A polymath-style project on non transitive dice (Wikipedea) is now running over Gowers blog. (Here is the link to the first post.)

A polymath-style project on non transitive dice (Wikipedea) is now running over Gowers blog. (Here is the link to the first post.)

We haven’t quite hit the 100-comment mark on the second Polymath 12 blog post, but this seems like a good moment to take stock. The project has lost some of its initial momentum, perhaps because other priorities have intruded into the lives of the main participants (I know that this is true of myself). However, I don’t want to turn out the lights just yet, because I don’t believe we’re actually stuck. Let me take this opportunity to describe some of the leads that I think are most promising.

For general matroids, the online version of Rota’s Basis Conjecture is false, but it is still interesting to ask how many bases are achievable. One of the nicest things to come out Polymath 12, in my opinion, has been a partial answer to this question: It is somewhere between *n*/3 + *c* and *n*/2 + *c*. There is hope that this gap could be closed. If the gap can be closed then in my opinion this would be a publishable short paper. Incidentally, if a paper is published by Polymath 12, what pseudonym should be used? I know that D. H. J. Polymath was used for the first project, but maybe R. B. C. Polymath would make more sense?

It was suggested early on that graphic matroids might be a more tractable special case. It wasn’t immediately clear to me at first why, but I understand better now. Specifically, graphic matroids with no *K*_{4} minor are series-parallel and therefore strongly base-orderable and therefore satisfy Rota’s Basis Conjecture. Thus, in some sense, *K*_{4} is the *only* obstruction to Rota’s Basis Conjecture for graphic matroids, whereas the analogous claim for matroids in general does not hold.

In one of my papers I showed, roughly speaking, that if one can prove an *n* × 2 version of Rota’s Basis Conjecture, then this fact can be parlayed into a proof of the full conjecture. Of course the *n* × 2 version is false in general, but I do believe that a thorough understanding of what can happen in just two columns will give significant insight into the full conjecture. One question I raised was whether any *n* × 2 arrangement of edges can yield two columns that are bases if we pull out no more than *n*/3 edges. This is perhaps a somewhat clumsy question, but it is trying to get at the question of whether there are any *n* × 2 counterexamples that are not just the disjoint union of copies of *K*_{4} that have been expanded by “uncontracting” some edges. If we can classify all *n* × 2 counterexamples then I think that this would be a big step towards proving the full conjecture for graphic matroids.

This is of course not the only possible way to tackle graphic matroids. The main point is that I think there is potential for serious progress on this special case.

I mentioned an unpublished manuscript by Michael Cheung that reports that the *n* = 4 case of Rota’s Basis Conjecture is true for all matroids. I find this to be an impressive computation and I think it deserves independent verification.

Finding 5 × 2 counterexamples to Rota’s Basis Conjecture would also be illuminating in my opinion. Gordon Royle provided a link to a database of all nine-element matroids that should be helpful. Luke Pebody started down this road but as far as I know has not completed the computation.

In 1995, Marcel Wild proved the following result (“Lemma 6”): Let be a matroid on an -element set that is a disjoint union of independent sets of size . Assume that there exists another matroid on the same ground set with the following properties:

(1) is strongly base orderable.

(2) for all , where is the rank function of .

(3) All circuits of satisfying remain dependent in .

Then there is an grid whose th row comprises and whose columns are independent in .

Wild obtained several partial results as a corollary of Lemma 6. How much mileage can we get out of this? Can we always find a suitable for graphic matroids?

I’m less optimistic that these will lead to progress on Rota’s Basis Conjecture itself, but maybe I’m wrong. Gil Kalai made several suggestions:

- Consider
*d*+ 1 (affinely independent) subsets of size*d*+ 1 of such that the origin belongs to the interior of the convex hull of each set. Is it possible to find*d*+ 1 sets of size*d*+ 1 such that each set is a rainbow set and the interior of the convex hulls of all these sets have a point in common? - The wide partition conjecture or its generalization to arbitrary partitions.
- If we have sets
*B*_{1}, …,*B*(not necessarily bases) that_{n}*cannot*be arranged so that all*n*columns are bases, then can you always find disjoint*n*+ 1 sets*C*_{1}, …,*C*_{n+1}such that each set contains at most one member from each*B*and the intersection of all linear spans of the_{j}*C*_{i}is non trivial? (I confess I still don’t see why we should expect this to be true.)

