What to do now that Lusztig's and James' conjectures have been shown to be false?

Question

Lusztig and James provided conjectures for dimensions of simple modules (or decomposition numbers) for algebraic groups and symmetric groups in characteristic $p$. These conjectures have been considered almost certainly true and have guided a lot of the research in these areas for a long time. A new preprint by Geordie Williamson, (with a classily understated title: "Schubert calculus and torsion") shows that the Lusztig conjecture is false (and therefore that James' conjecture is also false).

Amongst other things, this certainly implies that the existing cases in which the conjectures have been proved become more interesting (very large $p$ for Lusztig's, RoCK blocks and certain defects for James').

But my question is: what next? Do we just accept that we'll only understand algebraic groups in very large characteristic? Do we direct focus on non-abelian defect blocks for symmetric groups?

Or... there's a lovely conjecture due to Doty which (though less explicit than Lusztig's conjecture) could, in principle, give a character formula for the characters of simple modules for $GL_n$ and hence symmetric groups. It states that:

The modular Kostka numbers are defined as follows: $K′= [Tr^λ(E) : L(μ)]$, for $Tr^\lambda(E)$ the truncated symmetric power and $L(\mu)$ the irreducible polynomial $GL_n$-module of highest weight $\mu$. Then Doty’s Conjecture states that the modular Kostka matrix $K′ = (K′_{\mu,\lambda} )$, with rows and columns indexed by the set of all partitions $\lambda$ of length $\leq n$, and bounded by $n(p−1)$ (fixed in some order), is non-singular for all $n$ and all primes $p$.

Could this conjecture be the new "big problem" for algebraic and symmetric groups in positive characteristic? Are there any other conjectures out there of a similar flavour?

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References

G. Williamson, Schubert Calculus and Torsion. http://people.mpim-bonn.mpg.de/geordie/Torsion.pdf

Doty, S., Walker, G., Modular Symmetric Functions and Irreducible Modular Representations of General Linear Groups, Journal of Pure and Applied Mathematics, 82, (1992), 1-26.

See also page 105 of S. Martin "Schur algebras and Representation theory".

Answer 1

The questions raised here will probably need some substantial research papers to answer, inventing new approaches and methods. In any case, the question of what to do about "small" primes has been around for decades without any clear program emerging. Three logical outcomes are possible: these range from least satisfactory (no general method, just a lot of ad hoc case-by-case and prime-by-prime results) to highly satisfactory (a single all-encompassing theoretical framework, though requiring recursive calculations as at present). The third possibility lies of course somewhere in between. Meanwhile maybe I can fill in a little more of the background, community-wiki style.

The general problem is to understand the $p$-modular representation theory (mainly finite dimensional) of a (simple or perhaps reductive) algebraic group $G$, in conjunction with the study of its Lie algebra $\mathfrak{g}$ and various finite subgroups of $G$ (Chevalley or twisted groups). Historically, the search for simple modules has been a natural starting point, but there are many other questions involving indecomposables, projectives, blocks, extensions, cohomology, etc.

In the narrower case at hand, the focus is on the interaction of modular representations of general (or special) linear groups and symmetric groups. But one might prefer to work in the full generality of simple algebraic groups in spite of the lesser symmetry in some root systems. (Here Jantzen's 2003 edition provides most of the needed foundations.) At the risk of oversimplification and with apologies to those whose work is slighted, I'll sketch briefly how the ideas have evolved:

(1) In the early period (late 1950s into 1960s), Chevalley parametrized the simple modules $L(\lambda)$ for $G$ as in the classical theory by dominant integral weights $\lambda$ (realizing them in effect as submodules of the global sections of suitable line bundles on a flag variety). Further study by Curtis and then Steinberg related these modules to those for $\mathfrak{g}$ when the weights are "$p$-restricted" and with those for related finite groups of Lie type. Here Steinberg's twisted tensor products account for arbitrary weights, while there is more emphasis on realizing the $L(\lambda)$ as quotients of modules obtained from characteristic 0 by reduction mod $p$ (later called Weyl modules). The two realizations are essentially dual, a consequence of Kempf's Kodaire-type vanishing theorem for dominant line bundles proved in the 1970s.

(2) In the middle period (1970s), more details and examples were filled in, along with some general theory which often imitated the infinite dimensional representation theory of Lie algebras rather than Cartan-Weyl theory. At first some people had expected closed formulas like Weyl's for characters or weight multiplicities. Instead a version of Harish-Chandra's action of the Weyl group on weights (shifted by $\rho$) got combined with reduction mod $p$. In my emphasis on $\mathfrak{g}$ I had to omit primes dividing the index of connection, but soon Jantzen developed much better versions for $G$ and Andersen removed conditions on $p$ for the group notion of "linkage".

My approach yielded an early form of BGG reciprocity for $\mathfrak{g}$ but overlooked the appearance of an affine Weyl group $W_p$ relative to $p$ (for the Langlands dual root system). That was developed by Verma around the time of the 1971 Budapest summer school on Lie groups. He also conjectured that most of the theory should be independent of the prime $p$. Improved results and examples by Jantzen and Andersen in the 1970s were complemented by cohomology results of Cline-Parshall-Scott and others. The subject became broader and more active, but still lacked a good conjecture on the character of $L(\lambda)$. (Jantzen did however realize that a solution in characteristic $p$ would contain a solution of the hard open problem for Verma modules in characteristic 0.)

