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".



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


