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.