Experiments

The successor-closed corpus pipeline works exactly as designed (11,379 roots, 616,048 sibling labels, 100% action completeness, all CHECK tests pass), but the frozen label-stability floor failed: with K=8 aligned scenarios and an H40 phase-greedy-D1 continuation, the split-half Spearman correlation of within-root action rankings is 0.246, far below the 0.50 floor. Per the preregistered gate the outcome is inconclusive: the scenario-mean H40 outcome ranking is too noisy at K=8 to certify any model's ranking. Diagnosis: within-action scenario std is ~21k points while the median between-action gap is ~7.1k, so the target ranking is noise-dominated; noise math predicts K=64 (split-half 32v32) lifts stability to roughly 0.7. For the record, against this noisy target the model trailed fair D4 (top-1 0.247 vs 0.330 pooled; pairwise 0.571 vs 0.637), and D4 beat D1 (0.330 vs 0.254), consistent with the historical ranking of those searches. No gameplay tier was opened.

With K=256 aligned scenarios the label-stability floor passed decisively (decisive-root split-half Spearman 0.818, unconditioned 0.638, both >= 0.5), so for the first time in this line the ranking target is stable enough to certify a verdict. The verdict is a valid negative for the direct-play configuration: the distributional afterstate ranker trailed exact fair D4 on every preregistered comparison in both fresh held-out half-folds (pooled top-1 0.424 vs 0.499; pairwise 0.685 vs 0.737; regret 0.241 vs 0.178). On the 411 decisive roots (spread > 20k) the gap narrowed but persisted (top-1 0.526 vs 0.584; regret 0.082 vs 0.064). The model clearly beat its D1 continuation teacher (top-1 0.424 vs 0.319) and its quantile head is calibrated (0.864 coverage). Conclusion: a compact action-free afterstate network trained on successor-closed H40 D1-continuation labels is a viable, calibrated long-horizon evaluator, but it is NOT a viable direct replacement for 4-ply expectimax; any future use must be as a companion signal inside search, and the same ranking gate applies. No gameplay tier was opened.

K=64 improved label stability from 0.246 to 0.446 mean split-half Spearman on fresh held-out origins, but still below the frozen 0.5 floor, so the preregistered verdict is again inconclusive. Quantile calibration passed (0.807 coverage of the nominal 76.5% interval). Against the still-noisy target the model trailed fair D4 consistently in both half-folds (pooled top-1 0.342 vs 0.433; pairwise 0.637 vs 0.697; regret 0.303 vs 0.232) while beating its D1 continuation teacher (top-1 0.342 vs 0.299). Training stopped at epoch 15 of 20 on the GPU time budget with the ranking loss still decreasing. No gameplay tier was opened.

The calibrated top-two near-tie override of fair D4 by the frozen iteration-3 afterstate model FAILED its frozen gate by a narrow margin, with genuinely positive signal. On 2,689 fresh held-out roots, 1,030 (38.3%) were near-tied at the frozen 500-point threshold and the override fired on 37.0% of those. On eligible roots the override reduced mean normalized regret versus unchanged D4 in both half-folds (half1 0.2484 vs 0.2835, +0.0351; half2 0.2343 vs 0.2418, +0.0075; pooled +0.0214), but the frozen criterion required at least +0.01 in EACH half-fold, and half2 fell short. On the 84 decisive eligible roots the improvement was larger (+0.0426: 0.0880 vs 0.1306). Label stability passed (decisive Spearman 0.814), model quantile calibration passed (0.861), the gate is deterministic (byte-identical repeated reports), and the corpus is successor-closed. Interpretation: the conservative-override MECHANISM works as designed (fires often, calibrated, positive in both halves) and this is the first preregistered held-out test in this repository where a learned model's intervention improved on fair D4 at all; the CHECKPOINT's ranking quality is the bottleneck, consistent with the model being undertrained (11 of 20 epochs) and trained on a weak D1-continuation teacher. Per the frozen failure action, no further override variants of this same checkpoint are opened; a retry requires new evidence such as a fully trained or stronger-teacher model under the same frozen rule.