(3) Initiating the modern period, the landmark 1979 paper by Kazhdan-Lusztig on Hecke algebras and Coxeter groups, with its explicit conjecture on the composition factor multiplicities of Verma modules, led Lusztig to a parallel conjecture for Weyl modules in characteristic $p$. Here he recognized the need to avoid "small" $p$, which has continued to be a source of concern in the question asked here. But the main breakthrough was the realization that Kazhdan-Lusztig polynomials for an affine Weyl group (which is a Coxeter group) should supply key multiplicities. It took many years for a partial proof to be developed by Andersen-Jantzen-Soergel, which used an indirect comparison with quantum groups at a root of unity and left bounds on $p$ uncertain. (Soergel's former students Fiebig and Williamson have gone further.)

Playing off general linear and symmetric groups is especially tricky for small primes, since even the optimistic lower bound on $p$ given by the Coxeter number gets arbitrarily large here. This difficulty has been appreciated by those working in the modular theory of symmetric groups. In the algebraic group situation, the built-in problem with reliance on the single affine Weyl group $W_p$ has been the involvement of higher powers of $p$ when weights are relatively small. More systematic study of small primes is needed here, to create a database. But even Jantzen's early examples are instructive. For instance, in type $B_2$ when $p=2$, one fundamental weight reflects to the lower 0 weight across a $p$-hyperplane which is also a $p^2$-hyperplane. Relative to $p$, the weight is singular, but not relative to $p^2$. This suggests the interaction of a hierarchy of affine Weyl groups for increasing powers of $p$. How complicated will this be to formulate? And can it be enough to predict all character formulas? (Maybe not.)

Answer 2

Some comments (most are not original):

1) even when Lusztig's conjecture holds, there is a gap in our understanding: we only have a "direct" character formula for weights in both the principal block and fundamental box (actually for weights with 2 "p-adic digits"). To get character formulas in general we have to expand our weight p-adically, and use Steinberg's tensor product theorem. This is much more computationally intensive than what happens in "normal" KL type situations, where one gets the answer reasonably directly once one has calculated Kazhdan-Lusztig polynomials.

2) In this sense, Lusztig's conjecture for quantum groups is the perfect conjecture. There is no fundamental box restriction, and no $p \ge h$. (There are some restrictions, however these are believed to be an artefact of the proof.) Also, for singular weights (and even when there is no regular weight) one gets the answer from parabolic KL polynomials.

3) The absence of a conjecture for $p < h$ has always been a real problem and shouldn't be ignored. For example, if one is interested in tilting modules for $GL_n$ one can (thanks to Donkin) translate this into a question about the standard multiplicity in a projective module for $GL_m$ with $m$ usually (much) bigger than $n$. Even if you $p$ was "reasonable" (i.e. $p \ge n$) then it is unlikely that $p \ge m$. That is, if one defines "reasonable" to be $p \ge h$ then a natural and important question for reasonable $p$ leads quickly to a natural question for unreasonable $p$.

4) One can ask what constitutes an answer. KL polynomials are extremely complicated things, and yet we feel this is an answer. I guess the key property of KL polynomials is "computable by a recursive algorithm which does not involve doing serious linear algebra". (Serious linear algebra: computing invariant forms and their ranks.) Perhaps we will have to weaken what we consider an answer.

5) It doesn't seem crazy to expect that the $p$-canonical basis gives character formulas for all $p$ in a uniform way. (I.e. no $p \gt h$ restriction, and also working for singular weights). Soergel has a result in this direction, and the natural generalisations of his statement seem to match the little that is known. The $p$-canonical basis is computable (using the Braden-MacPherson algorithm (Fiebig) or "Soergel calculus"). However it is much more complicated to compute than the KL basis, and involves serious linear algebra. Perhaps there is a rich combinatorics underlying it? Certainly this combinatorics includes the case of KL polynomials, but is more complicated. Time will tell if we can say anything, although the few examples that I have computed aren't necessarily a source of optimism.

6) A metaphor: in number theory one has number fields and function fields. Deep and difficult statements about numbers often become simple and comprehensible when translated into function fields. Perhaps we should think about quantum groups and algebraic groups in the same way. Perhaps for large $n$ and not too large $p$ there are serious arithmetical issues to be overcome in order to understand the difference between the quantum group and the algebraic group. The same comments apply to the representations of the symmetric group in char $p$ versus representations of the Hecke algebra at a $p^{th}$ root of unity.

7) (Following on from 6). Kazhdan-Lusztig theory for the quantum group takes place on the affine flag variety or affine Grassmannian. This is a function field object (built using $F_q((t))$). It is interesting to ask if there is an affine Grassmannian or affine flag variety built using $\mathbb{Q}_p$. Lusztig has done such a thing in his recent papers "Unipotent almost characters of simple p-adic groups". Interestingly, these objects do not exist in the category of varieties. Instead one has to work in a slightly larger category where one has inverted a lift of the Frobenius.

