I learned about Szemerédi’s theorem in 1978 from the Séminaire Bourbaki talk by Jean-Paul Touvenot “La démonstration de Furstenberg du théorème de Szemerédi sur les progressions arithmétiques”. As it is clear already from the title, the talk was devoted to the work of Furstenberg and not to the work of Szemerédi.

The theorem itself looked amusing, being a generalization of a very well known theorem of van der Warden. The latter one was, probably, known to every former student of a mathematical school in USSR and was usually considered as a nice toy and a good way to show smart and mathematically inclined kids how tricky the use of the mathematical induction could be. Nobody considered it as a really important theorem or as a result comparable with the main work of van der Warden.

But the fact that such a statement can be proved by an application of the theory of dynamical systems was really surprising. It looks like Bourbaki devoted a talk to this subject exactly for the sake of this unusual at the time application and not for the sake of the theorem itself. According to a maxim attributed to Yu.I. Manin, proofs are more important than theorems, and definitions are more important than proofs. I wholeheartedly agree. In any case, the work of Szemerédi was not reported at the Séminaire Bourbaki. I also was impressed by this application of dynamical systems and later read several initial chapters of Furstenberg’s book. But when I told about this to a young very promising expert in my area of mathematics, I got very cold reception:

*“This is not interesting at all”*. Even references to Bourbaki and to the dynamical systems did not help. Now I think that we were both right. The theorem was not interesting because it was (and, apparently, still is) useless for anything but to proving its variations, and it is not sufficiently charming by itself (I think that the weaker van der Warden’s theorem is more charming). The theorem is interesting because it can be proved by tools completely alien to its natural context.

Then I more or less forgot about it, with a short interruption when Furstenberg’s book appeared.

Many years later I learned about T. Gowers from a famous and very remarkable mathematician, whom I will simply call M, short for Mathematician. In 1995 he told me about work of Gowers on Banach spaces, stressing that a great work may be completely unnoticed by the mathematical community. According to M, Gowers solved all open problems about Banach spaces. I had some mixed feelings about this claim and M’s opinion. May be Gowers indeed solved all problems of the Banach spaces theory (it seems that he did not), but who cares? For outsiders the theory of Banach spaces is a dead theory deserving a chapter in Bourbaki’s treatise because its basic theorems (about 80 years old) are exceptionally useful. On the other hand, Gowers was a Congress speaker in 1994, and this means that his work did not went unnoticed. In 1998 Gowers was awarded one of the four Fields medals for that year, quite unexpectedly to every mathematician with whom I discussed 1998 awards (M is not among them). It was also surprising that in his talk on the occasion of the award Gowers spoke not about his work on Banach spaces, but about a new approach to Szemerédi’s theorem. The approach was, in fact, not quite new: it extended the ideas of an early paper by K.-F. Roth on this topic (the paper is a few years earlier than his proof of what is known now as the Tue-Siegel-Roth theorem).

I trusted enough to M’s opinion to conclude that, probably, all work by Gowers deserves attention. So, I paid some attention to his work about Szemerédi’s theorem, but his paper looked technically forbidding (especially given that my main interests always were more or less at the opposite pole of pure mathematics). Then Gowers published a brilliantly written essay

*“Two cultures in mathematics”*. He argued that the mainstream mathematics, best represented by the work of Serre, Atiyah, Grothendieck and their followers (and may be even Witten, despite he is not really a mathematician) is no more than a half of mathematics,

*“the first culture”*, as he called it. Usually it is called

*“the conceptual mathematics”*, since the new concepts are much more important to it than solutions of particular problems (as was already mentioned, the definitions are more important than proofs and theorems). Gowers argued that there is an equally important

*“second culture”*. Apparently, it is best represented by the so-called

*“Hungarian combinatorics”*and the work of Erdös and his numerous collaborators. In this mathematics of

*“the second culture”*, the problems are stressed, the elementary (not involving abstract concepts, but may be very difficult) proofs are preferred, and no rigid structures (like the structure of a simple Lie algebra) are visible. Moreover, Gowers argued that both cultures are similar in several important aspects, despite this is very far from being transparent. A crucial part of his essay is devoted to outlining these similarities. All this was written in an excellent language at the level of best classical fiction literature, and appeared to be very convincing.