The stronger-teacher hypothesis fails as tested. A successor-closed corpus relabeled with a fair-D2 (five-sample) continuation teacher at K=64 (2.88M rows over 6,535 roots; partial at the generator's 4h default wall stop) trained a model that, on the fresh 0x5da70500 ranking gate against the fixed D1-continuation H40 target, reached top-1 0.3365 - far below fair D4's 0.5020, below the D1-teacher model's 0.4245 from iteration 3, and only at exact-D1's own 0.3339. The frozen criterion (top-1 >= 0.4616 on each half, i.e. closing half the iteration-3 gap to D4) failed by a wide margin in both halves (0.342, 0.331). The frozen override gate on fresh 0x5da70600 roots also failed (eligible-root regret: half1 -0.0089, half2 +0.0110, pooled +0.0012). IMPORTANT CONFOUND, disclosed: the D2-teacher model was evaluated against D1-continuation outcomes (frozen for comparability with iteration 3), so part of its regression may reflect the teacher/target mismatch rather than teacher quality alone. Read narrowly, the result says a stronger-teacher corpus did not produce a better ranker of the fixed public-continuation outcome, and the afterstate line's ranking deficit is robust to the teacher choice within the tested configurations.

Scale-out stage 1 fails its prerequisite: a compact action-free afterstate model cannot learn fair D4's within-root ordering even from successor-closed, exactly-labeled search values. Training labels were the pinned reference's own depth-3 values of every legal sibling's resolved afterstate under its own five-stratum quadrature (291,890 labeled afterstates over 8,639 training roots, completeness 1.0). On 3,030 fresh held-out roots the model's one-ply chance-averaged ordering agreed with exact fair D4 at top-1 0.375 (frozen threshold >= 0.60), pairwise 0.643 (>= 0.78), normalized regret 0.291 (<= 0.13), failing every criterion in both origin-hash half-folds. For scale, exact fair D1 agrees with D4 at 0.486 top-1 on the historical panel - the learned student is WORSE than the cheapest exact search. Combined with the repository's prior played-action distillation failures, this strengthens the conclusion to: the obstacle to learning D4's ranking is not sibling coverage but the representational capacity of a compact board evaluator for the 4-ply search-value function. The registered self-play loop's stage-1 prerequisite is not met at this model scale.

Full training does not rescue the afterstate model; it overfits. The model was trained to 22 epochs on the 2M-row K=256 subsample (44M row-updates, 2x iteration 3, cosine schedule completed, ranking loss 0.584 vs iteration 3's 0.630). On the SAME held-out roots as iteration 3 (corpus-C, a labeled diagnostic reuse), the fully-trained model ranks WORSE than iteration 3's 11-epoch checkpoint (top-1 0.361 vs 0.424, pairwise 0.658 vs 0.685, regret 0.281 vs 0.241) - training loss improved while held-out ranking degraded, a textbook overfitting signature against the D1-continuation H40 labels. The frozen override gate on fresh corpus-E (2,867 roots, 1,106 near-tie eligible, 41% override rate) then FAILED: eligible-root regret half1 0.2289 vs D4 0.2517 (+0.0228) but half2 0.2778 vs 0.2481 (-0.0297, the override is actively harmful there), pooled +0.0018. Stability (0.824), calibration (0.800), determinism (byte-identical) all passed. Conclusion: the model's limitation is not training completeness but generalization to held-out roots under a weak D1 teacher; the direct-override use of this model family is closed per the frozen failure action.

