can try my
book on the subject. Also, I should
say that while mathematics competitions are certainly a lot of fun,
they are
very different activities from mathematical learning or mathematical
research;
don’t expect the problems you get in, say, graduate study, to have the
same cut-and-dried, neat flavour that an Olympiad problem does. (While individual steps in the solution might
be able to be finished off quickly by someone with Olympiad training,
the
majority of the solution is likely to require instead the much more
patient and
lengthy process of reading the literature, applying known techniques,
trying
model problems or special cases, looking for counterexamples, and so
forth.) So enjoy these competitions, but
don’t neglect the more “boring” aspects of your mathematical
education, as those turn out to be ultimately more useful.

As I said above, I have no “secret formula”
or other
one-size-fits-all prescription for how to succeed in mathematical
research and
academia. There are, however, very
generic (and fairly obvious) pieces of advice I can give:

**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!

**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.**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.

**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).**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).**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".)

**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.**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.- 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.

**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 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.**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.**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).**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".

**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.**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.**Take the initiative.**On the other hand, you shouldn’t rely purely on your advisor; if you feel like you want to learn something, do something, or write something, just go ahead and do it (though in some cases other priorities, such as writing your thesis, may be temporarily more important). Research your library or the internet, talk with other graduate students or faculty, read papers and books on your own, and so forth. (See also “ask yourself dumb questions”.)**Be patient.**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. 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. 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).

**Be flexible.**Mathematical research is by its nature unpredictable – if we knew in advance what the answer would be and how to do it, it wouldn’t be research! Thus you will be led in unexpected directions, and it may end up that you may find a new problem or area of mathematics more interesting than the one you were initially working in. Thus, while it is certainly worthwhile to have long-term goals, they should not be set in stone, and should be updated when new developments occur. One corollary to this is that one should not base a career decision (such as what university to study at or work in) purely based on a single faculty member, since it may turn out that this faculty member may move, or that your interests change, while you are there. Another corollary is that it is generally not a good idea to announce that you are working on a well-known problem before you have a feasible plan for solving it, as this can make it harder to gracefully abandon the problem and refocus your attention in more productive directions in the event that the problem is more difficult than anticipated. This is also important in grant proposals; saying things like "I would like to solve <Famous Problem X>" or "I want to develop or use <Famous Theory Y>" does not impress grant reviewers unless there is a coherent plan (e.g. some easier unsolved problems to use as milestones) as well as a proven track record of progress.

**Be professional in your work.**Take your duties and responsibilities seriously; being frivolous is fine with friends, but can be annoying for your colleagues, especially those who are busy with similar responsibilities. One’s writing should also be taken seriously; your work is going to appear in permanently available journals, and what may seem witty or clever today may be incredibly embarrassing for you a decade from now. Being assertive is fine, but being overly self-promoting or competitive is generally counterproductive; if your work is good, it should speak for itself, and it is better to spend your energies on creating new mathematics than trying to fight over your old mathematics. Try not to take any research setbacks (such as a rejection of a paper, or discovery of an error) personally; there are usually constructive resolutions to these issues that will ensure that you become a better mathematician and avoid these problems in the future. Be generous with assigning credit, acknowledgements and precedence in your own writing (but make sure it is assigned correctly!). The tone of the writing should be neutral and professional; personal opinions (e.g. as to the importance of a subject, a paper, or an author) should be rarely voiced, and clearly marked as opinion when they are. On your web page, keep the personal separated from the professional; your colleagues are visiting your web page to get your papers, preprints, contact info, and curriculum vitae, and are probably not interested in your hobbies or opinions. (Conversely, your friends are probably not interested in your research papers.)**Be considerate of your audience.**This applies primarily to papers, but also to lectures and seminars. On the one hand, the most important thing in mathematics is to get results, and prove them correctly. However, one also needs to make a good faith effort to communicate these results to their intended audience. Good exposition is hard work – almost as hard as good research, sometimes – and one may feel that having proved the result, one has no further obligation to explain it. However, this type of attitude tends to needlessly infuriate the very people who would otherwise be the strongest supporters and developers of your work, and is ultimately counter-productive. Thus, one should devote serious thought (and effort) to issues such as logical layout of a paper, choice and placement of notation, and the addition of heuristic, informal, motivational or overview material in the introduction and in other sections of a paper. Ideally, at every point in the paper, the reader should know what the immediate goal is, what the long-term goal is, where various key statements or steps will be justified, why the notation, lemmas, and other material just introduced will be relevant to these goals, and have a reasonable idea of the context in which these arguments are placed in. (In short, a good paper should tell the reader “Why” and “Where” and not just “How” and “What”.) In practice one tends to fall far short of such ideals, but there are often still ways one can make one’s papers more accessible without compromising the results. It sometimes helps to sit on a paper for a while, until the details have faded somewhat from your memory, and then reread it with a fresher perspective (and one closer to that of your typical audience); this can often highlight some significant issues with the exposition which can then be easily addressed. See also my advice on writing and submitting papers.- Don't
prematurely obsess on a single "big problem" or "big theory".
This is a
particularly dangerous occupational hazard in this subject - that one
becomes 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
career) to devote so much of one's research time to such a
project. 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 make up 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
(a) has a proven track record of reliably producing significant papers
in the area already, and (b) has a secure career (e.g. a tenured
position). If you do not yet have both (a) and (b), 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 approach instead: 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.

