

陶哲轩（Terence Tao）博文选集
Selected Articles from Terence
Tao's Blog


Part 1 Career Advice  Part
2 On Writing  Part
3 Miscellaneous
I Advice on gifted education
If you can give your son or daughter only one gift, let it be enthusiasm. (Bruce Barton)
Education is a complex, multifaceted, and painstaking process, and being gifted does not make this less so. I would caution against any single “silver bullet” to educating a gifted child, whether it be a special school, private tutoring, home schooling, grade acceleration, or anything else; these are all options with advantages and disadvantages, and need to be weighed against the various requirements and preferences (both academic and nonacademic) of the child, the parents, and the school. Since this varies so much from child to child, I cannot give any specific advice on a given child’s situation. [In particular, due to many existing time commitments and high volume of requests, I am unable to personally respond to any queries regarding gifted education.]
I can give a few general pieces of advice, though. Firstly, one should not focus overly much on a specific artificial benchmark, such as obtaining degree X from prestigious institution Y in only Z years, or on scoring A on test B at age C. In the long term, these feats will not be the most important or decisive moments in the child’s career; also, any shortterm advantage one might gain in working excessively towards such benchmarks may be outweighed by the time and energy that such a goal takes away from other aspects of a child’s social, emotional, academic, physical, or intellectual development. Of course, one should still work hard, and
participate in competitions if one wishes; but competitions and academic achievements should not be viewed as ends in themselves, but rather a way to develop one’s talents, experience, knowledge, and enjoyment of the subject.
Secondly, I feel that it is important to enjoy one’s work; this is what sustains and drives a person throughout the duration of his or her career, and holds burnout at bay. It would be a tragedy if a wellmeaning parent, by pushing too hard (or too little) for the development of their child’s gifts in a subject, ended up accidentally extinguishing the child’s love for that subject. The pace of the child’s education should be driven more by the eagerness of the child than the eagerness of the parent.
Thirdly, one should praise one’s children for their efforts and achievements (which they can control), and not for their innate talents (which they cannot). This article by Po Bronson describes this point excellently. See also the Scientific American article “The secret to raising smart kids” for a similar viewpoint.
Finally, one should be flexible in one’s goals. A child may be
initially gifted in field X, but decides that field Y is more enjoyable or is a better
fit. This may be a better choice, even if Y is “less prestigious”
than X; sometimes it is better to work in a less well known field
that one feels competent and comfortable in, than in a “hot” but
competitive field that one feels unsuitable for. (See also Ricardo’s law of comparative advantage.)
My own education is discussed in the following articles. While I am very happy with the way things turned out for me, I would again caution that each child’s situation, strengths, and weaknesses are different, and that my experience might not necessarily be the ideal template to follow for others.
■ “Terence Tao”vii, Ken Clements, Educational Studies in Mathematics, August 1984, Vol. 15, No. 3, 213238
■ “Parental involvement in Gifted Education”, Billy Tao, Educational Studies in Mathematics, August 1986, Vol. 17, No. 3, 313321
■ “Radical Acceleration in Australia: Terence Tao”, Miraca Gross, G/C/T, July/August 1986
■ “Insights from SMPY’s greatest former child prodigies: Drs. Terence (“Terry”) Tao and Lenhard (“Lenny”) Ng reflect on their talent development”, Michelle Muratori, Julian Stanley, Lenhard Ng, Jack Ng, Miraca Gross, Terence Tao, Billy Tao, Gifted Child Quarterly, Fall 2006, Vol. 50, No. 4, 307324
For professional advice on gifted education, I can recommend the Center for Talented Youth. See also my page on career advice.

II Advice on mathematics competitions
Sports serve society by providing vivid examples of excellence. (George Will)
I greatly enjoyed my experiences with high school mathematics competitions (all the way back in the 1980s!). Like any other school sporting event, there is a certain level of excitement in participating with peers with similar interests and talents in a competitive activity. At the
Olympiad levels, there is also the opportunity to travel nationally and internationally, which is an experience I strongly recommend for all highschool students.
Mathematics competitions also demonstrate that mathematics is not just about grades and exams. But mathematical competitions 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 cutanddried, neat
flavor 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.) Also, the “classical” type of mathematics you learn while doing Olympiad problems (e.g. Euclidean geometry, elementary number theory, etc.) can seem dramatically different from the “modern” mathematics you learn in undergraduate and graduate school, though if you dig a little deeper you will see that the classical is still hidden within the foundation of the modern. For instance, classical theorems in Euclidean geometry provide excellent examples to inform modern algebraic or differential geometry, while classical number theory similarly informs modern algebra and number theory, and so forth. So be prepared for a significant
change in mathematical perspective when one studies the modern
aspects of the subject. (One exception to this is perhaps the field of combinatorics, which still has large areas which closely resemble its classical roots, though this is changing also.) In summary: enjoy these competitions, but don’t neglect the more “boring” aspects of your mathematical education, as those turn out to be ultimately more useful. For advice on how to solve mathematical problems, you can try my book on the subject.