The fifth ply buys nothing at either chance resolution, and the earlier interim reading that it was actively harmful is withdrawn. Complete leg, 64 of 64 games: depth 5 at five strata scores 288,704 against depth 4 at five strata's 297,327, a paired -8,624 with a one-sided 95% whole-game bootstrap lower bound of -55,134 and W-T-L 33-0-31, for 23.29x the logical work per move. That is a wash, not a reversal. Partial leg, 16 of 64 games and still running: depth 5 at seven strata is -1,581 against the depth-4 seven-stratum control (95% lower bound -173,154, W-T-L 7-0-9) at 34.32x the work, and +16,622 against depth 3 at seven strata (95% lower bound -130,027, W-T-L 8-0-8) at 1,084.78x the work. At a fixed stratum count, depth 3 -> 4 -> 5 does not separate. READ THIS BEFORE QUOTING THE MEANS: the eye-catching gap between the 398,498 of d4s7 and the 288,704 of d5s5 is a chance-samples effect and not a depth effect, because those two arms differ in both factors; the correct paired depth contrasts at fixed chance resolution are d5s5 - d4s5 = -8,624 and d5s7 - d4s7 = -1,581, both indistinguishable from zero, and the correct paired stratum contrast at fixed depth is finding-05's d4s7 - d4s5 = +101,171. The interim slice reported in finding-15 section 2.2 (-268,611 over 8 paired games) was completion-order biased against depth 5 exactly as that section warned; at 16 games the bias is gone and the delta is -1,581. The engine control is clean and is the other retained result here: the fast engine's depth-4 seven-stratum arm reproduces the recorded unoptimised arm over 64 paired games x 11 fields with 0 mismatches, and the depth-5 five-stratum arm reproduces the recorded 32-game unoptimised arm over 32 paired games x 11 fields with 0 mismatches across two binaries and two different cache capacities. Every arm audited 0 incomplete decisions at its requested depth, 0 censored games and 0 score-decomposition identity failures. Flow rates fall with depth at five strata (1.9387 clears and 1.0651 reveals per move against depth 4's 1.9489 and 1.0697, and against the 2.400 and 1.400 indefinite survival needs), so nothing here moves toward the target.

SUPERSEDES RS-20260821T181917Z-9a34ba02, which assessed this experiment when the depth-5 seven-stratum arm held 16 games. The arm was stopped by the repository owner's decision at the 32-game chunk boundary and will not be resumed, so its analysis is now FINAL even though the cohort is partial: 32 of 64 planned games, every one of them a whole game, 0 censored, 0 score-decomposition identity failures, 0 incomplete decisions, minimum completed depth 5. The old record remains committed history and is not edited. THE HEADLINE IS A CORRECTION, NOT AN UPDATE. The previous record read the fifth ply as 'does not separate'. That reading was a NON-MEASUREMENT REPORTED AS A NULL. Doubling the sample from 16 to 32 games moved the depth-5-minus-depth-4 seven-stratum contrast from -1,581 to +23,367 and its median from -39,660 to +18,820 - THE SIGN FLIPPED - which is what a quantity being estimated far below its detection floor looks like. By chunk the paired mean is -1,581 on the first 16 seeds and +48,315 on the second 16. Do NOT replace the old reading with 'depth 5 helps': +23,367 is equally unsupported. The one-sided 95% bootstrap lower bound is -83,046 and the contrast's detection floor at n=32 is 107,988, so the estimate sits at 22% of the smallest effect this cohort could have resolved. The correct statement is that THE FOURTH-TO-FIFTH PLY CONTRAST AT SEVEN STRATA WAS NEVER MEASURED, in either record. THE POWER ANALYSIS IS THE MOST USEFUL THING THIS EXPERIMENT PRODUCED. Detection floor, taken as 1.645 x sd / sqrt(n), the smallest true effect whose one-sided 95% bound would clear zero: d4s7-d4s5 +101,171 against a floor of 55,192 (n=64); d4s7-d3s7 +86,172 against 61,457 (n=64); d5s5-d4s5 -8,624 against 47,052 (n=64); d5s7-d4s7 +23,367 against 107,988 (n=32). EVERY SIGNIFICANT RESULT IN THIS FACTORIAL IS ABOVE ITS FLOOR AND EVERY NULL IS BELOW IT - the factorial separated the contrasts it had the power to separate and nothing else. Resolving the observed +23,367 needs about 684 paired games; finishing to the planned 64 would have left a standard error near 46,400 against a 23,367 estimate, still a non-measurement. That is the justification for the stop: the contrast is not answerable at any affordable cohort size, so the marginal machine-day buys no information. The variance is structural, not fixable by tidier running: the five largest single-seed paired deltas are -1,002,862, +958,985, -678,455, +592,546 and -577,069, so individual games swing by more than twice the cohort mean. WHAT IS ACTUALLY MEASURED HERE, and it is the same lesson from the other side: at depth 5, going from five to seven strata is worth +123,613 with a lower bound of +32,575, W-T-L 19-0-13 - SIGNIFICANT, and comfortably above its 95,207 floor - for 5.85x the work. The chance-exactness axis pays at depth 5 exactly as it pays at depth 4 (+101,171 [+47,447] there). The previous record's warning therefore survives and is strengthened: the eye-catching gap between d4s7's 398,498 and d5s5's 288,704 is a CHANCE-SAMPLES effect, not a depth effect, and both stratum contrasts are now significant while no depth contrast is. The engine controls are unchanged and clean: the fast engine's depth-4 arm reproduces the recorded unoptimised arm over 704 field comparisons with 0 mismatches, and the depth-5 five-stratum arm reproduces its recorded 32-game predecessor over 352 comparisons with 0 mismatches across two binaries and two cache capacities.

