The polymath blog

June 4, 2013

Polymath proposal: bounded gaps between primes

Filed under: planning,polymath proposals — Terence Tao @ 4:31 am

Two weeks ago, Yitang Zhang announced his result establishing that bounded gaps between primes occur infinitely often, with the explicit upper bound of 70,000,000 given for this gap.  Since then there has been a flurry of activity in reducing this bound, with the current record being 4,802,222 (but likely to improve at least by a little bit in the near future).

It seems that this naturally suggests a Polymath project with two interrelated goals:

  1. Further improving the numerical upper bound on gaps between primes; and
  2. Understanding and clarifying Zhang’s argument (and other related literature, e.g. the work of Bombieri, Fouvry, Friedlander, and Iwaniec on variants of the Elliott-Halberstam conjecture).

Part 1 of this project splits off into somewhat independent sub-projects:

  1. Finding narrow prime admissible tuples of a given cardinality (or, dually, finding large prime admissible tuples in a given interval).  This part of the project would be relatively elementary in nature, relying on combinatorics, elementary number theory, computer search, and perhaps some clever algorithm design.  (Scott Morrison has already been hosting a de facto project of this form at this page, and is happy to continue doing so).
  2. Solving a calculus of variations problem associated with the Goldston-Yildirim-Pintz argument (discussed at this blog post, or in this older survey of Soundararajan) [in particular, this could lead to an improvement of a certain key parameter k_0, currently at 341,640, even without any improvement in the parameter \varpi mentioned in part 3. below.]
  3. Delving through the “hard” part of Zhang’s paper in order to improve the value of a certain key parameter \varpi (which Zhang sets at 1/1168, but is likely to be enlargeable).

Part 2 of this project could be run as an online reading seminar, similar to the online reading seminar of the Furstenberg-Katznelson paper that was part of the Polymath1 project.  It would likely focus on the second half of Zhang’s paper and would fit well with part 1.3.  I could run this on my blog, and this existing blog post of mine could be used for part 1.2.

As with other polymath projects, it is conceivable that enough results are obtained to justify publishing one or more articles (which, traditionally, we would publish under the D.H.J. Polymath pseudonym).  But it is perhaps premature to discuss this possibility at this early stage of the process.

Anyway, I would be interested to gauge the level of interest and likely participation in these projects, together with any suggestions for improving the proposal or other feedback.

April 28, 2011

Polymath wiki logo

Filed under: planning — Terence Tao @ 4:37 pm

Michael Nielsen has collected a number of possible logos for the polymath wiki and is asking for discussion on them.

June 12, 2010

Mini-polymath proposal: IMO 2010 Q6

Filed under: news,planning,polymath proposals — Terence Tao @ 11:16 pm

I am proposing the sixth question for the 2010 International Mathematical Olympiad (traditionally, the trickiest of the six problems) as a mini-polymath project for next month.  Details and discussions are in this post on my other blog.

[Update, June 27: the project is scheduled to start on Thursday, July 8 16:00 UTC.]


August 3, 2009

Polymath on other blogs

Filed under: planning — Terence Tao @ 12:33 pm

There has been some discussion of the polymath enterprise on other blogs, so I thought it would be good to collect these links on the main polymath wiki page.  If you find another link about polymath on the net, please feel free to add it to the wiki also (or at least to mention it in the comments here).

It should also be mentioned that besides the proposed polymath projects on this blog, Gil Kalai is in the process of setting up a polymath project on the polynomial Hirsch conjecture, tentatively scheduled to be launched later this month.  See the following preparatory posts:

  1. The polynomial Hirsch conjecture, a proposal for Polymath 3 (July 17)
  2. The polynomial Hirsch conjecture, a proposal for Polymath 3 cont. (July 28)
  3. The polynomial Hirsch conjecture – how to improve the upper bounds (July 30)
  4.  The polynomial Hirsch conjecture : discussion thread (August 9)
  5.  The polynomial Hiresch conjecture: discussion thread continued (September 6)
  6. Plans for polymath3 (December 8). The plan is to launched polymath3 on the polynomial Hirsch conjecture in April 15, 2010.

An extremely rudimentary wiki page for the proposed project has now been created.

polymath3

New: Tim Gowers devotes a post to several proposals for a polymath project in November.

July 27, 2009

Selecting another polymath project

Filed under: planning — Terence Tao @ 5:55 pm

In a few months (the tentative target date is October), we plan to launch another polymath project (though there may also be additional projects before this date); however, at this stage, we have not yet settled on what that project would be, or even how exactly we are to select it.  The purpose of this post, then, is to begin a sort of pre-pre-selection process, in which we discuss how to organise the search for a new project, what criteria we would use to identify particularly promising projects, and how to run the ensuing discussion or voting to decide exactly which project to begin.  (We think it best to only launch one project at a time, for reasons to be discussed below.)

