Research Status

Bottom line

The simulator and reference searches are mature enough to support reproducible research, but the strategy problem is unsolved. Corrected-score fair depth-4 expectimax is the strongest dependable reference found so far. Its broader 64-game ledger mean is about 308,296 points, far below the required one-million-point average.

Exploratory work on 2026-08-20/21 reproduced that reference on fresh seeds and completed the depth-by-chance-resolution factorial that the roadmap had listed as priority 8. Two results from it are load-bearing for what to do next, and both are single-cohort development tier — they do not upgrade the ledger:

• The fourth ply is worth +86,172 points, but only with an exact chance model (95% lower bound +26,605, 40-0-24 over 64 paired games). With an approximate five-stratum model the same fourth ply is worth −7,723. Chance resolution does not merely add points; it changes the sign of the depth gradient.
• The fifth ply is not measurable by this design. At five strata it is −8,624 over 64 paired games; at seven strata it is +23,367 over 32. Both are far inside their own detection floors (see below), and the seven-stratum estimate changed sign when the cohort grew from 16 games to 32. The honest statement is that any depth-5 effect is smaller than a 64-game paired cohort can resolve, not that it is zero. What can be said is economic: even the optimistic estimate is +23,367 for 35.6x the work per move.
• A 64-game paired cohort in this game cannot see an effect below roughly 50,000 points. Paired whole-game deltas have a standard deviation of 228,000 to 371,000 depending on the contrast, so the one-sided 95% detection floor runs from 47,052 to 107,988. Every null result in the depth factorial is below its own floor and is therefore a non-measurement rather than evidence of no effect. Resolving the observed +23,367 would take about 684 paired games, about 13 wall-days at that arm's measured throughput. Choose experiments whose predicted effect exceeds the floor, or find a lower-variance estimator than complete games.

No candidate has qualified for the protected validation protocol. The frozen record marks both the protected and one-shot final cohorts as unopened.

Evidence snapshot

The cleanup reproduced engine behavior and buildability, not the long and expensive training/evaluation runs in the historical ledger.

How the research progressed

1. Establishing a trustworthy simulator

The work first aligned TypeScript and native Hardcore rules, chain scoring, gray-disc reveals, row rises, and deterministic seed behavior. A scoring audit corrected the five-move mode's level award from 7,000 to 17,000. Results made with 7,000-point scoring remain historical Sequence-scored evidence and are not used for the Hardcore million-point claim.

2. Hand-written policies and shallow lookahead

Feature-weighted heuristics, open-loop beams, risk penalties, tunneling, ignition, evolutionary search, and shallow fair lookahead provided fast baselines. They showed that immediate score alone is a poor guide: a policy must keep revealing covered numbers and preserve future chain structure.

3. Fair expectimax as the reference

Completed fair D4 consistently improved on D3 in the corrected-score small cohorts and became the reference for later experiments. Going deeper was not automatically better. Selective D5, full D5, and cycle-boundary variants often spent much more work, sampled chance outcomes too noisily, or overrode good D4 actions on unstable estimates.

4. Learning public-state values

N-tuples, Monte Carlo values, NNUE-style networks, DQN variants, phase students, PPO, and fitted-policy methods explored longer horizons. A repeated problem was sibling extrapolation: a model learned the outcome of the action that was played, then deployment asked it to choose among several actions it had not observed equally well. Low value error on visited states did not guarantee good root-action ranking.

5. Oracle and long-outcome teachers

Privileged future-aware planners, D4 distillation, 25-move outcomes, rollout vetoes, and curriculum data were used to build better labels. They found predictive signal, but students usually lacked enough diverse successor data, failed held-out sibling ranking, or were too slow to improve complete games. Oracle strength is an upper-bound teaching signal, not a legal policy result.

6. Constructive cycles and explicit reservoirs

Reservoir, viability-controller, constructive-spectrum, and tail-survival experiments tried to build chain structures deliberately across row rises. A 12-move constructive horizon improved over a 7-move version in one development comparison, but longer horizons were not monotonic and the policies did not displace D4. The idea still appears useful as a feature or option, but not yet as a standalone controller.

7. Offline policy improvement around D4

The latest completed work evaluated every legal sibling on a locked panel of 477 public roots. A martingale-dual H12 ranker underperformed D4: 28.93% vs 38.16% top-1 accuracy, 59.85% vs 66.82% pairwise accuracy, and higher normalized regret. A regenerative policy-iteration variant was nearly identical to D4 but overrode only 11 roots; six overrides helped, confidence bounds were negative, and only five of eight origins did not regress. Neither justified a gameplay run.