Chance-node decorrelation and search depth do not compound; they substitute. The primary arm is complete at 64 of 64 games: depth 4 with seven disc samples and two reveal samples scores 356,548 against the 398,498 of the same search with one reveal sample, a paired -41,950 with a one-sided 95% whole-game bootstrap lower bound of -100,137 and W-T-L 28-0-36, for 4.07x the logical work per move. The gate asked for a lower bound above zero and got a negative point estimate, so the compounding theory is rejected as tested. STATE THE DOSE WHEN QUOTING THIS: two reveal samples raises joint (disc, reveal) coverage from 14.3% to 28.6%, which is a smaller increment than the six samples (85.7%) that first cleared noise at depth 3; at depth 3 the three-sample dose (42.9%) was also not significant (+24,980, lower bound -23,451). This result therefore rejects a doubling of reveal samples on top of the fourth ply, and does not establish that a wide reveal estimator at depth 4 would fail - that arm was never affordable. What the arm does establish is that the depth-4 search is not starved for the thing the extra samples supply. The striking positive finding is an equivalence at near-equal work: depth 3 with six reveal samples costs 4,244,020 work per move and scores 376,442, while depth 4 with one reveal sample costs 4,956,614 and scores 398,498, and the paired delta between them is -22,056 with a lower bound of -89,867 and W-T-L 30-0-34 - two different ways of spending the same budget landing in the same place, which is the same exchangeability the depth factorial shows from the other side. The new arm is not worthless: against the frozen five-stratum depth-4 reference it is +59,221 with a lower bound of +9,134 and W-T-L 37-0-27, so the gain comes from the seven disc samples, not from the reveal samples. Second arm, partial at 32 of 64 games and still running: depth 3 with twelve reveal samples takes joint coverage to 100% and scores -4,495 against the six-sample arm on the 32 shared seeds (lower bound -91,425, W-T-L 15-0-17) and +31,413 against the one-sample arm (lower bound -70,729), so the ladder that ordered with coverage from M=1 to M=6 stops ordering at M=12. Every arm audited 0 decisions below target depth, 0 work-limit events, 0 censored games and 0 score-decomposition identity failures, and the chunk-pooling used to survive interruption was verified to reproduce a single 64-game run field-for-field with identical summed logical work.