Pavel Paták presented a lemma from one of his papers that might be useful. Let *M* be a matroid of rank *r* and let *S* be a sequence of *kr* elements from *M*, split into *r* subsequences, each of length at most *k*. Then any largest independent rainbow subsequence of *S* is a basis of *M *if and only if there does not exist an integer *s* < *r* and set of *s* + 1 color classes, such that the union of these color classes has rank *s*.

In a different direction, there are graph-theoretic conjectures such as the Brualdi–Hollingsworth conjecture: If the complete graph *K*_{2m} (for *m* ≥ 3) is edge-colored in such a way that every color class is a perfect matching, then there is a decomposition of the edges into *m* edge-disjoint rainbow spanning trees.

Finally, let me make a few remarks about the directions of research that were suggested in my previous Polymath 12 blog post. I was initially optimistic about matroids with no small circuits and I still think that they are worth thinking about, but I am now more pessimistic that we can get much mileage out of straightforwardly generalizing the methods of Geelen and Humphries, for reasons that can be found by reading the comments. Similarly I am more pessimistic now that the algebro-geometric approach will yield anything since being a basis is an open condition rather than a closed condition.

The other leads in that blog post have not been pursued much and I think they are still worth looking at. In particular, that old standby, the Alon–Tarsi Conjecture, may still admit more partial results. Rebecca Stones’s suggestion that maybe *L _{n}*

There has been enough interest that I think we can formally declare Rota’s Basis Conjecture to be Polymath 12. I am told that it is standard Polymath practice to start a new blog post whenever the number of comments reaches about 100, and we have reached that point, so that is one reason I am writing a second post at this time. I am also told that sometimes, separate “discussion” and “research” threads are created; I’m not seeing an immediate need for such a separation yet, and so I am not going to state a rule that comments of one type belong under the original post whereas comments of some other type belong under this new post. I will just say that if you are in doubt, I recommend posting new comments under this post rather than the old one, but if common sense clearly says that your comment belongs under the old post then you should use common sense.

The other reason to create a new post is to take stock of where we are and perhaps suggest some ways to go forward. Let me emphasize that the list below is not comprehensive, but is meant only to summarize the comments so far and to throw in a few ideas of my own. Assuming this project continues to gather steam, the plan is to populate the associated Polymath Wiki page with a more comprehensive list of references and statements of partial results. If you have an idea that does not seem to fit into any of the categories below, please consider that to be an invitation to leave a comment about your idea, not an indication that it is not of interest!

I want to start with an idea that I mentioned in my MathOverflow post but not in my previous Polymath Blog post. I think it is very promising, and I don’t think many people have looked at it. Geelen and Humphries proved that Rota’s Basis Conjecture is true for paving matroids. In the case of vector spaces, what this means is that they proved the conjecture in the case where every (*n* – 1)-element subset of the given set of *n*^{2} vectors is linearly independent. It is natural to ask if *n* – 1 can be reduced to *n* – 2. I have not digested the Geelen–Humphries paper so I do not know how easy or hard this might be, but it certainly could not hurt to have more people study this paper and make an attempt to extend its results. If an oracle were to tell me that Rota’s Basis Conjecture has a 10-page proof and were to ask me what I thought the method was, then at this point in time I would guess that the proof proceeds by induction on the size of the smallest circuit. Even if I am totally wrong, I think we will definitely learn something by understanding exactly why this approach cannot be extended.

Let me now review the progress on the three ideas I mentioned in my first blog post. In Idea 1, I asked if the *n*^{2} vectors could be partitioned into at most 2*n* – 2 independent partial transversals. A nice proof that the answer is yes was given by domotorp. Eli Berger then made a comment that suggested that the topological methods of Aharoni and Berger could push this bound lower, but there was either an error in his suggestion or we misunderstood it. It would be good to get this point clarified. I should also mention that Aharoni mentioned to me offline that he unfortunately could not participate actively in Polymath but that he did have an answer to my question about their topological methods, which is that the topological concepts they were using were intrinsically not strong enough to bring the bound down to *n* + 1, let alone *n*. It might nevertheless be valuable to understand exactly how far we can go by thinking about independent partial transversals. Ron Aharoni and Jonathan Farley both had interesting ideas along these lines; rather than reproduce them here, let me just say that you can find Aharoni’s comment (under the previous blog post) by searching for “Vizing” and Farley’s comment by searching for “Mirsky.”

Idea 2 was to look for additional obstructions to natural strengthenings of Rota’s Basis Conjecture, by computationally searching for counterexamples that arise if the number of columns is smaller than the number of rows. Luke Pebody started such a search but reported a bug. I still believe that this computational search is worth doing, because I suspect that any proof that Rota’s Basis Conjecture holds for all matroids is going to have to come to grips with these counterexamples.