I decided to at least attempt to learn something from this

*“second culture”*. Very soon I have had some good opportunities. T. Gowers was giving a series of lectures about his work on Szemerédi’s theorem in a not very far university. I decided to drive there (a roundtrip for each lecture) and attend the lectures. The lectures turned out to be exceptionally good. Then, after I applied some minor pressure to one of my colleagues, he agreed to give a series of lectures about some tools used by Gowers in his work. His presentation was also exceptionally good. I also tried to read relevant chapters in some books. All this turned out to be even more attractive than I expected. I decided to teach a graduate course in combinatorics, and attempted to include some Gowers-style stuff. The latter wasn’t really successful; the subject matter is much more technically difficult (and I do not mean the work of Szemerédi and Gowers) than would be appropriate. Anyhow, over the years I devoted significant time and efforts to familiarize myself with this

*“second culture”*mathematics. This was interrupted both by mathematical reasons (it is nearly impossible to completely switch areas in the western mathematical community), and by some completely external circumstances.

When later I looked anew both at the

*“second culture”*mathematics and at the theory of the

*“Two cultures in mathematics”*, I could not help but to admit that they both lost their appeal. There is no second culture. The fact is that some branches of mathematics are not mature enough to replace assembling long proofs out of many similar pieces by a conceptual framework, making them less elementary, but more clear. The results of the second culture still looked isolated from the mainstream mathematics. I realized that the elementary combinatorial methods of proofs, characteristic for the purported second culture, occur everywhere (including my own work in

*“the first culture”*). I would not say that they are always inevitable, but very often it is simpler to verify some fact by a combinatorial argument than to find a conceptual framework trivializing it.

Perhaps, my opinion about the

*“second culture”*reached its peak on the day (April 8, 2004) of posting to the arXiv of the Green-Tao paper about arithmetic progression of primes. Prime numbers are the central notion of mathematics, and every new result about them is interesting. But gradually it became clear that the Green-Tao paper has nothing to do with primes. Green and Tao proved a generalization of Szemerédi’s theorem. By some completely independent results about primes due to Goldston and Yildirim, the set of primes satisfies the assumptions of the Green-Tao theorem. The juxtaposition of these two independent results leads to a nicely looking theorem. But anything new about primes is contained in the Goldston-Yildirim part, and not in Green-Tao part. This was a big disappointment.

So, the affair ended without any drama, in contrast with the novel

*“The End of the Affair”*by Graham Greene.

Next post: The politics of Timothy Gowers. 1.

Hi Owl,

ReplyDeleteThank you for your interesting blog. Can you tell me what is the basic theorem of Banach space you have mentioned above? Thank you.

Dear John Plant,

ReplyDeleteDo you mean the 80 years old results, or Gowers's results? One can get some idea about the latter from Gowers's talk at the 1994 Congress, which is available at pdf file of the Gowers's talk, as also from his more technical publications. By now at least some of them found their way into at least two advanced level textbooks/research monographs (one is closer to one category, the other is closer to the other category).

The 80 years old theorems I had in mind are included in more or less every functional analysis textbook (the classics like Dunford-Schwartz, Volume 1, or Rudin, are, probably, better than more modern books). The main are the Hahn-Banach theorem, the open mapping theorem, the closed graph theorem, and related results. Perhaps, one should add to them the Krein-Milman theorem from the late 40ies.

Thank you very much for your interest in my blog. Please, do not hesitate to ask.

Dear Owl,

ReplyDeleteThanks a lot for your response. I meant the 80 years old theorems.

I think that nowadays most of mathematics published papers are useless for the progress of mathematics but most of them are useful in someway for human society. However, it must be very careful to honor someone by big prizes because they might make wrong ways for people. Do you agree with me?

Dear Owl,

ReplyDeleteI read your blog with great interest. Thank you.

In this post you wrote: "it is nearly impossible to completely switch areas in the western mathematical community".

Could you please elaborate on that? What are the obstacles?

Maph33333:

Delete"Now, here, you see, it takes all the running you can do, to keep in the same place. If you want to get somewhere else, you must run at least twice as fast as that!" - L. Carroll, Through the Looking-Glass.

You expected to publish, to give talks at a zillion of conferences, to serve as a referee, to be an editor of journals and/or conference proceedings, to get grants, etc. If you change the area you work in, you are a beginner and you need to prove yourself. If you stay in the same area, in few years you know everybody, you are invited to give talk by default, without asking if you have any new results - and you will always be able to find something to talk about. Your papers accepted because you are an expert in a particular area. May be the only one, but still a leading expert. You get grants because you are "on the list".

If you are confident enough and do not care much about that other people say, you may try to ignore all this.

But nowadays you will be also pressed by your chairperson and your colleagues. The situation changed, the universities are run now not by the faculty, as it used to be, but by career administrators. Administrators do not care about your desire to change fields, or about your long term projects. Grisha Perelman would not get tenure in US: he did not published anything since 1995, and would fail the tenure review sometimes in 2001-2002. The administrators understand only numbers: of publications, of citations, or, best of all, of dollars (of the grant money).

It is rather sad, but in the modern US the faculty prefers to listen to the administrators, not to their colleagues.