SUPERSEDES RS-20260821T181918Z-ea7076a3, which assessed the same experiment while its second arm held 32 of 64 games. Both arms are now complete at 64 of 64 and the run validity rises from partial to valid. The old record remains as committed history and is not edited; this record carries the completed figures and everything below replaces the partial ones. Nothing in arm 1 changed and the direction of arm 2 did not change; only its magnitude did, by about 6x. ARM 1, unchanged and complete: depth 4 with seven disc samples and two reveal samples scores 356,548 against the 398,498 of the same search with one reveal sample - a paired -41,950 with a one-sided 95% bootstrap interval of (-100,137, +17,541) and W-T-L 28-0-36, for 4.07x the logical work per move. The gate required a lower bound above zero, so the compounding theory is rejected as tested. The sign is stable across both cohort halves (-11,082 on seeds 0xa51d1000-0xa51d101f and -72,818 on 0xa51d1020-0xa51d103f), independently confirmed by the agent that completed the runs. The +17,541 ceiling is the load-bearing number: had the axes compounded even at a quarter of the +64,116 the same knob is worth at depth 3, the data would have had to show it. The axes substitute in the strong sense. ARM 2, now complete: depth 3 with twelve reveal samples - the configuration at which (disc, reveal) joint coverage reaches 100% - scores 349,345, not the 356,890 its first 32 games suggested. Against the six-sample arm it is -27,097 with an interval of (-83,807, +31,209) and W-T-L 28-0-36; against the one-sample arm +37,019 (-25,076, +102,426), 30-0-34. THE REVEAL AXIS SATURATES AT M ABOUT 6 AND DOES NOT IMPROVE TO FULL COVERAGE. Read this as saturation, not as a demonstrated regression: the M=6 to M=12 step does not clear zero in either direction, so the data are consistent with the curve being flat from M=6 onward and are not consistent with it continuing to climb at the rate M=1 to M=6 showed. Score, moves, numbered clears and covered reveals all peak at M=6 (85.7% coverage) and fall back at M=12 (100%); only mean occupancy improves monotonically across all four points (23.88, 23.81, 23.49, 23.39). This weakens two SUPPORTING arguments in finding-09 without touching its headline, which rests on its own paired tests and stands: the dose-response is no longer monotone once the fourth point is added, with four of five tracked quantities reversing, and section 2's attribution of strength to joint coverage fails exactly at the 100% endpoint that attribution predicts should be best. finding-09 section 5 should now be read as 'M=6 is a local optimum', not 'more M is better'. Validity controls all pass: 0 decisions below target depth, 0 work-limit events, 0 censored games and 0 score-decomposition identity failures in both arms, and the chunk-and-pool procedure on which every cohort in this family depends was verified end to end by running depth 3 (N=5, M=1) as four 16-game chunks at 1 thread and reproducing the existing 64-game 12-thread artifact field-for-field - 0 mismatches, identical summed logical work of 312,966,881, only per-game wallSeconds differing, which also re-confirms worker-count independence.

Corpus analysis of entombed numbered discs (value n with column height > n and horizontal run > n) over 4,863,627 non-explored positions. Prevalence: an entombed disc of value >= 3 is on the board in 19.1% of depth-4 behaviour states overall, rising from 7.6% more than 40 moves before death to 69.8% within 5 moves of it. At death: 579 of 768 complete depth-4 games (75.4%) end with one on the board (criterion 1 holds). Lead time from first persistent appearance to death: median 11 moves, quartiles 5.5-15, 57% at least 10 moves, 8% at least 20 (criterion 2 holds, narrowly). Incremental signal: held-out R^2 for log1p(moves to death) is 0.6952 with the 18 frozen leaf features + occupancy + rise clock and 0.6955 with the entombed features added (+0.0003); the held-out partial correlation of the entombed count is -0.023 (threshold -0.05). Criterion 3 fails. Occupancy-matched, an entombed >= 3 disc shortens mean remaining life by about two moves (e.g. 35.0 vs 37.4 at 24-27 occupied cells; 24.6 vs 26.3 at 28-31). Reading: the disc is a reliable marker of the policy's last two rises, but the leaf's value-blind height and cover terms already carry almost all of its lifetime information; as a static foresight term it is not what the search is missing. Gate: FAIL (not-supported-as-tested).