Note that if we are interested just in vector spaces, we could do some Gröbner basis calculations. I am not sure that this would be any less computationally intensive than exhausting over all small matroids, but it might reveal additional structure that is peculiar to the vector space case.

There has been minimal progress in this (admittedly vague) direction. I will quote Ellenberg’s initial thoughts: “If you were going to degenerate, what you would need to do is say: is there any version of this question that makes sense when the basic object is, instead of a basis of an *n*-dimensional vector space *V*, a 0-dimensional subscheme of *V* of degree *n* which is not contained in any hyperplane? For instance, in 2-space you could have something which was totally supported at the point (0,1) but which was “fat” in the horizontal direction of degree 2. This is the scheme *S* such that what it means for a curve *C* to contain *S* is that *S* passes through (0,1) and has a horizontal tangent there.”

Let me also mention that Jan Draisma sent me email recently with the following remarks: “A possible idea would be to consider a counterexample as lying in some suitable equivariant Hilbert scheme in which being a counterexample is a closed condition, then degenerate to a counterexample stable under a Borel subgroup of *GL _{n}*, and come to a contradiction. ‘Equivariant’ should reflect the action of

Now let me move on to other ideas suggested in the comments. There were several thoughts about the Alon–Tarsi Conjecture that the Alon–Tarsi constant *L _{n}*

Σ_{A} (–1)^{σ(A)} det(*A*)^{n},

where the sum is over all zero-one matrices and *σ*(*A*) is the number of zero entries in *A*. This formula suggests various possibilities. For example one could try to prove that *L _{n}*

Another possibility, suggested by Gil Kalai, is to consider a Gaussian analogue. Instead of random zero-one matrices, consider random Gaussian matrices and try to understand the Hermite expansion of det^{n}, in particular showing that the coefficient corresponding to all ones is nonzero. This might be easier and might give some insight.

Note also that in the comments to my MathOverflow post, Abdelmalek Abdesselam proposed an analogue of the Alon–Tarsi conjecture for odd *n*. I do not think that many people have looked at this.

Some generalizations and special cases of the conjecture were mentioned in the comments. Proving the conjecture for graphic matroids or binary matroids would be an enormous advance. There is a generalization due to Jeff Kahn, in which we have *n*^{2} bases *B _{ij}* and we have to pick

Juan Sebastian Lozano suggested the following reformulation: Does there exist a group *G* such that *V* is a representation of *G* and there exists *g _{i}* ∈

span{*g*^{0}*b*, …, *g*^{n – 1}*b*} = *V*

where *g ^{i}* =

Fedor Petrov mentioned a theorem by him and Roman Karasev that looks potentially relevant (or at least the method of proof might be useful). Let *p* be an odd prime, and let *V* be the **F**_{p}-vector space of dimension *k*. Denote *V*^{*} = *V* \ {0} and put *m* = |*V*^{*}|/2 = (*p ^{k}* – 1)/2. Suppose we are given

(*v*_{11}, …, *v*_{1k}), (*v*_{21}, …, *v*_{2k}), …, (*v*_{m1}, …, *v*_{mk}).

Then there exist pairwise distinct *x*_{1}, …, *x _{m}*,

Gil Kalai notes that the Alon–Tarsi conjecture is related to the coloring polynomial of a graph and asks if we can learn anything by considering more general polynomials such as

Π {(*x _{i}* –

where the *λ _{e}* are weights associated to the edges

This post tentatively kicks off Polymath 12 on Rota’s basis conjecture.

I proposed Rota’s basis conjecture as a possible Polymath project on MathOverflow last year. If you have not read my proposal, I strongly recommend that you read it now, because in it, I sketched some reasons why I thought this would make a good Polymath project, as well as some known partial results and potential avenues for progress.

Recently, I emailed several likely participants, and a number of them responded enthusiastically, enough in my opinion to warrant an attempt to start a Polymath project. I have discussed the possibility with the polymath blog admins and since I do not have a blog of my own, they have generously agreed to host the project here on the polymath blog itself. This means that you should comment freely in the comments section below.

Rota’s basis conjecture states that if *B*_{1}, *B*_{2}, …, *B _{n}* are

1. the *n* vectors in row *i* are the members of the *i*th basis *B _{i}* (in some order), and

2. in each column of the matrix, the *n* vectors in that column form a basis of *V*.