III 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 naive,
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. See also “Learn the limitations of your
tools” and “Be sceptical of your own work”.

IV 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.)
See also Tom Korner’s “How to listen to a maths lecture”.

V Batch lowintensity tasks together
It is much easier to try one’s hand at many things than to concentrate one’s powers on one thing. (Quintilian)
The tasks one is faced with in work can be broadly divided into
two categories:
1. “highintensity” tasks, which are complex and require your
full concentration and focus (e.g. writing a research paper;
preparing for a class or talk; writing a lengthy, detailed, and
careful email; thinking about a mathematical problem; reading a
research paper or text), and
2. “lowintensity” tasks, which are routine (but can be
timeconsuming) and do not require much mental energy (e.g. filling out paperwork; teaching a class or giving a talk that you have already prepared; writing a short email response; errands and appointments; reading email or browsing the web).
Working with highintensity requires a rather different “mode” of
thought than with lowintensity tasks. (For instance, I find it can take a good halfhour or so of uninterrupted thinking before I am fully focused on a maths
problem, with all the relevant background at my fingertips.) To
reduce the mental fatigue of transitioning from one “mode” to
another, I find it useful to batch similar lowintensity tasks together, and to separate them in time (or space) from the highintensity ones. For example, you can devote a block of time to clearing a lot of “trivial” tasks off of your plate. Schedule all the “distracting” tasks (e.g. office hours and other appointments) in a single day; try to bunch up teaching days; etc. (I found, for instance, that teaching two sections of a large calculus class back to back (e.g. at 9am and then at 10am) led to significant time savings in class preparation (as well as savings in mental energy), when compared to teaching two different classes, or the same class at very different times.)
One can also do this blocking off in space as well as in time. For instance, with regards to keeping track of paperwork, I have one small area of my office for “important” forms and records that I am likely to need to deal with again in the future, and a larger area in another part of my office for “mundane” paperwork which have a low (but nonzero) probability of being needed again in the future. I don’t organise or
file the latter set of papers very much, given how rarely I need to
retrieve files from it; it tends to accumulate in a pile, which I sort through (and mostly discard) every few months or so. (But I do make an effort to keep the “important” forms relatively organized, and to not have them be cluttered by the much larger set of “mundane” forms.)
In a somewhat analogous fashion, one can have an “out” tray for lowpriority physical mail, and send them all out at once, rather than making multiple trips to the office mail room in one day. (While doing so, of course, that would be a good time to check one’s mailbox, or any other task that requires walking around the department.)
With regards to email, an assembly line approach seems to be efficient: wait until it builds up, and then (a) pass through deleting spam, (b) pass through again dealing with easily dealt with emails (ones that need to be read once and discarded or
filed, or require a very brief response, or pushed into some sort of “pending”
folder; and then (c) deal with one or more of the emails that demand a longer response, if you feel that this is an appropriate time to do so.
If you like to browse multiple web sites during the course of the day, I recommend using a feed aggregator (I myself use Google Reader) so that you can do all your browsing at once, so that they do not distract you from your other tasks.
If one has a batch of tasks that are both lowintensity and lowpriority, then it is probably a good idea to set it aside until one really needs a break from more highintensity
work; for instance, if I get too frustrated on an obstacle in my
research, I find this to be a good time to go do some accumulated errands or paperwork, or even just to catch up on my email and web browsing. Having some easy tasks of this nature lying around is then handy for killing time in a reasonably productive fashion until one’s creative energies return.
Note that batching only works well for lowintensity tasks. A highintensity task requires so much focus, and exhausts so much of one’s mental stamina, that it can be counterproductive or distracting to mix this activity with other low or high intensity tasks.

