This is the summary of our algorithmic-contribution write-up; the full 45-page PDF (12 figures) is attached. Referenced graded submission: #326024 (raw final-layer MSE 2.5651×10⁻⁶, multiplier 0.1132, adjusted score 2.9045×10⁻⁷, graded 08-08 under the current evaluator). Cost-model note: adjusted scores are only comparable within one evaluator configuration, and it moved three times in the last three weeks (flopscope 0.9.0 dtype pricing on 07-23, 0.10.0 plus the re-evaluation announced on 08-03, and the one-core participant runtime in the same update). Numbers here are quoted against the current configuration unless a version is stated; the PDF was finalized under 0.9.x and states its own version context — its raw (unadjusted) MSEs are unaffected, and where an adjusted score differs the version is named.
Disclosure. This work was AI-assisted (Claude, Anthropic). The model proposed and ran experiments, wrote the code, and drafted the documents; a human directed the research, chose which threads to pursue, and approved every submission. The write-up’s §11 gives the full disclosure. Where we are uncertain why something works we say so explicitly rather than rationalizing it — §9’s negative results include several cases where our own earlier explanation turned out to be wrong, and they are reported as such.
The estimator in one paragraph
Skew-augmented Gaussian-closure covariance propagation (a third-cumulant Gram–Charlier ReLU closure with an off-diagonal Mehler co-skewness term, plus an offline-trained per-layer mean correction) fused per neuron with a Monte-Carlo pass by inverse-variance weighting — and, the piece that carries the score, a mid-network activation used as a multivariate control variate for the scored final layer, with the analytic propagation supplying the control’s mean.
What we would like judged
1. The intra-network control variate, and the structural observation behind it. “Variance reduction is unavailable at depth 32” is a statement about input-space samplers, and it says nothing about a control built from the network’s own state. We want to be precise about the input-space part, because our own earlier record of it was wrong and we corrected it: stratification and lattice/QMC do deliver a real raw variance reduction (≈1.4×) at depth 32 — what they do not deliver is score, because behind the control variate below their gain is absorbed. The two are substitutes, not complements, and we measured the fused difference between Latin-hypercube and i.i.d. sampling to be indistinguishable from zero. So the honest form of the folklore is “input-space variance reduction does not survive fusion”, not “it does not survive depth”. A mid-layer activation is already computed by the Monte-Carlo pass (no second forward pass; the marginal cost is one ridge solve) and the analytic chain already supplies its mean. Control depth is a bias/correlation trade with a middle optimum: layer 1 has an exact control mean but barely correlates with the deep readout (~1.2×); an oracle penultimate control would give ~110× but its analytic mean is maximally drifted, so deployably it is worse than plain MC. Layers ≈5–8 give a leak-free 2.4×. Our own earlier control-variate probe had dismissed the whole lever by testing only those two useless endpoints — the sweet spot is the finding.
The sharpening matters more than the number: the deployable variance reduction is bounded by the analytic mean’s fidelity, so what looks like a variance-reduction gap between competitors is an analytic-bias gap in disguise. We confirmed this from three directions (structured Jacobian controls, exactly-unbiased controls, and nonlinear/quadratic controls all raise raw variance reduction while leaving the fused score untouched), and it also explains the leaderboard’s rank ordering, which tracks the vs-sampling factor rather than raw MSE.
Since Phase 1 closed, two disclosures in this forum describe the same lever from independent directions — an inter-layer fluctuation control in the post-mortem thread (#18152), and the observation in #18147 that exact Gaussian structure “pays when subtracted (as a control) and fails when predicted (as an estimator)”, which is this section’s thesis in one sentence. Our graded trail for the control variate begins 21 June (#311555); we read the convergence as evidence the observation is structural rather than incidental, and the bias-bound sharpening above as the part our measurements add to it.
2. The wall, stated mechanistically — and ARC’s own published method measured against it. Mean propagation through a critically-initialized deep ReLU network is a unit-gain feedback loop (∂M₁/∂μ ≈ 1, measured slightly above 1): per-layer closure error accumulates undamped over 32 layers, and once μ has drifted, a per-step closure improvement is applied to the wrong input and cancels out. That single loop predicts a family of otherwise puzzling results — better-shaped closures with the same moments do nothing, adding moments actively hurts, and a learned per-layer operator that is 40% more accurate one-step diverges by +12,000% when iterated (accuracy ⊥ stability; the Gaussian closure’s virtue is that it is a stable iterate, not an accurate one).
Breaking the loop is mathematically three exits — an unbiased closure, a contracting propagator, or truth injection — and we measured all three closed. Most relevant to the organizers: we ported and measured ARC’s own published cumulant propagation (arXiv:2605.05179) across a depth × order grid (depths 4/8/16/32 × k=1…4, reference implementation used as an oracle). At depth 4 it behaves exactly as published (k=3 reaches the perfect-three-moment frontier). At depth 32 it does not: the k=3-over-k=2 gain collapses 46× → 55× → 8× → 1.3× as depth doubles, k=3 error accelerates ×3.1 → ×7.9 → ×11.8 per depth doubling, and k=4 — which does converge where it is computable — memory-walls at exactly the depths that need it (61.5 GB at depth 16, 122 GB at depth 32). This is a direct measurement of the depth-scaling question the paper leaves open, and it is a counterexample to the position stated at the townhall that higher-order Edgeworth divergence is a width-16 problem and a non-blocker at width 256: the divergence we measure is along depth, at width 256.
