About the title

About the title

I changed the title of the blog on March 20, 2013 (it used to have the title “Notes of an owl”). This was my immediate reaction to the news the T. Gowers was presenting to the public the works of P. Deligne on the occasion of the award of the Abel prize to Deligne in 2013 (by his own admission, T. Gowers is not qualified to do this).

The issue at hand is not just the lack of qualification; the real issue is that the award to P. Deligne is, unfortunately, the best compensation to the mathematical community for the 2012 award of Abel prize to Szemerédi. I predicted Deligne before the announcement on these grounds alone. I would prefer if the prize to P. Deligne would be awarded out of pure appreciation of his work.

I believe that mathematicians urgently need to stop the growth of Gowers's influence, and, first of all, his initiatives in mathematical publishing. I wrote extensively about the first one; now there is another: to take over the arXiv overlay electronic journals. The same arguments apply.

Now it looks like this title is very good, contrary to my initial opinion. And there is no way back.

Wednesday, August 21, 2013

About some ways to work in mathematics

Previous post: New ideas.

From a comment by Tamas Gabal:

“...you mentioned that the problems are often solved by methods developed for completely different purposes. This can be interpreted in two different ways. First - if you work on some problem, you should constantly look for ideas that may seem unrelated to apply to your problem. Second - focus entirely on the development of your ideas and look for problems that may seem unrelated to apply your ideas. I personally lean toward the latter, but your advice may be different.”

Both ways to work are possible. There are also other ways: for example, not to have any specific problem to solve. One should not suggest one way or another as the right one. You should work in the way which suits you more. Otherwise you are unlikely to succeed and you will miss most of the joy.

Actually, my statement did not suggest either of these approaches. Sometimes a problem is solved by discovering a connection between previously unrelated fields, and sometimes a problem is solved entirely within the context in was posed originally. You never know. And how one constantly looks for outside ideas? A useful idea may be hidden deep inside of some theory and invisible otherwise. Nobody studies the whole mathematics in the hope that this will help to solve a specific problem.

I think that it would be better not to think in terms of this alternative at all. You have a problem to solve, you work on it in all ways you can (most of approaches will fail – this is the unpleasant part of the profession), and that’s it. The advice would be to follow development in a sufficiently big chunk of mathematics. Do not limit yourself by, say, algebra (if your field is algebra). The division of mathematics into geometry, algebra, and analysis is quite outdated. Then you may suddenly learn about some idea which will help you.

Also, you do not need to have a problem to begin with. Usually a mathematician starts with a precisely stated problem, suggested by the Ph.D. advisor. But even this is not necessary.

My own way to work is very close to the way M. Atiyah described as his way of work in an interview published in “The Mathematical Intelligencer” in early 1980ies (of course, I do not claim that the achievements are comparable). This interview is highly recommended; it is also highly recommended by T. Gowers. I believe that I explained how I work to a friend (who asked a question similar to yours one) before I read this interview. Anyhow, I described my way to him as follows. I do not work on any specific problem, except of my own working conjectures. I am swimming in mathematics like in a sea or river and look around for interesting things (the river of mathematics carries much more stuff than a real river). Technically this means that I follow various sources informing about the current developments, including talks, I read papers, both current and old ones, and I learn some stuff from textbooks. An advanced graduate level textbook not in my area is my favorite type of books in mathematics. I am doing this because this is that I like to do, not because I want to solve a problem or need to publish 12 papers during next 3 years. From time to time I see something to which, I feel, I can contribute. From time to time I see some connections which were not noticed before.

My work in “my area” started in the following way. I was familiar with a very new theory, which I learned from the only available (till about 2-3 years ago!) source: a French seminar devoted to its exposition. The author never wrote down any details. Then a famous mathematician visited us and gave a talk about a new (not published yet) remarkable theorem of another mathematician (it seems to me that it is good when people speak not only about their own work). The proof used at a key point an outside “Theorem A” by still another mathematicians. The speaker outlined its proof in few phrases (most speakers would just quote Theorem A, so I was really lucky). Very soon I realized (may be the same day or even during the talk) that the above new theory allows at least partially transplant Theorem A in a completely different context following the outline from the talk. But there is a problem: the conclusion of Theorem A tells that you are either in a very nice generic situation, or in an exceptional situation. In my context there are obvious exceptions, but I had no idea if there are non-obvious exceptions, and how to approach any exceptions. So, I did not even started to work on any details. 2-3 years later a preprint arrived in the mail. It was sent to me by reasons not related at all with the above story; actually, I did not tell anybody about these ideas. The preprint contained exactly what I needed: a proof that there are only obvious exceptional cases (not mentioning Theorem A). Within a month I had a proof of an analogue of Theorem A (this proof was quickly replaced by a better one and I am not able to reproduce it). Naturally, I started to look around: what else can be done in my context. As it turned out, a lot. And the theory I learned from that French seminar is not needed for many interesting things.

Could all this be planned in advance following some advice of some experienced person? Certainly, not. But if you do like this style, my advice would be: work this way. You will be not able to predict when you will discover something interesting, but you will discover. If this style does not appeal to you, do not try.

Note that this style is opposite to the Gowers’s one. He starts with a problem. His belief that mathematics can be done by computers is based on a not quite explicit assumption that his is the only way, and he keeps a place for humans in his not-very-science-fiction at least at the beginning: humans are needed as the source of problems for computers. I don’t see any motivation for humans to supply computers with mathematical problems, but, apparently, Gowers does. More importantly, a part of mathematics which admits solutions of its problems by computers will very soon die out. Since the proofs will be produced and verified by computers, humans will have no source of inspiration (which is the proofs).