VI Be considerate of your audience
Think like a wise man, but communicate in the language of the people. (William Butler Yeats)
This advice applies primarily to papers, but also to lectures and seminars (though one should also bear in mind that talks are not the same as papers).
On the one hand, one of the most important things in mathematics (though certainly not the only thing) 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. (It may feel like you have attained some level of intellectual achievement if you can discuss a topic which is so difficult or jargonheavy that most of your audience do not understand what you are talking about, but it is in fact a far greater intellectual achievement if you can actually communicate that difficult topic effectively to such an 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 counterproductive. 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 longterm 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 (e.g. use of some specialized jargon, without ever defining the term or citing a reference for it) which can then be easily addressed.
See also my advice on writing and submitting papers.

VII Be flexible
It is not the strongest of the species that survives, nor the most intelligent, but the one most responsive to change. (Charles
Darwin)
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! You should therefore be prepared for research
to lead you 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. (See also “Don’t be afraid to
learn things outside your field” and “Learn the power of other mathematician’s tools”.)
Thus, while it is certainly worthwhile to have longterm 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. (See also “Don’t base career decisions on glamor or fame”.)
Another corollary is that it is generally not a good idea to announce that you are working on a wellknown 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. (See also “Don’t prematurely obsess on a single big problem or big theory”.)
This is also important in grant proposals; saying things like “I would like to solve ” or “I want to develop or use ” 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.

VIII 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 of effort 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 mysteriously 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). See also “work hard” and
“be flexible”.

X Be professional in your work
Integrity without knowledge is weak and useless, and knowledge without integrity is dangerous and dreadful. (Samuel Johnson, “Rasselas”)
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 selfpromoting 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. In short, you should write professionally. (See also my advice on writing papers.)
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.)