Held-out SCREEN of the CMA-ES leaf (distribution mean after 40 generations, stop=max-generations) against the frozen fair leaf, depth 4 five strata, 64 paired never-read games 0xa52b0000+: mean 289720 vs 320020, paired delta -30300 (bootstrap 95% LB -70928, t LB -71500, paired sd 197434, floor 40597), W-T-L 28-0-36, halves -53933/-6667, Q25 delta +8592. Gate: FAIL. Secondary seven-stratum transfer on the same seeds (diagnostic only): delta -47119 (LB -117910). Training-block population-mean-minus-control exceeded +20,000 in at least one of the last 10 generations.

One-entry leaf memo (fast-engine-memo/MemoSearch) on real probe seeds: leaf bits 0/4,260 (d4s5) and 0/2,500 (d4s7) mismatches in the search's feeding order; parity with FastSearch 0 action/work/node/cache-hit/completed-depth mismatches over 160 (d4s5, 117,732,775 leaf calls) and 50 (d4s7, 119,607,901 leaf calls) moves; determinism 0 mismatches at 1 vs 4 threads; memo hit rate 61.74% (d4s5) and 68.47% (d4s7); interleaved timing plain/memo 1.581x (d4s5, 12 real roots x 3 reps) and 1.634x (d4s7, 6 roots x 2 reps) under load ~31, indicative. Engineering result: semantics-preserving; no strength claim.

Offline capacity/training sweep of the NNUE-shaped survival leaf on runs/RUN-A51D-corpus/all.states (13 runs, same whole-origin test split, 486,819 held-out examples). Baseline h64/m32/e10/lr3e-3 held-out lifetime Pearson 0.8546 (finding-08 recorded 0.8564 on an earlier torch build); seed-to-seed spread 0.0023 over three seeds. Best configuration h64-m64-e10-lr3e3-s0 at 0.8568, delta +0.0022 <= max(0.005, 2 x spread): gate verdict supported-as-tested. Width hurts: Pearson by width (params, Pearson, final train loss) h32-m32-e10-lr3e3-s0 (286,447 params: 0.855, loss 0.5238); h64-m32-e10-lr3e3-s0 (572,367 params: 0.8546, loss 0.511); h128-m32-e10-lr3e3-s0 (1,144,207 params: 0.8543, loss 0.5006); h256-m32-e10-lr3e3-s0 (2,287,887 params: 0.8515, loss 0.4857); h256-m64-e20-lr3e3-s0 (2,296,591 params: 0.8446, loss 0.4596); h512-m64-e20-lr3e3-s0 (4,592,143 params: 0.8378, loss 0.4197). Training loss falls monotonically with width while held-out accuracy falls, i.e. larger students overfit this corpus; 20 epochs change nothing at h64 and hurt at h128/h256; lr 1e-3 and mid 16/64 are within spread. The accuracy of this feature space on this corpus is saturated near 0.855-0.857; it is not limited by hidden width, middle width, epochs or learning rate.

Held-out SCREEN of the survival-instinct root filter, depth 4 five strata, 128 paired never-read games 0xa52c0000+. STRICT (refuse a landing that is vertically dead AND entombed by its row): mean 346838 vs unchanged 348808, paired delta -1970 (bootstrap 95% bounds -27738 to +22313, paired sd 171933, floor 24999), W-T-L 41-26-61, moves 100.95 vs 101.32; the filter refused a column at 811 of 12922 decisions and overrode the unchanged search's column at 254 (1.97%), just under the preregistered 2% coverage bar, so the primary gate is recorded as INCONCLUSIVE by its own rule: the strict rule neither helps nor hurts measurably and rarely applies. LITERAL (the owner's wording, refuse every vertically dead landing that does not clear on arrival; secondary arm): mean 251744, paired delta -97064 (LB -136887, UB -59500), W-T-L 43-0-85, moves 75.67 vs 101.32, overrides 1243 of 9686 (12.8%): a clear, valid negative — forbidding vertically dead landings outright costs about a quarter of the game's length. Both arms: 0 incomplete and 0 illegal decisions.