**Talks are not the same as papers.**It is difficult to give good talks, especially when one is just starting out one’s career. One should avoid the common error of treating a talk like a paper, with all the attendant details, technicalities, and formalism. (In particular, one should**never**give a talk which consists solely of transparencies of one’s research paper!) Such talks are almost impossible for anyone not intimately familiar with your work to be able to follow, especially since (unlike when reading a paper) it is difficult for an audience member to refer back to notation that had been defined, or comments that had been made, four slides or five blackboards ago. Instead, a talk should*complement*a paper by providing a high-level and more informal overview of the same material, especially for the more standard or routine components of the argument; this allows one to channel more of the audience’s attention onto the most interesting or important components, which can be described in more detail. A good talk should also be “friendly” to non-experts by devoting at least the first few minutes going over basic examples or background, so that they are not completely lost even from the beginning. Actually, even the experts will appreciate a review of the background material; even if none of this material is new, sometimes you will have a new perspective on the old material which is of interest. Also, if you organize your presentation of background material correctly, your treatment of the new material should flow more naturally and be more readily appreciated by the audience. One particularly effective method is to present a proof of New Theorem Y by first reviewing a proof of Standard Theorem X in the style of the proof of Y, and then later in the lecture, when the time comes to prove Y, just note that one simply repeats all the steps used to prove X with only a few key changes, which one then highlights. (Of course, it would be a good idea to keep the proof of X on the blackboard or on screen during all of this, if possible.) This often works better, and can even be a little bit faster, than if one skipped the proof of X “to save time” and started directly on the proof of Y.**Use the wastebasket.**Not every idea leads to a success, and not every first draft forms a good template for the final draft. This is true even for the very best mathematicians. There are times when a project just isn’t working the way it was initially planned, and you have to scale it down, refocus it, or shelve it altogether; or a lemma that you spent a lot of time on turns out not to add anything much to the paper and has to be reluctantly jettisoned or deferred to another paper; or that the structure of a half-written paper is clearly not optimal and that one needs to rewrite the entire thing from scratch. (Indeed, some of the papers I am most proud of are virtually unrecognizable from their first draft, due to one or more complete rewrites.) One has to know when one should be persistent and patient, and when one should be pragmatic and realistic; stubbornly working away at a dead end is not the most efficient use of your time, and publishing every last scrap of your work is not always the best way to meet the standards of quality you expect from your publications. Of course, in today’s digital age it is cheap and easy to backup all your work, and you should of course do this*before*performing major surgery on any paper. Even an embarrassingly wrong piece of work (and I have a number of these, which fortunately have never made it as far as publication) should be stored somewhere, because you never know whether something salvageable can be extracted from it, and also it is good to make a note of mistakes that one should avoid in the future.- Write
down what you've done. 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 beyond the
obvious one of having the argument permanently available to you in the
future. Firstly, 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. Secondly, it tests whether you
have really understood the argument on more than just a superficial
level. Thirdly, 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. Finally, your writeup may also
eventually
be helpful in your later research papers, lecture notes, or a
research proposals.

**Make your work available.**With the advent of the internet and world-wide web, and in particular with preprint servers such as the arXiv, there is really no excuse not to make your preprints available online, so that anyone who is interested in your work can easily find it. (Most journals now also have online availability, but given that the gap between preprint release and publication is measured in years, it still makes sense to have the preprint online too.) In particular, your work will show up in search engine queries in your topic (I have come across many an interesting paper this way). This will help spread awareness of you and your work among your colleagues, and hopefully lead to future collaborations, or other people building upon (and citing) your papers. One might be worried that by making your work available, you are inviting too much “competition” into your area, but if the area you work in is of that much interest to others, the competition will come anyway, and this way you will at least have priority (note that submissions to servers such as the arXiv have reliable timestamps) and be acknowledged in citations. Of course, one should still ensure that your preprints are written to publication-quality standard if at all possible, although this is not as important as it is with published papers since it is relatively easy to replace preprints with updated versions. As to whether you should email your preprints to other experts in the field, I would only do this if the preprint is unquestionably of direct interest to that person (e.g. it solves a conjecture that they formulated). Otherwise there is the awkward possibility that the person you send the preprint to is too busy (or no longer interested in the topic) to read your work in detail, or that you might accidentally be perceived as being pushy, egotistic, or arrogant. In most cases it suffices to just make your work on-line; awareness of your work will spread by itself via several channels (e.g. the refereeing process, conferences, word-of-mouth, preprint mailing lists) and there is usually little additional gain in trying to actively push the paper.

- John Baez’s page on career advice.
- Po Bronson's article on the relative importance of
innate intelligence versus effort.

- Alain Connes’s “Advice to the beginner”.
- Lance Fortnow's "Graduate
Student Guide".

- Oded Goldreich's "On our
duties as scientists".

- Gian-Carlo Rota’s “Ten lessons I wish I had been taught”.
- Ian Stewart's "Letters to a Young Mathematician".
- AMS advice page for new PhDs