I imagine most people reading this will already have heard that Terence Tao has solved the Erdős discrepancy problem. He has blogged about the solution in two posts, a first that shows how to reduce the problem to the Elliott conjecture in number theory, and a second that shows (i) that an averaged form of the conjecture is sufficient and (ii) that he can prove the averaged form. Two preprints covering (i) and (ii) are here and here: the one covering (i) has been submitted to Discrete Analysis.
This post is therefore the final post of the polymath5 project. I refer you to Terry’s posts for the mathematics. I will just make a few comments about what all this says about polymath projects in general.
After the success of the first polymath project, which found a purely combinatorial proof of the density Hales-Jewett theorem, there was an appetite to try something similar. However, the subsequent experience made it look as though the first project had been rather lucky, and not necessarily a good indication of what the polymath approach will typically achieve. I started polymath2, about a Banach-space problem, which never really got off the ground. Gil Kalai started polymath3, on the polynomial Hirsch conjecture, but the problem was not solved. Terence Tao started polymath4, about finding a deterministic algorithm to output a prime between and , which did not find such an algorithm but did prove some partial results that were interesting enough to publish in an AMS journal called Mathematics of Computation. I started polymath5, with the aim of solving the Erdős discrepancy problem (after this problem was chosen by a vote from a shortlist that I drew up), and although we had some interesting ideas, we did not solve the problem. The most obviously successful polymath project was polymath8, which aimed to bring down the size of the gap in Zhang’s prime-gaps result, but it could be argued that success for that project was guaranteed in advance: it was obvious that the gap could be reduced, and the only question was how far.
Actually, that last argument is not very convincing, since a lot more came out of polymath8 than just a tightening up of the individual steps of Zhang’s argument. But I want to concentrate on polymath5. I have always felt that that project, despite not solving the problem, was a distinct success, because by the end of it I, and I was not alone, understood the problem far better and in a very different way. So when I discussed the polymath approach with people, I described its virtues as follows: a polymath discussion tends to go at lightning speed through all the preliminary stages of solving a difficult problem — trying out ideas, reformulating, asking interesting variants of the question, finding potentially useful reductions, and so on. With some problems, once you’ve done all that, the problem is softened up and you can go on and solve it. With others, the difficulties that remain are still substantial, but at least you understand far better what they are.
In the light of what has now happened, the second case seems like a very accurate description of the polymath5 project, since Terence Tao used ideas from that project in an essential way, but also recent breakthroughs in number theory by Kaisa Matomäki and Maksim Radziwiłł that led on to work by those authors and Terry himself that led on to the averaged form of the Elliott conjecture that Terry has just proved. Thus, if the proof of the Erdős discrepancy problem in some sense requires these ideas, then there was no way we could possibly have hoped to solve the problem back in 2010, when polymath5 was running, but what we did achieve was to create a sort of penumbra around the problem, which had the effect that when these remarkable results in number theory became available, the application to the Erdős discrepancy problem was significantly easier to spot, at least for Terence Tao …
I’ll remark here that the approach to the problem that excited me most when we were thinking about it was a use of duality to reduce the problem to an existential statement: you “just” have to find a function with certain properties and you are done. Unfortunately, finding such a function proved to be extremely hard. Terry’s work proves abstractly that such a function exists, but doesn’t tell us how to construct it. So I’m left feeling that perhaps I was a bit too wedded to that duality approach, though I also think that it would still be very nice if someone managed to make it work.
There are a couple of other questions that are interesting to think about. The first is whether polymath5 really did play a significant role in the discovery of the solution. Terry refers to the work of polymath5, but one of the key polymath5 steps he uses was contributed by him, so perhaps he could have just done the whole thing on his own.
At the very least I would say that polymath5 got him interested in the problem, and took him quickly through the stage I talked about above of looking at it from many different angles. Also, the Fourier reduction argument that Terry found was a sort of response to observations and speculations that had taken place in the earlier discussion, so it seems likely that in some sense polymath5 played a role in provoking Terry to have the thoughts he did. My own experience of polymath projects is that they often provoke me to have thoughts I wouldn’t have had otherwise, even if the relationship between those thoughts and what other people have written is very hard to pin down — it can be a bit like those moments where someone says A, and then you think of B, which appears to have nothing to do with A, but then you manage to reconstruct your daydreamy thought processes to see that A made you think of C, which made you think of D, which made you think of B.
Another question is what should happen to polymath projects that don’t result in a solution of the problem that they are trying to solve, but do have useful ideas. Shouldn’t there come a time when the project “closes” and the participants (and othes) are free to think about the problem individually? I feel strongly that there should, since otherwise there is a danger that a polymath project could actually delay progress on a problem by discouraging research on it. With polymath5 I tried to signal such a “closure” by writing a survey article that was partly about the work of polymath5. And Terry has now written up his work as an individual author, but been careful to say which ingredients of his proof were part of the polymath5 discussion and which were new. That seems to me to be exactly how things should work, but perhaps the lesson for the future is that the closing of a polymath project should be done more explicitly — up to now several of them have just quietly died. I had at one time intended to do rather more than what I did in the survey article, and write up, on behalf of polymath5 and published under the polymath name, a proper paper that would contain the main ideas discovered by polymath5 with full proofs. That would have been a better way of closing the project and would have led to a cleaner situation — Terry could have referred to that paper just as anyone refers to a mathematical paper. But while I regret not getting round to that, I don’t regret it too much, because I also quite like the idea that polymath5’s ideas are freely available on the internet but not in the form of a traditional journal article. (I still think that on balance it would have been better to write up the ideas though.)
Another lesson for the future is that it would be great to have some more polymath projects. We now know that Polymath5 has accelerated the solution of a famous open problem. I think we should be encouraged by this and try to do the same for several other famous open problems, but this time with the idea that as soon as the discussion stalls, the project will be declared to be finished. Gil Kalai has said on his blog that he plans to start a new project: I hope it will happen soon. And at some point when I feel slightly less busy, I would like to start one too, on another notorious problem with an elementary statement. It would be interesting to see whether a large group of people thinking together could find anything new to say about, for example, Frankl’s union-closed conjecture, or the asymptotics of Ramsey numbers, or the cap-set problem, or …