C0 reanalysis (K2 program section 8 row 0): the paired per-game bound behind the +79,115 head start is now printed, and it clears zero. On the 64 shared seeds 0xa51d1000-0xa51d103f, depth 3 with seven disc strata and six reveal samples (fair leaf, finding-16) scores 376,442 against fair depth 4 at five strata's 297,327 (finding-05): paired +79,115, one-sided 95% percentile bootstrap lower bound +29,033 (upper +129,722; 20,000 resamples, seed 0xb0071eaf), Student-t lower bound +27,548, W-T-L 35-0-29, halves +88,138 / +70,092, Q25 +34,872 (227,224 vs 192,352), median 322,859 vs 260,415, median paired delta +32,926, moves +22.30 (LB +8.67), paired sd 247,113, detection floor 50,813, at 3.27x the logical work per move (4,244,020 vs 1,296,034). Both gate bounds are positive, so the experiment passes and the theory is supported-as-tested at public-development tier. READ THE CAVEATS: the means and their difference were published before this gate was written, so this is a bound attached to a known sign on already-read development data, not a discovery; it is not promotable above this tier on this cohort. The delta is heavy-tailed: the five largest paired gains (seeds 0xa51d1012 +747,416, 0xa51d1020 +684,129, 0xa51d1008 +643,799, 0xa51d1001 +643,344, 0xa51d1033 +558,163) carry 64.7% of the summed delta, the sixteen largest carry 134% (the remaining 48 games net negative), and the worst loss is -332,950 (0xa51d103c); the minimum leave-one-out mean is still +68,507, so no single game is load-bearing, but against a detection floor of 50,813 the mean sits 1.56 floors above zero and the bootstrap lower bound only 0.57 floors above it. The flow statistics move with the score: numbered clears per move 2.0447 vs 1.9489, cover reveals per move 1.1423 vs 1.0697 (paired clears +53.9 per game, LB +21.1; reveals +31.8, LB +12.6), mean occupancy 23.49 vs 24.29. SECONDARY, not gated: against fair depth 4 at seven strata (398,498) the same arm is -22,056 with bounds (-92,005, +45,490), t lower bound -92,330, W-T-L 30-0-34, halves -27,121 / -16,991, Q25 +14,360, moves -5.20, at 0.86x the work; this reproduces finding-16's -22,056 point estimate exactly and its bootstrap lower bound to within 2,138 (finding-16 printed -89,867 from its own resampler; this run's pinned seed gives -92,005), and remains a wash. So the head start the K2 fallback route (c) stands on is real against D4 s5 but the same arm does not separate from D4 s7, which is the stronger comparator and the one the program's end state must beat on the strength-cost frontier.

E-FAST-M6 passes: factored reveal sampling (N disc strata x M reveal samples, native scenario indexing s = r*N + d over T = N*M) is ported into the fast memo engine as drop7::fastr::FastFactoredSearch and is trace-equivalent to the native FactoredSearch. Grid gate: 6,300 live probe decisions (525 per point over d3/d4 x N5/N7 x M1/M2/M6) with 0 column, 0 work-count and 0 completed-depth mismatches, including 549 work-limited decisions on the two budget-capped d4-M6 points where both engines degrade to completed depth 3 identically. All 3 retained C0 games replay to byte-for-value final identity with the fast engine driving (335 decisions, 0 mismatches). M=1 regression: 2,100 decisions x {memo-on, memo-off} bit-identical to the untouched fast::FastSearch on all six metric fields. Determinism byte-identical across repeated runs and {26,7,1} threads; mirror invariance exact with symmetric boards excluded (finding-13 4C; one disclosed gate-harness iteration); the one-entry leaf memo stays enabled under M>1 (board-memcmp keying cannot alias across reveal samples) with memo-on/off trace identity across the grid. Continuation duty: 8 CRN continuations (2 C0 roots, K=4, H=40) byte-identical to native. Realised speedup at d3 N7M6 is 5.5-5.8x (play duty 2.140 -> 0.385 s/move; continuation duty 0.990 -> 0.177 s/move; grid 4.38-5.87x across points), measured under the gate's own 26-thread load - well below the 10-40x hoped for in the hypothesis, because that figure divided native M6 seconds by fast M1 seconds and ignored the ~27x work ratio. P-SOL continuation labels at native D3 N7M6 semantics now cost ~0.18 s/move instead of ~1-3.4 s/move.