There are already a small number of polymath projects being proposed, and I expect this number to grow in the near future.  Anyone with a problem which is potentially receptive to the polymath approach, and who is willing to invest significant amounts of time and effort to administrate and advance the effort, is welcome to make their own proposal, either in their own forum, or by contacting one of us.  (If you do make a proposal on your own wordpress blog, put it in the category “polymath proposals” so that it will be picked up by the above link.)    There is already some preliminary debate and discussion at the pages of each of these proposals, though one should avoid any major sustained efforts at solving the problem yet, until the participants for the project are fully assembled and prepared, and the formal polymath threads are ready to launch.

[One lesson we got from the minipolymath feedback was that one would like a long period of lead time before a polymath project is formally launched, to get people prepared by reading up and allocating time in advance.    So it makes sense to have the outlines of a project revealed well in advance, though perhaps the precise details of the project (e.g. a compilation of the proposer’s own thoughts on the problem) can wait until the launch date.]

On the other hand, we do not want to launch multiple projects at once.  So far, the response to each new launched project has been overwhelming, but this may not always be the case in the future, and in particular simultaneous projects may have to compete with each other for attention, and perhaps most crucially, for the time and efforts of the core participants of the project.  Such a conflict would be particularly acute for projects that are in the same field, or in related fields.  (In particular, we would like to diversify the polymath enterprise beyond combinatorics, which is where most of the existing projects lie.)

So we need some way to identify the most promising projects to work on.  What criteria would we look for in a polymath project that would indicate a high likelihood of full or partial success, or at least a valuable learning experience to aid the organisation of future projects of this type?  Some key factors come to mind:

  1. The amount of expected participation. The more people who are interested in participating, both at a casual level and at a more active full time level, the better the chances that the project will be a success.  We may end up polling readers of this blog for their expected participation level (no participation, observation only, casual participation, active participation, organiser/moderator) for each proposed project, to get some idea as to the interest level.
  2. The feasibility of the project. I would imagine that a polymath to solve the Riemann Hypothesis will be a spectacular and frustrating fiasco; we should focus on problems that look like some progress can be made.  Ideally, there should be several potentially promising avenues of inquiry identified in advance; simply dumping the problem onto the participants with no suggestions whatsoever (as was done with the minipolymath project) seems to be a suboptimal way to proceed.
  3. The flexibility of the project. This is related to point #2; it may be that the problem as stated is beyond the ability of the polymath effort, but perhaps some interesting variant of the problem is more feasible.  A problem which allows for a number of variations would be more suitable for a polymath effort, especially since polymath projects seem particularly capable of pursuing multiple directions of attack at once.
  4. The available time and energy of the administrator. Another thing we learned from the minipolymath project was that these projects need one or more active leaders who are willing to take the initiative and push the project in the directions it needs to go (e.g. by encouraging more efforts at exposition when the flood of ideas become too chaotic).  The proposer of a project would be one obvious choice for such a leader, but there seems to be no reason why a project could have multiple such leaders (and any given participant could choose to seize the initiative and make a major push to advance the project unilaterally).
  5. The barriers to entry. Some projects may require a substantial amount of technical preparation before participation; this is perhaps one reason why existing projects have been focused on “elementary” fields of mathematics, such as combinatorics.  Nevertheless, it should be possible (perhaps with some tweaking of the format) to adapt these projects to more “sophisticated” mathematical fields.  For instance, one could imagine a polymath project which is not aimed at solving a particular problem per se, but is instead trying to understand a difficult mathematical topic (e.g. quantum field theory, to pick a subject a random) as thoroughly as possible.  Given the right leadership, and sufficient interest, this very different type of polymath project could well be a great success.
  6. Lack of conflict with existing research. It has been pointed out that one should be careful not to let a polymath project steamroll over the existing research plans of some mathematician (e.g. a grad student’s thesis).  This is one reason why we are planning an extended process to select projects, so that such clashes can be identified as early as possible, presumably removing that particular project from contention.  (There is also the danger that even a proposal for a polymath project may deter other mathematicians from pursuing that problem by more traditional means; this is another point worth discussing here.)

Over to the other readers of this blog: what else should we be looking for in a polymath project?  How quickly should we proceed with the selection process?  Should we decide by popular vote, or by some fixed criteria?

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