If this project gets enough momentum to be formally declared “Polymath 12” then it will be important to give a thorough summary of what is already known, and to lay out in some detail all the promising directions. However, at this early stage, I think that it is important to have some “quick wins” to get things moving, so I would like to present a couple of new ideas that I think could lead to some new partial results quickly, and also invite others to present their own ideas.

The first idea is to extend an old result of Aharoni and Berger that I think has not received too much attention from others. Suppose we have two matroids on the same ground set *E*. By definition, a *common independent set* is a subset of *E* that is independent in both matroids. We can try to partition *E* into a disjoint union of common independent sets, and can ask the question, what is the smallest number *β* of common independent sets that we need?

Here is the relation to Rota’s basis conjecture. The ground set *E* has *n*^{2} elements, and one of the matroids is defined by the given set of *n*^{2} vectors (here, if the same vector appears in more than one basis, we treat the different occurrences as being distinct). The second matroid is the so-called *transversal matroid* whose independent sets are precisely those subsets of *E* that contain at most one element from each *B _{i}*. From this point of view, Rota’s basis conjecture says that

Aharoni and Berger have proved a general theorem about matroids that implies, in the specific case of Rota’s basis conjecture, that *β* ≤ 2*n*. They also have a very general conjecture on matroids that would imply that *β* ≤ *n* + 1 for Rota’s basis conjecture.

Let me now make the simple observation that it is easy to prove directly that *β* ≤ 2*n* – 1 for Rota’s basis conjecture. We begin with a lemma. Suppose we have a matroid and suppose that *I*_{1}, …, *I _{n}* are independent sets with |

Returning to the setup for Rota’s basis conjecture, we can write out the *n*^{2} given vectors in a grid with the elements of *B _{i}* in row

So the first question, which I don’t think has been looked at much and which hopefully should not be too hard, is:

**Can we show that β ≤ 2n – 2?**

In one of my papers I introduced the idea of looking for certain kinds of obstructions to an inductive proof of the conjecture. Specifically, suppose that instead of *n* bases, we are given *n* independent sets *I*_{1}, …, *I _{n}*, each of size

The last idea I want to present here is very vague. It is inspired by a paper by Ellenberg and Erman that I recently learned about. The result of the paper itself isn’t relevant, but I thought that the method might be. Roughly speaking, they reduce a certain combinatorial problem involving points and lines in a vector space to a “degenerate” case that is more tractable. Since various “degenerate” cases of Rota’s basis conjecture are known, perhaps the same idea could be applied to extend those degenerate cases to more cases.

As an example of a known degenerate case, let us first generalize Rota’s basis conjecture slightly as follows. Let us allow the vector space *V* to have some dimension *d* > *n*, and instead of *n* bases, let us take any *n* independent sets *I*_{1}, …, *I _{n}*, each of size

Let me end this initial blog post here, with just one further comment that a couple of people that I have communicated with recently have some other concrete ideas that we can sink our teeth into immediately. I am going to invite them to explain those ideas in the comments to this blog post.

1) The LogRank conjecture. Proposed by Arul.

2) The circulant Hadamard matrix conjecture. Proposed by Richard Stanley.

3) Finding combinatorial models for the Kronecker coefficients. Proposed by Per Alexandersson.

4) Eight lonely runners. Proposed by Mark Lewko.

5) A problem by Ruzsa:

Finding the slowest possible exponential growth rate of a mapping from **N** to **Z** that is not a polynomial and yet shares with (integer) polynomials the congruence-preserving property *n−m∣f(n)−f(m)*. Proposed by Vesselin Dimitrov.

6) Finding the Matrix Multiplication Exponent ω. (Running time of best algorithm for matrix multiplication.) Proposed by Ryan O’Donnell.

7) The Moser Worm problem and Bellman’s Lost in a forest problem. Proposed by Philip Gibbs.

8) Rational Simplex Conjecture ( by Cheeger and Simons). Proposed by Sasha Kolpakov.

9) determinants for 0-1 matrices Proving that for every integer with there is an

0-1 matrix matrix whose determinant equals . Proposed by Gerhard Paseman.

10) Proving or disproving that the Euler’s constant is irrational. Proposed by Sylvain JULIEN.

11) The Greedy Superstring Conjecture. Proposed by Laszlo Kozma.

12) Understanding the behavior and structure of covering arrays. Proposed by Ryan.

13) The group isomorphism problem, proposed by Arul based on an early proposal by Lipton.