XI Be sceptical of your own work
An expert is a man who has made all the mistakes, which can be
made, in a very narrow field. (Niels Bohr)
If you unexpectedly find a problem solving itself almost
effortlessly, and you can’t quite see why, you should try to analyze
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 neutralized 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.
A sceptical attitude towards your own work should be especially
enforced when dealing with a problem which is known to be difficult
(and this includes most “famous problems”), or one which is outside
your usual area of expertise. In particular, if your solution to
that problem resembled this process:
1. Transform the difficult problem to another difficult problem.
2. Transform the problem again to yet another difficult problem.
3. . . .
4. Transform the problem again to yet another difficult problem.
5. Transform the problem again. Suddenly the problem becomes much
simpler!
6. Transform the simple problem to another simple problem.
7. . . .
8. Transform the simple problem again to another simple problem.
9. Solve the last simple problem. Done!
then there is almost certainly a major error in your argument in
Step 5. (This is especially true if the difficulty of the
transformed problem had been steadily increasing through steps 14.)
At a bare minimum, this suspicious step should be thoroughly checked
and rechecked, any handwaving arguments near this step should be
written out in full, and some analysis should be undertaken as to
understanding what exactly was the decisive step in the argument
that dramatically simplified the problem, and how that step could be
so powerful as to achieve such a simplification.
Here is another common type of suspicious argument:
1. To prove Famous Conjecture X, use reductio ad absurdum, and
assume for sake of contradiction that X is false.
2. Do some random computations of tangential relevance to X.
3. Do some more random computations of this type.
4. . . .
5. Do another random computation, but this time unwittingly make
a sign error, division by zero, or similar mistake.
6. Do yet more random computations.
7. . . .
8. Notice that two of your computations are inconsistent with
each other.
9. Congratulations  you’ve obtained the desired contradiction.
Declare victory!
A good way to stresstest this sort of false argument is to try
to run the same argument without the initial assumption that X is
false. If one can easily modify the argument to again lead to a
contradiction, it shows the problem wasn’t with X  it was with the
argument. A classic example here would be a “proof” that the
existence of nontrivial natural number solutions to the equation a^{n}
+ b^{n} = c^{n} leads to a contradiction, which
mysteriously fails to use in any significant way the hypothesis that
n > 2 and would in fact would also work (perhaps after some small
modification) for n = 2 also.
Another warning sign is if the computations lead you further and
further away from the mathematical topics and connections that X is
supposed to be addressing (e.g. a proposed proof of the Riemann
hypothesis that proceeds almost entirely using the theory of
meromorphic functions, with almost no reference to integers, primes,
or other basic numbertheoretic concepts; or, conversely, an
argument that proceeds entirely by working with the integers, with
barely any reference to the zeta function).
For comparison, actual solutions to a major problem tend to be
arrived at by a process more like the following (often involving
several mathematicians over a period of years or decades, with many
of the intermediate steps described here being significant
publishable papers in their own right):
1. Isolate a toy model case x of major problem X.
2. Solve model case x using method A.
3. Try using method A to solve the full problem X.
4. This does not succeed, but method A can be extended to handle
a few more model cases of X, such as x’ and x”.
5. Eventually, it is realized that method A relies crucially on a
property P being true; this property is known for x, x’, and x”,
thus explaining the current progress so far.
6. Conjecture that P is true for all instances of problem X.
7. Discover a family of counterexamples y, y’, y”, . . . to this
conjecture. This shows that either method A has to be adapted to
avoid reliance on P, or that a new method is needed.
8. Take the simplest counterexample y in this family, and try to
prove X for this special case. Meanwhile, try to see whether method
A can work in the absence of P.
9. Discover several counterexamples in which method A fails, in
which the cause of failure can be definitively traced back to P.
Abandon efforts to modify method A.
10. Realize that special case y is related to (or at least
analogous to) a problem z in another field of mathematics. Look up
the literature on z, and ask experts in that field for the latest
perspectives on that problem.
11. Learn that z has been successfully attacked in that field by
use of method B. Attempt to adapt method B to solve y.
12. After much effort, an adapted method B’ is developed to solve
y.
13. Repeat the above steps 112 with A replaced by B’ (the
outcome will of course probably be a little different from the
sample storyline presented above). Continue doing this for a few
years, until all model special cases can be solved by one method or
another.
14. Eventually, one possesses an array of methods that can give
partial results on X, each of having their strengths and weaknesses.
Considerable intuition is gained as to the circumstances in which a
given method is likely to yield something nontrivial or not.
15. Begin combining the methods together, simplifying the
execution of these methods, locating new model problems, and/or
finding a unified and clarifying framework in which many previous
methods, insights, results, etc. become special cases.
16. Eventually, one realizes that there is a family of methods A?
(of which A was the first to be discovered) which, roughly speaking,
can handle all cases in which property P ? (a modern generalization
of property P) occurs. There is also a rather different family of
methods B ? which can handle all cases in which Q? occurs.
17. From all the prior work on this problem, all known model
examples are known to obey either P ? or Q? . Formulate Conjecture
C: all cases of problem X obey either P ? or Q? .
18. Verify that Conjecture C in fact implies the problem. This is
a major reduction!
19. Repeat steps 118, but with problem X replaced by Conjecture
C. (Again, the storyline may be different from that presented
above.) This procedure itself may iterate a few times.
20. Finally, the problem has been boiled down to its most
purified essence: a key conjecture K which (morally, at least)
provides the decisive input into the known methods A? , B ? , etc.
which will settle conjecture C and hence problem X.
21. A breakthrough: a new method Z is introduced to solve an
important special case of K.
22. The endgame: method Z is rapidly developed and extended,
using the full power of all the intuition, experience, and past
results, to fully settle K, then C, and then at last X.
23. The technology developed to solve major problem X is adapted
to solve other related problems in the field. But now a natural
successor question X’ to X arises, which lies just outside of the
reach of the newly developed tools and we go back to Step 1.
See also “Learn the limitations of your tools”, “Ask yourself
dumb questions”, “Think ahead”, and “Use the wastebasket”.

XII 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 shortterm value to
one’s career in writing publishable papers, there is a longterm
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
longterm 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 highprofile 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 highprofile 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
o?” 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 generalizing 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 shortterm goal of publishing a paper, but about the
longterm goal of expanding your range. This is somewhat analogous
to exploiting the power of compound interest in longterm 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”.)

XIII 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 hardwon 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 nontrivial, 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 at any given point in time, 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 greatest 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 nutsandbolts 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 nonglamorous 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 longterm 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.