3. A measured negative map (~20 named, committed probes). Each verdict is end-to-end (score or held-out MSE), not per-step: characteristic-function propagation, randomized-truncation unbiased analytic, particle/cubature, off-diagonal fourth cumulants (built, closed form derived and MC-validated, then measured harmful), learned autoregressive operators, MLMC, cost-asymmetric unbiased controls, nonlinear controls, mid-depth re-anchoring, learned 2-index propagation trained on the public higher-moment dataset, per-MLP adaptive sample counts. Two patterns recur and are, we think, the transferable lessons: transfer traps — six independent cases where an apparent gain evaporated out of sample or under more replicates, plus one (an anisotropic ridge on the control) where the population fit transferred cleanly and still failed to monetize, so clean transfer is necessary and not sufficient — and projection-orientation: reducing ‖δ‖ by 23% increased the quantity the fusion actually spends (‖Bᵀδ‖) by 11%, because the fused estimator consumes a projection of the error, not its norm.
4. The compute bill’s composition is its own optimization axis. Above the multiplier floor the score is linear in effective compute, so with every statistical lever closed the remaining question is how the same computation is charged. Two exact, bit-identical-value cuts graded real (a Gram matrix spelled as a repeated-operand einsum bills at 0.502×; a second FLOP-composition bundle). One measured negative worth flagging: residual wall-time does not transfer — a −38% local / −26% proxy cut moved the grader 0%, its residual-time profile being machine-specific. We also audited the accounting for fairness and found no exploit available to us (98.0% of the referenced entry’s bill is rate-1 matmul/einsum).
The axis kept paying after the report was written. When flopscope 0.9.0 replaced the flat cost model with a dtype-aware one, our bill rose 7.1% at bit-identical predictions; propagating the analytic state in float32 recovered −4.06% and graded −3.2% (#318640). When 0.10.0 landed on 2026-07-30 and changed when a symmetry claim is honoured, the same float32 path turned out to be exactly immune — its billed FLOPs are unchanged to the integer, while the float64 formulation of the identical mathematics costs +3.5%. We had not anticipated that release; the immunity is a consequence of having moved the analytic tail off the contraction whose discount the patch invalidates. The 08-03 re-evaluation then confirmed this end-to-end on the grader: #318640’s raw MSE and billed FLOPs came back unchanged (its adjusted movement, +6.7%, is entirely the one-core runtime repricing residual wall-time, which hit every entry), while our own float64 formulations of the same mathematics additionally paid the predicted FLOP increase (+9.5–12.9% total). The identical file resubmitted under the current evaluator is the referenced entry, #326024. We report the sequence because it is the cleanest evidence we have for the section’s claim: on this benchmark, how the same arithmetic is spelled is a first-class part of the score, and it is measurable in advance.
5. Two harness findings the organizers may want (from adapting to the 0.9.x dtype-aware model, §9): flops.stats.norm.{pdf,cdf,ppf} return float64 for any input dtype, which silently re-promotes a float32 propagation at every layer — since this report was finalized (07-31), the same promotion has been independently reported (#18127, 08-04) and organizer-confirmed to affect all 24 flopscope.stats callables, which we take as corroboration rather than claim priority over; and — on 0.9.x specifically — the three-operand contraction einsum("ij,ia,jb->ab", cov, w, w) had its inferred symmetry validated numerically at atol=1e-6, which float32 cannot satisfy: entries (a,b) and (b,a) sum identical terms in different orders, so after ~19 layers of cancellation one public-mini MLP (#19) exceeded the tolerance and the raised error forfeited that entire MLP. A data-dependent failure invisible on whichever seeds a local bench happens to use — a single occurrence moved our 100-MLP proxy from 3.6×10⁻⁷ to 6.6×10⁻². We re-ran the exact failing configuration on 0.10.0 and it no longer fires (0 of 100 failed): that release stamps a symmetry claim with its buffer’s write count and voids it on write, so the inference — and with it the validation — no longer survives past the first layer of the propagation. The trap is closed as a side effect, but the shape of it seems worth recording: a numerically-validated inferred property turns a tolerance into a cliff, and the cliff is invisible until the data reaches it.
Where this leaves the gap
We can put a number on what we did not solve, using only public data. The public board’s top ranks are dominated by entries fitting the 50 public MLPs directly (final MSEs orders of magnitude below the exact-three-moment frontier; the organizers note in the 08-03 update that this is allowed but will not generalize to the private re-evaluation), so we compare only against entries that spend their budget through the instrumented path as we do — the ratio of mean per-MLP FLOPs to mean effective compute, both shown on every submission page, is ≈0.95–0.96 for them and 0.92 for ours (read 08-12 from the frozen final Phase-1 board). Those estimators run at raw final-layer MSE 1.6–2.0×10⁻⁷ while spending 45–69% of the budget. Our own aggregate bias floor, fitted from a sample-count sweep, sits at ≈7×10⁻⁷: ≈3.5–4.3× above their operating MSE. That single comparison explains why the heavy-compute road is closed to us specifically — six times our compute would land near 6×10⁻⁷ adjusted, twice as bad as our deployed operating point — and it is the honest summary of this report: the low-bias moment propagation we spent the phase failing to build is real, and someone has it.
Reproducibility
Every quantitative claim traces to a standalone probe script with logged seeds, run against cached large-N Monte-Carlo ground truth built by the published generative process. Headline numbers are grader-confirmed submission IDs; the raw final-layer MSE of three consecutive graded entries agrees to every printed digit (fixed-seed determinism, grader-confirmed), the same file resubmitted twelve days apart (#318640 → #326024) reproduced its raw MSE to every printed digit across a cost-model re-evaluation and the runtime migration, and each billing change was verified toggle-off bit-identical against the previously graded entry. All probes and the full report will be released open-source per the Rules if the submission is prize-eligible.
Happy to answer questions on any of the negative results — several of them cost more to establish than the positive ones, and a few contradict things we ourselves asserted earlier in the competition.
writeup.pdf (2.0 MB)