8) At the heart of these questions are difficult algebro-geometric ideas (hard Lefschetz, Hodge-Riemann bilinear relations, Deligne's weights), but now with coefficients in positive characteristic. These are the ideas which make Kazhdan-Lusztig theory work, and so it is natural to study how they fail when trying to understand what the replacement should be. For example, I do not know of any results that control the failure of the hard Lefschetz theorem modulo $p$. Of course this is very hard, but perhaps very interesting too. In this direction it seems natural to revisit Deligne's proof of hard Lefschetz using Lefschetz pencils and semi-simplicity of monodromy. This seems interesting because it avoids positivity considerations (e.g. Hodge-Riemann bilinear relations) and hence makes sense in positive characteristic. What monodromy groups occur for IH of Schubert varieties? Can one use the modular representation theory of these monodromy groups to understand what is going on?

Answer 3

Geordie made some excellent points, beyond my earlier community-wiki comments, but maybe it's worth spilling more pixels to emphasize another important but often neglected viewpoint: Lusztig's 1980 Generic Decomposition Conjecture (GDC), closely related to what is usually called the Lusztig Conjecture (LC). Here is a brief overview of the essential literature:

In a 1977 paper (J. Algebra 49), Jantzen worked out some ideas about "generic decomposition" of Weyl modules in sufficiently large characteristic $p$. This reveals patterns of composition factors (interchangeable in a sense for different alcove types) for all highest weights in general position in the lowest $p^2$-alcove for an affine Weyl group $W_p$ relative to $p$ of Langlands dual type. (For example, in type $B_2$ he finds generically 20 composition factors with multiplicity 1, whereas for $G_2$ there are 119 composition factors with multiplicity ranging from 1 to 4.) He later proved existence more efficiently in a 1980 Crelle J. 317 paper, also in German.

Jantzen's patterns look rather unpredictable, but a "dual" version (which I observed at first indirectly via the finite groups of Lie type) shows symmetry around a special point for $W_p$. From these generic patterns Jantzen also showed how to derive all patterns for arbitrary weights in the region. But the underlying assumption is always that $p$ is at least the Coxeter number $h$, to ensure existence of weights inside $p$-alcoves and permit use of translation functors. To get generic patterns, $p$ of course has to be even bigger in general.

In his write-up of a survey of problems at the 1979 AMS summer institute in Santa Cruz, published in PSPM (1980), Lusztig first stated LC with the hypothesis $p \geq h$ and the stipulation that the dominant weight involved should lie inside an alcove within the "Jantzen region" in the lowest $p^2$-alcove for $W_p$; then the irreducible character should be a $\mathbb{Z}$-linear combination of Weyl characters with coefficients up to sign given by specializations at 1 of Kazhdan-Lusztig polynomials for the (abstract) affine Weyl group.

Eventually Andersen-Jantzen-Soergel proved this (via the successful quantum group version) for "sufficiently large" $p$, after which Fiebig derived an explicit but huge lower bound on $p$. As Williamson has observed, there are serious problems about smaller $p \geq h$.

In 1980 a more technical paper by Lusztig (in Advances 37) laid out a generic version of Jantzen's ideas. Here one has the symmetric dual patterns of alcoves in the abstract affine Weyl group, with polynomial entries in $q$ given by inverse K-L polynomials. His Remark 1.9 is the conjecture that for $q=1$ one should recover Jantzen's patterns, for $p$ "sufficiently large".

In a 1985 paper, S.I. Kato (Advances 60) calls this the GDC and proves in Thm. 5.6 that for "sufficiently large" $p$ it is equivalent to the LC. He builds on a previously accepted but later published 1986 paper by Andersen (*Advances 60) which studies inverse K-L polynomials in more detail.

With this background, it makes sense to distinguish three ranges for $p$: always we need $p \geq h$ (which is a serious limitation for type $A_n$ and related symmetric group problems), whereas for "very large" $p$ both LC and GDC are simultaneously true. For a range of "intermediate" $p$ and for $p<h$ there is serious uncertainty about what if anything to conjecture. Taking GDC as the main focus, I suggest that one try to bound $p$ below as efficiently as possible so that all of Janzten's (dual) generic decomposition patterns around some special point lie inside the Jantzen region of the dominant Weyl chamber. In view of the equivalence of GDC and LC for "sufficiently large" $p$, and Verma's older conjecture that the essential data should be independent of $p$, this might lead to a better lower bound on $p$ based on root system constants such as the Weyl group order $|W|$. (Unless this conflicts with Williamson's estimates.)

It's clear that the largest generic pattern will involve at least $|W|$ copies of the "box" (Lusztig's term) at the special point, while the box itself contains $|W|/f$ of the $p$-alcoves with $f$ the index of the root lattice in the weight lattice. But typically there will be more $p$-alcoves involved, containing non-restricted weights below restricted ones (as in $G_2$ etc.). Since the number of $p$-alcoves in the lowest $p^2$-alcove is only $p^\ell$ (with $\ell$ the rank), we are already forced to make $p$ rather large in order to get GDC.