Stage D0 refuses the H-pool theory on two of its three preregistered criteria. Pool O was 1,984 public states sampled from 64 oracle games (depth 4, beam 128; 63 of 64 games reached the 500-move cap); 1,271 were matched 1:1 to fair-D4 states on exact (rise phase, occupancy/4, max-height/2) buckets over all 256 comparator seeds (match rate 0.641; 713 O states dropped and counted). Under 32 common public futures with fair D1 continuation at horizon 25, oracle-visited boards are only marginally better than matched fair boards: R_fair(O) = 24.783 vs R_fair(F) = 24.520 (difference +0.263 moves, cluster bootstrap 95% [+0.156, +0.367], same positive sign in both origin-game halves). The preregistered transferable fraction is negative, tau = -0.959 (95% cluster interval [-3.069, -0.390]), because its denominator degenerates at this horizon: R_tape(O) = 24.338 vs R_real(F) = 24.611 (94-95% of both realised remainders were capped at 25), so the realised-lifetime gap the fraction was defined against is -0.274 moves rather than positive. Independently of that degeneracy, the action-quality criterion fails outright: the oracle's own column is fair-top-1 at its own roots less often than fair D4's column at the same roots (0.766 vs 0.814 over 1,271 roots, difference -0.049, 95% [-0.069, -0.029]; on the 194 unique-maximum roots 0.268 vs 0.387). Blocked-flow-band fraction over matched O states is 0.0047 (F: 0.026). Per the preregistration the theory is assessed not-supported-as-tested, the pool-comparison follow-on is not registered, and audit-05's H-pool program closes.

The leaf-affordable NNUE-class student does not reproduce fair D4's within-root ordering from the existing successor-closed labels. Five initialisation seeds of the LeafNet h64/m32 student (571,905 parameters; features from learned-leaf/leaf_features.py) were trained for 30 epochs on the 6,551 training roots of runs/RUN-20260821T085042Z-c5cf0e71/d4q-labels with the preregistered listwise + gap-weighted pairwise + 0.1 MSE loss; the seed with the best calibration-fold top-1 (0xA52E02, 0.3281) was then read once on the 3,030-root held-out panel of that experiment. Held-out top-1 was 0.296 / 0.3011 in the two origin-seed half-folds (gate >= 0.60), pairwise 0.6266 / 0.6259 (>= 0.78), normalised regret 0.3354 / 0.3379 (<= 0.13): every criterion fails in both half-folds. The other four seeds lie between 0.2987 and 0.3135 pooled top-1, all below the 3.4M-parameter afterstate CNN of RS-20260821T104500Z-77d21e90 (0.375) and below exact D1 (0.486). The student is leaf-affordable as claimed (1.27 us per state through the existing d7leaf export and leaf-check), but at this size it holds less of D4's ordering than the CNN did. Per the preregistered failure action: no leaf-affordable NNUE-class student of this size reproduces D4's ordering from these labels; the self-play loop TH-20260821-...-299ed02f stays blocked in its leaf form and its redesign is routed to the larger-student question. Diagnostic tier: the held-out panel had already been read once by the d4q experiment, so this is a diagnostic read on existing data, not new evidence about fresh roots.