A Record Is Not a Trajectory

On 17 August a ten-author paper landed on arXiv announcing a new world record for ω, the exponent of matrix multiplication: ω < 2.371177, down from 2.371339. The improvement is 0.000162. The discussion threads did the customary joke — galactic algorithm, nobody will ever multiply a matrix that big — and moved on. The joke is fine, but it misses the more interesting thing, which is that this number series has a shape, and the shape says the current program is finished. Line up the record since Coppersmith and Winograd’s 1990 bound of 2.375477. Le Gall 2014: 2.3728639. Alman–Vassilevska Williams 2020: 2.372860. That is six years of work by two of the best people in the field for an improvement of under four millionths. Then Duan–Wu–Zhou 2022 jumped to 2.371866 — a gain of 0.000994, roughly 250× the previous decade’s total. Then 2.371552 (2023), then 2.371339 (2024), now 2.371177. Look at the gains after that 2022 jump: 0.000994, 0.000314, 0.000213, 0.000162. Each gain as a fraction of the one before it runs 0.32, 0.68, 0.76 — a geometric decay tightening toward something like 0.75. Sum the remaining tail at that rate and about 0.0004 of headroom is left. Be generous, assume the ratio is really 0.95 with a long fat tail, and you get 0.003. Either way this line terminates somewhere around 2.3703–2.3708, and it will take a decade of papers to crawl the last thousandth.

That limit is not near 2. It is not even near the barrier this field already proved for itself — and the history of how one such barrier fell is the whole lesson. In 2014 Ambainis, Filmus and Le Gall proved limitations of the Coppersmith–Winograd method: analyzing higher tensor powers of the CW identity in the then-standard way could never beat 2.3725, and a wide class of variants could never beat 2.3078. The first of those barriers has since fallen, and Duan–Wu–Zhou say so in their own abstract, in as many words: “Our result breaks the lower bound of 2.3725 in [Ambainis, Filmus & Le Gall 2015] because of the new method for analyzing component (constituent) tensors.” The barrier did not fall to a better optimizer. It fell because someone noticed that analyzing the eighth power of the CW tensor incurs a specific accounting error — “combination loss” — and invented asymmetric hashing to partially recover it. A new object of analysis, not a better search over the old one.

Which is exactly why I would bet against the current line. Read the new record’s own abstract: it reformulates the optimization problem, applies modern numerical methods to it, and refines the result with an automated search. Every one of those improves how well the existing framework is solved, not what the framework is — and that is precisely the variable that saturates. The 2014→2020 dead zone is what a saturated framework looks like from the inside: real mathematicians working hard and extracting four millionths, because the loss was in the formulation, not in the arithmetic. Meanwhile the barriers that remain are not close. Ambainis–Filmus–Le Gall’s 2.3078 sits 0.063 below the current record — around 150 papers away at the present decay rate, which is to say unreachable by this method. And Josh Alman proved in 2018 that the Universal Method — which subsumes Strassen’s laser method and the Cohn–Umans group-theoretic approach, essentially everything anyone knows how to do — applied to any Coppersmith–Winograd tensor CW_q cannot yield a bound better than 2.16805. Perfect play with the entire known toolbox, against the tensor the field has been mining since 1990, stops 0.168 short of the conjectured answer.

So the honest reading of ω < 2.371177 is not “we’re getting closer to 2.” It is: we are finishing our measurement of one 1990 construction. The exponent race has quietly become a very expensive, very precise instrument for reading off the ceiling of the Coppersmith–Winograd tensor, and the number that keeps improving is a property of that tensor rather than of the multiplication problem. The bet, then: no bound below 2.370 will come from optimizing the present framework, and whatever paper does break 2.370 will announce a structural reframing in its title — a different tensor, or a different notion of degeneration — the way Duan–Wu–Zhou did. Alman’s paper even hands the field the right search procedure, almost as an aside: he proves the laser method is complete, meaning that when it applies to a tensor T it achieves ω = 2 if and only if the far more general Universal Method could. The laser method is therefore a screening test. Point it at a candidate tensor and it tells you whether that tensor is worth years of your life. Which suggests the productive question stopped being “how low can we push the bound?” some time around 2022, and became “which tensor should we be mining instead?” Nobody has a good answer. That, and not the sixth decimal place, is where ω = 2 is hiding.