14) Frankl’s union closed set conjecture (Proposed by Dominic van der Zypen; Also one of the proposals by Gowers in this post). (Launched)

15) Komlos’s conjecture in Discrepancy Theory. Proposed by Arul.

16) Rota’s Basis Conjecture. Proposed by Timothy Chow.

17)+18) I contributed two proposals. One in ANT is to A problem in ANT show that

$latex 2^n+5$ is composite for almost all positive integers . (Might be too hard.) Another is to prove a remarkable combinatorial identity on certain Permanents.

19) Real world applications of large cardinals Proposed by Joseph van Name. There were a few more proposals in comments.

20) A project around a cluster of tiling problems. In particular: Is the Heech number bounded for polygonal monotiles? Is it decidable to determine if a single given polygonal tile can tile the plane monohedrally? Even for a single polyomino? Proposed by Joseph O’Rourke

Here is the link to a mathoverflow question asking for polymath proposals. There are some very interesting proposals. I am quite curious to see some proposals in applied mathematics, and various areas of geometry, algebra, analysis and logic.

The MIT PRIMES program and the Art of Problem Solving are planning to run a “Crowdmath” project for high school students with advanced mathematical backgrounds, based on the polymath approach to mathematical research. The project, which officially starts on March 1, will be devoted to original research on a mathematics problem to be specified at the time of the project (but judging from the reference material provided, it will probably involve the combinatorics of 0-1 matrices). Participation is open to all high school students (though they will need an Art of Problem Solving account).

I am posting this proposal on behalf of Dinesh Thakur.

Let be the ring of polynomials over the finite field of two elements, and let

be the set of irreducible polynomials in this ring. Then infinite series such as

and

can be expanded as formal infinite power series in the variable .

It was numerically observed in http://arxiv.org/abs/1512.02685 that one appears to have the remarkable cancellation

and

For instance, one has

and all other terms in are of order or higher, so this shows that has -valuation at least 3. Similarly, if one expands the first sum for all primes of degree (in ) up to 37, one obtains (the calculation took about a month on one computer), implying that the -valuation of the infinite sum is at least 38; in fact a bit of theory can improve this to 42. (But we do not know whether this 42 is the answer to everything!).

For the second sum, calculation for degrees up to 28 shows that the difference between the two sides has -valuation at least 88.

The polymath proposal is to investigate this phenomenon further (perhaps by more extensive numerical calculations) and supply a theoretical explanation for it.

Background links:

- The paper http://arxiv.org/abs/1512.02685 where these (and many more guesses of this type) are given with some background on zeta deformation etc, and
- http://www.math.rochester.edu/people/faculty/dthakur2/primesymmetryrev.pdf where the updated version is and will be maintained.

Below the fold is some more technical information regarding the above calculations.

This post is meant to propose and discuss a polymath project and a sort of polymath project.

One of the interesting questions regarding the polymath endeavor was:

Can polymath be used to develop a theory/new area?

My idea is to have a project devoted to develop a theory of “convex hulls of real algebraic varieties”. The case where the varieties are simply a finite set of points is a well-developed area of mathematics – the theory of convex polytopes, but the general case was not studied much. I suppose that for such a project the first discussions will be devoted to raise questions/research directions. (And mention some works already done.)

In general (but perhaps more so for an open-ended project), I would like to see also polymath projects which are on longer time scale than existing ones but perhaps less intensive, and that people can “get in” or “spin-off” at will in various times.

The Riemann hypothesis is arguably the most famous open question in mathematics. My view is that it is premature to try to attack the RH by a polymath project (but I am not an expert and, in any case, a project of this kind is better conducted with some specific program in mind). I propose something different. In a sort of polymath spirit the project I propose invite participants, especially professional mathematicians who thought about the RH over the years, to share their thoughts about RH.

Ideally each comment will be

1) One or a few paragraphs long

2) Well-thought, focused and rather polished

A few comments by the same contributors are also welcome.

To make it clear, the thread I propose is **not** going to be a research thread and also **not** a place for further discussions beyond some clarifying questions. Rather it is going to be a platform for interested mathematician to make statements and expressed polished thoughts about RH. (Also, if adopted, maybe we will need a special name for such a thing.)

____________________

This thread is **not launching** any of the two suggested projects, but rather a place to discuss further these proposals. For the second project, it will be better still if the person who runs it will be an expert in the area, and certainly not an ignorant. For the first project, maybe there are better ideas for areas/theories appropriate for polymathing.