Most useful conclusions so far

• Fair chance handling matters. Optimistic, worst-case, or tiny reused reveal samples can rank moves incorrectly.
• More depth is not automatically more strength. Horizon, continuation quality, chance variance, and work budget interact. The 2026-08-21 factorial makes the interaction concrete: with an approximate chance model the best depth is three and deeper search actively loses; with an exact chance model the best depth is four. Depth and chance resolution substitute rather than compound: at equal work, depth 3 with six-fold reveal sampling (4.24M per move, 376,442) and depth 4 with single-sample reveals (4.96M, 398,498) are statistically indistinguishable, and doubling reveal samples on top of ply 4 buys nothing measurable for 4.07x the work. Refining the reveal distribution is itself worth +64,116 at depth 3 (95% lower bound +7,475) and saturates before full joint coverage.
• Flow matters before spectacular chains. The task record repeatedly used roughly 2.4 numbered clears and 1.4 reveals per move as the region associated with stable long games. Treat these as diagnostic targets from limited runs, not proven universal thresholds.
• Static board potential is insufficient. Similar-looking boards can have very different futures depending on how reachable triggers and covered discs evolve across rises.
• State-value accuracy is not action-ranking accuracy. Training data must cover legal siblings or use an objective designed for relative action value. As of 2026-08-21 this is necessary but demonstrably not sufficient: a student given successor-closed coverage, every legal sibling, and exact search-value labels still ranked worse than a one-ply exact search.
• Score is heavy-tailed, and this sets a hard measurement floor. One million-point game can coexist with a much lower average; paired whole-game cohorts and confidence bounds are essential. But pairing does not rescue small effects: single-seed paired deltas in the depth factorial reach −1,002,862 and +958,985, more than twice the cohort mean, so a 64-game cohort resolves nothing below roughly 50,000 points. Before running a cohort, state the effect size the mechanism predicts and check it against the floor.
• D4 is useful but not the answer. It is a strong tactical fallback and teacher, yet its average is not close enough to qualify.
• The leaf evaluation prices what search cannot see. Refitting it toward a quantity the search already computes exactly — achievable clears over the next few moves — loses monotonically, and loses by destroying the upper tail rather than the lower one. A leaf that correlates weakly with short-horizon clear rate is behaving correctly, not failing.
• Cheap proxies for this game invert. Three independent times a short-horizon screen has ranked configurations in the opposite order from complete games: the suite-h9-v1 scenario suite, a depth-3 screening run, and an eight-move achievable-clear label. Screen at the depth you intend to deploy, or do not screen.

Directions closed by exploratory evidence, 2026-08-20/21

Each entry rejects the exact configuration tested, at development or pilot tier. None of them is a proof that the underlying idea is impossible, and each names what would reopen it.

The two afterstate rows matter more than their tier suggests. The program's standing explanation for every failed learned policy was insufficient sibling coverage. The 2026-08-21 experiment supplied successor-closed coverage, every legal sibling, exact search-value labels, and completeness 1.0 — and the student still ranked worse than a one-ply exact search. That relocates the obstacle from the training data to the capacity of a compact board evaluator, and it makes "train a bigger student" a falsifiable next step rather than a hopeful one.

Open work

The next research step should be evidence-driven rather than another broad architecture sweep:

1. Re-register any resumed SHA-locked experiment against the reorganized source tree and rerun cross-engine parity.
2. Refit the search leaf against remaining lifetime, the quantity that correlates with score at r = 0.9995, rather than against achievable clears.
3. Test whether student capacity is the binding constraint, since that is now the explicit claim on the table and the cheapest one to falsify.
4. Test long-cycle features as bounded corrections to D4 before allowing them to control an entire game.
5. Resolve the three recorded divergences between this simulator and the shipped game, which is an owner decision and not an agent decision.

Items 1, 4 and 5 are unchanged. Items 2 and 3 replace the AFBR-40 closure sequence, whose data-feasibility question was answered directly: closure was achieved and did not rescue the model.

AFBR-40 as originally proposed has no implementation, protocol, model, or measurements in this repository and must not appear in a list of attempted results. The action-free afterstate models that were built and measured on 2026-08-20/21 are separate, separately recorded, and are not AFBR-40.

For configurations and every retained entry point, use the experiment index. For the unabridged chronological record, use the experiment history. For alternatives and research priority, use the strategy landscape and the staged research roadmap. Future agents must use the standard benchmark contract and machine-readable records under research/; these do not retroactively upgrade the historical evidence above.