Next post: Is algebraic geometry applied or pure mathematics?


  1. Dear Sowa,

    This is very interesting. I am sure your approach will appeal to many young mathematicians and it is reassuring to know that "you will be not able to predict when you will discover something interesting, but you will discover". It only makes me wonder how risky this approach may be at the beginning of one's career given the pressure to publish regularly? But, as you say, if this style makes you happy, go for it. Mathematics is so hard, and there is no better motivation than enjoying what you do.

    It would also be invaluable if you could make a list of your favorite graduate level textbooks when you have time.

  2. The interview with Atiyah was a great read, very inspirational. However, not many mathematicians can "move around in the mathematical waters" as easily as he does, which requires a lot of talent. I also think that he puts too little weight on the fact that sometimes in order to increase the understanding you need to break through the obstacle. I am not sure that it is always possible to "go around the problem, behind the problem.., and so the problem disappears". In any case, it is a beautiful interview.

  3. Dear Tamas Gabal,

    You are correct, this approach is risky. It wasn’t so risky in the past. In any case, if some approach is much more suitable for you than any other, then you have serious chances to succeed by doing things in your way. Most likely you will miserably fail working in other styles. You asked about my experience, and my story is nothing more. It is not an advice.

    My message here is that it is possible to work this way, it may be very enjoyable, and it is possible to succeed in this way. One can even get a Fields medal and have a huge influence on the whole mathematics, as it happened with M. Atiyah. I suspect that many are not aware of such way of working and think that mathematics is about solving some problems.

    I am glad you liked that interview. Every mathematician should read it. I don’t think that “moving around in the mathematical waters” like Atiyah requires a special talent. Rather, it requires some personality traits. And, of course, one should be near this ocean. The latter is much easier in times of the internet than in times of Atiyah. Atiyah had wonderful opportunities to meet and to work with mathematicians of about the same caliber as he himself. It seems that in order to have these opportunities, he needed only to demonstrate his level in few first papers, and then show his efficiency as a collaborator at least once. Then he is regularly invited to the Institute of Advanced Studies and other places; not to give a talk, but for a long term stay. I have had no comparable opportunities by geopolitical reasons.

    I respectfully disagree about obstacles. According to an old joke about mathematicians, a mathematician would spend a year looking for a way to solve his problem in an hour, while it would be possible to solve that problem directly in two weeks. I like this aspect of mathematics. There are no (purely) mathematical problems that need to be solved quickly. So we can wait till the problem disappears.

    Let me try the following analogy. There are two rooms with a common wall in huge complicated building. You need to get from one to the other, but there are no doors between them; if you go to the hallway, there are no doors into the room of interest, etc. The Hollywood way to deal with such a situation is to break the wall. Certainly, such a way is justified if a bomb is ticking in that room. But no unsolved mathematical problem presents any danger. The alternative way is to investigate the whole building, and understand its design. Then you will see some way to get into that room without breaking anything (except if it is not really a room). It may even turn out that the design of the building and other rooms are so interesting that you will forget about your original goal.

    The Last Fermat Theorem was such a room. In early 1980ies it was realized that it is a corollary of a system of very natural conjectures, which would be investigated in any case (i.e. that it is a small room in a huge building). Only after this A. Wiles started to work – to work not on the LFT, in fact, but on a key conjecture, the modularity conjecture. And this is despite he dreamed about proving the FLT since his school years. Other conjectures were proved by other mathematicians earlier. He proved eventually the modularity conjecture (with the help of R. Taylor at the end), and the FLT was an automatic corollary.

    I will think about a list of books. It shouldn’t be hard.

    The real problem is that many really needed books are not written, and there is a little hope that they will be written in any foreseeable future. Few years ago I had 2-3 of book projects (with my course notes and even parts typeset in TeX). They are essentially abandoned by now, since I see no acceptable to me ways to publish them.

  4. The insistence (by such as Gowers) that mathematics is a collection of problems to be solved rather than an exploration of a part of nature reflects the existence of applied mathematics which, by definition, consists of problems. Of course, this observation is very old and well known but maybe bearing it in mind helps to understand the genesis of Gowers' position. (It is also true that, in my experience, Hungarian-style combinatorialists hate to be described as applied mathematicians so their agreement with this point is not to be expected.)

  5. Dear xerxes,

    I am unable to agree with any part of your argument. T. Gowers never worked in applied mathematics in any known to me sense. I fail to see how the existence of applied mathematics may explain the genesis of *his* position.

    The claim that applied mathematics consists of problems *by definition* is something that I cannot even interpret somehow. Different people hold different positions about what is the applied mathematics, or about its value. But all (except you) think that it is something similar to other sciences and to mathematics. There are theories, methods, desire to understand things. In fact, it seems that interest in "problems" in the sense mathematicians use this word is much less in applied mathematics than in the pure mathematics.

  6. This division into 'pure' and 'applied' mathematics is real, as it is understood and awkwardly enforced by the math departments in the US. How is algebraic geometry not 'applied' when so much of its development is motivated by theoretical physics?

    I also agree that many 'applied' areas of mathematics do not have famous open problems, unlike 'pure' areas. In 'applied' areas it is more difficult to make bold conjectures, because the questions are often imprecise. They are trying to explain certain phenomena and most efforts are devoted to incremental improvements of algorithms, estimates, etc.

  7. Dear Tamas Gabal,

    My reply to your first paragraph is Is algebraic geometry applied or pure mathematics?.

    The reply to the second paragraph is The role of the problems.