XIV 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 Ertzix, “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 (and in extreme cases, on nonmathematical activity also), 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 “lowhanging fruit”, which will build up your experience, mathematical power, and credibility for when you are ready to tackle the more ambitious projects.
See also “Don’t base career decisions on glamor or fame” and “Use the wastebasket”.
 Addendum: on publishing proofs of famous open problems
If you do believe that you have managed to solve a major problem, I would advise you to be extraordinarily sceptical of your own work,
and to exercise the utmost care and caution before releasing it to
anyone; there have been too many examples in the past of
mathematicians whose reputation has been damaged by claiming a proof
of a wellknown result to much fanfare, only to find serious errors in the proof shortly thereafter. I recommend asking yourself the following questions regarding the paper:
1. What is the key new idea or insight? How does it differ from what has been tried before? Is this idea emphasized in the introduction to the paper?
(As a colleague of mine is fond of saying: “Where’s the beef?”.)
2.
How does the arguments in this paper relate to earlier partial
results or attempts on the problem? Are there clear analogues
between the steps here and steps in earlier papers? Does the new
work shed some light as to why previous approaches did not fully
succeed? Is this discussed in the paper?
3. What is the simplest,
shortest, or clearest new application of that idea? A related
question: what is the first nontrivial new statement made in the paper, that was not able to have been shown before by earlier methods? Is this proofofconcept given in the paper, or does it jump straight to the big conjecture with all its additional (and potentially errorprone) complications? In the event that there is a fatal error in the full proof, is there a good chance that a deep and nontrivial new partial result can at least be salvaged?
4. Any major problem comes with known counterexamples, obstructions, or philosophical objections to various classes of attack strategies (e.g. strategy X does not work because it does not distinguish between problem Y, which is the big conjecture, and problem Z, for which counterexamples are known). Do you know why your argument does not encounter these obstructions? Is this stated in the paper? Do you know any specific limitations of the argument? Are these stated in the paper also?
5. What was the highlevel strategy you employed to attack the problem? Was it guided by some heuristic, philosophy, or intuition? If so, what is it? Is it stated in the paper? If the strategy was “continue blindly transforming the problem repeatedly until a miracle occurs”, this is a particularly bad sign. Can you state, in highlevel terms (i.e. rising above all the technical details and computations), why the argument works?
6. Does the proof come with key milestones  such as a key proposition used in the proof which is already of independent interest, or a major reduction of the unsolved problem to one which looks significantly easier? Are these milestones clearly identified in the paper?
7. How robust is the argument  could a single sign error or illegal use of a lemma or formula destroy the entire argument? Good indicators of robustness include: alternate proofs (or heuristics, or supporting examples) of key steps, or analogies between key parts of the argument in this paper and in other papers in the literature.
8. How critically have you checked the paper and reworked the exposition? Have you tried to deliberately disprove or hunt for errors in the paper? One expects a certain amount of checking to have been done when a major paper is released; if this is not done, and errors are quickly found after the paper is made public, this can potentially be quite embarrassing. Note that there is usually no rush when solving a major problem that has already withstood all attempts at solution for many years; taking the few extra days to go through the paper one last time can save oneself a lot of trouble.
9. How much space in the paper is devoted to routine and standard theory and computations that already appears in previous literature, and how much is devoted to the new and exciting stuff which does not have any ready counterpart in previous literature? How soon in the paper does the new stuff appear? Are both parts of the paper being given appropriate amounts of detail?
Also, to reduce any potential negative reception to such a paper (especially if as is all too likely  significant errors are detected in it)  any bragging or otherwise selfpromoting text with little informative mathematical content should be kept to a minimum in the title, abstract, and introduction of the paper.
For instance: Example of a bad title: “A proof of the Poincaré
conjecture”.
Example of a good title: “The entropy formula for
the Ricci flow and its geometric applications”.
More generally,
given any major open problem, the importance of the problem and its
standard history will be a given to any informed reader, and should
only be given a perfunctory treatment in the paper, except for those
portions of the history of the problem which are of relevance to the
proof. Pointing out that countless great mathematicians had tried to solve the problem and failed before you came along is in particularly bad taste and should be avoided completely. It should also be noted that due to the sheer volume of failed attempts at solving these problems, most professional mathematicians will refuse to read any further attempts unless there is substantial auxiliary evidence that there is a nonzero chance of correctness (e.g. a previous track record of recognized mathematical achievement in the area). See for instance my editorial policy on papers involving a famous problem, or Oded Goldreich’s page on solving famous problems. See also Scott Aaronson’s “Ten signs a claimed mathematical proof is wrong” and Dick Lipton’s “On Mathematical Diseases”.

XV Don’t base career decisions on glamor or fame
One who pursues fame at the risk of losing one’s self, is not a scholar. (Zhuangzi, “The Grandmaster”)
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 glamor
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 and effort 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 longterm to just produce good mathematics
and contribute to your field, and the prizes and recognition will take care of themselves (and be wellearned when they eventually do appear). On the other hand, it can be worth researching why a problem or mathematician is famous, or how an institution or department earns its prestige; such specific
information can help you decide whether this problem, mathematician,
or department would be of interest to you.
See also “Which universities should I apply to?”

XVI 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.
See also “Learn and relearn your field”.

XVII 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.

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