EDP9 — a change of focus

The discussion in the last thread has noticeably moved on to new topics. In particular, multiplicative functions have been much less in the spotlight. Some progress has been made on the question of whether the Fourier transform of a sequence of bounded discrepancy must be very large somewhere, though the question is far from answered, and it is not even clear that the answer is yes. (One might suggest that the answer is trivially yes if EDP is true, but that is to misunderstand the question. An advantage of this question is that there could in theory be a positive answer not just for -valued functions but also for -valued functions with norm at least , say.)

Another question that has been investigated, mostly by Sune, is the question about what happens if one takes another structure (consisting of “pseudointegers”) for which EDP makes sense. The motivation for this is either to find a more general statement that seems to be true or to find a more general statement that seems to be false. In the first case, one would see that certain features of were not crucial to the problem, which would decrease the size of the “proof space” in which one was searching (since now one would try to find proofs that did not use these incidental features of ). In the second case, one would see that certain features of were crucial to the problem (since without them the answer would be negative), which would again decrease the size of the proof space. Perhaps the least satisfactory outcome of these investigations would be an example of a system that was very similar to where it was possible to prove EDP. For example, perhaps one could find a system of real numbers that was closed under multiplication and had a counting function very similar to that of , but that was very far from closed under addition. That might mean that there were no troublesome additive examples, and one might even be able to prove a more general result (that applied, e.g., to -valued functions). This would be interesting, but the proof, if it worked, would be succeeding by getting rid of the difficulties rather than dealing with them. However, even this would have some bearing on EDP itself, I think, as it would be a strong indication that it was indeed necessary to prove EDP by showing that counterexamples had to have certain properties (such as additive periodicity) and then pressing on from there to a contradiction.

EDP8 — what next?

It’s taken noticeably longer than usual for the number of comments on the previous EDP post to reach 100, so this is perhaps a good moment to think strategically about what we should do. Individual researchers continually have a choice — whether to take a break from the problem and work on other, possibly more fruitful, projects or to tackle that blank page head on and push towards a new level of understanding — and I see no difference with a Polymath project.

I would be interested in the views of others, but my own feeling is that there is still plenty to think about here. There has been a certain amount of talk about Fourier analysis, and that still feels like an insufficiently explored avenue. A good preliminary question, it seems to me, is this. Suppose that is a quasirandom -valued function defined on for some large , in the sense that all its Fourier coefficients are small. Must there be some HAP along which the sum has absolute value at least ? If so, how quasirandom does need to be? What I like about this question is that I think it should be substantially easier than EDP itself. It could be that a simple calculation would solve it: my attempts so far have failed, but not catastrophically enough to rule out the possibility that they could succeed next time. It also seems a pertinent question, because the functions we know of with very low discrepancy have some very high Fourier coefficients. (I don’t really mean Fourier coefficients, so much as real numbers such that has very large absolute value.) Therefore, proving that low discrepancy implies a high Fourier coefficient would be a result in the direction of proving that these examples are essentially the only ones, which would solve the problem.

DHJ latest

A quick post to say that earlier today I put a new version of the write-up of Polymath1’s proof of the density Hales-Jewett theorem on the arXiv. Very soon it will be submitted for publication. I will not say more at this stage (since I don’t want the journal to evaluate the paper in the public eye) but will report back when I know whether it has been accepted.

Update: it is now submitted.

EDP7 — emergency post

I don’t feel particularly ready for a post at this point, but the previous one has got to 100 comments, so this is one of the quick summaries again — but this one is even shorter than usual.

We are still doing an experimental investigation of multiplicative functions, trying to understand how special they have to be if they have low discrepancy. Ian Martin has produced some beautiful plots of the graphs of partial sums of multiplicative functions generated by various greedy algorithms. See this comment and the ensuing discussion.

Terence Tao has some thoughts about how one might try to reduce to the character-like case.

I came up with a proof strategy that I thought looked promising until I realized that it made predictions that are false for character-like functions such as and . Even if the idea doesn’t solve the problem, I think it may be good for something, so I have written a wiki page about it. Gil has had thoughts of a somewhat similar, but not identical, kind. Here is a related comment of Gil’s, and here are some more amazing plots of Ian’s. (I think we should set up a page on the wiki devoted to these plots and the ideas that led to them.) Regardless of what happens with EDP itself, I think we have some fascinating problems to think about, which can be summed up as, “What is going on with these plots?”

EDP6 — what are the chances of success?

I thought it might be good to have a post where I tried to take stock and assess the chances that Polymath5 will actually result in a solution to the Erdős discrepancy problem. But before I talk about that, I want to make the point, which I have made before, that solving the problem one sets out to solve is not a necessary condition for the attempt to count as worthwhile. There is easily enough material on the blog now for it to be possible to base a publishable paper on it, even if quite a lot of that paper ends up being a combination of a survey about the problem and a report on the interesting phenomena that have become apparent as a result of computations, some of which we understand reasonably well and some of which are still rather mysterious.

I am not saying this in order to hint that I think that it might be time to give up. At the moment it feels to me as though we still have momentum, so my enthusiasm is not flagging. What is mathematical momentum? I might define it as follows: an assault on an open problem has momentum if one’s understanding of the problem is continuing to develop. Right now I feel as though with each passing day I understand things about EDP that I did not understand before — and I presume that applies to everyone else too. And for as long as that is the case, one can never quite be sure that the problem won’t suddenly yield.

EDP5 — another very brief summary

I wasn’t expecting to have to write another post quite this soon, so this is another one where I don’t have much to say. Here are a few bits and bobs from the last lot of comments, but there’s plenty more in the comments themselves, and actually I think that it’s not that hard to browse through them now that we have depth-1 threading and quite a lot of the comments are very short.

Johan de Jong came up with a very interesting variant of the problem, in which is replaced by the space of polynomials over . I confess to being a little sad when the problem was solved negatively soon afterwards, as it had looked as though it might be a rather good model problem. However, the solution was nice.

One of the general aims at the moment is to try to show that a multiplicative function of bounded discrepancy must have some kind of character-like behaviour. Terence Tao has come up with an intriguing argument that shows not that but at least something in the right ball park.

Work has continued on a human proof that completely multiplicative sequences must have discrepancy greater than 2. It looks as though the proof will be complete before too long, and not too painful. Some nice tricks of Jason Dyer have come in helpful in reducing the amount of case analysis that is needed.