Research status

This record separates implementation checks, scripted effectiveness measurements, and human experience. Passing a correctness test is not an enjoyment result.

Completed experiments

The adaptation-v1 report is complete and passed integrity checks: 8,568 actual encounters, 32 independent tactic-sampling seeds, one deterministic map, and three scripted movement changes. The protocol was specified before this run; the fixtures were already familiar. It is a local engineering experiment, not a public preregistration.

After clockwise training, continued learning gained 18.70 HP of damage per round [16.31, 21.09] over the identical frozen learner against counterclockwise movement, in post-switch rounds 17–24. This meets the declared primary screening criterion. It still trailed the selected fixed policy by 12.14 HP [10.03, 14.53]. Against direction feints, continued learning reduced damage by 4.73 HP [3.89, 5.58] versus frozen memory. Cover produced exactly 72 HP under every tested policy. Brackets are paired seed-bootstrap 95% intervals; secondary comparisons are exploratory and unadjusted.

These results establish useful adaptation in one fixture, a regression in another, and an insensitive damage measure in the cover fixture. Moving tactic probabilities alone is not evidence of improvement. This original run established no human enjoyment, new-map generalization, scout-delivery benefit, or broad superiority over fixed policies. The later three-scenario screen below extends its scope without establishing arbitrary-world generalization.

The first serial execution was interrupted for runtime reasons after six of 32 seeds completed; no full result or statistical conclusion was produced. The same protocol then completed from the beginning with four independent workers. A test compares serial and worker execution of the same trial exactly. The learning algorithm, observations, controllers, sample count and decision threshold were not changed in response to outcomes.

The subsequent reward-attribution experiment tested a single 50/50 individual/team-average damage reward under a separate protocol. It completed 5,376 candidate encounters plus a 264-encounter exact reference replay, reusing verified original comparisons. Do not promote: only two of five predeclared gates passed. Candidate-minus-original late damage was −4.55 HP [−5.91, −3.28] after reversal and −0.66 HP [−1.08, −0.28] against feints. The candidate's continued-minus-frozen learning effect on feints was −4.22 HP [−4.88, −3.56]. Cover was unchanged. All candidate choices/feedback/commits were independently replayed through Wasm. The browser retains the original reward.

Additive credit and fresh scenarios

The additive-credit-v1 experiment preserves full personal damage credit and adds a teammate-only bonus. It completed 5,376 candidate encounters and a 264-encounter exact reference replay. Do not promote: three of five gates passed. Relative to original online learning, late damage gained only +0.42 HP [0.14, 0.75] on feints, below the 3 HP practical threshold, and +0.89 HP [0.28, 1.73] on reversal. Its continued-versus-frozen effect remained negative on feints: −4.78 HP [−5.63, −3.94]. Reversal retained +19.22 HP [17.02, 21.56]. Cover was unchanged.

The separately specified scenario-transfer-v1 screen executed 11,760 actual encounters across three authored cover/spawn layouts and 16 fresh policy seeds. Both rules were evaluated regardless of development outcome. Aggregate original learning benefit was +9.13 HP [7.81, 10.63] on reversal and +3.44 HP [2.94, 4.03] on feints. Additive-minus-original was +1.28 HP [0.72, 1.94] on reversal and +0.03 HP [−0.13, 0.19] on feints. The candidate failed its feint-improvement gate and remains out of the game.

These results show environment dependence: feints hurt continued learning on the original map but helped on the three new layouts, by differing amounts. The aggregate averages each seed across the same three worlds, then bootstraps the 16 seed means. It does not treat 48 world/seed pairs as 48 independent maps. The new fixed policy was selected only on clockwise calibration and is not an oracle for reverse/feint behavior. None of these tests estimates human enjoyment.

All candidate policy decisions were independently replayed through Wasm. The scenario verifier also re-executed all fixed calibration/comparison encounters and one full seed for each reward rule in each world, matching exactly (960 combat replays). Original evidence remains reproducible from the immutable v1 source archive. Across the four scored experiments there are 31,080 encounter executions, excluding reference replays and verification replays; reused original baselines are not counted again.

Synthetic population and interaction diagnostic

The synthetic-population-v1 screen completed 9,920 new encounters with twelve replicate seeds. Each seed combines independent policy, map and bot parameter streams. Four training player families and two map families are separate from the two reserved player families crossed with two reserved map families. Both training arms receive 48 encounters; each reserved history contains twelve repeat, twelve switched-direction and twelve return encounters.

In the late switch window, varied training with continued learning exceeds its own frozen checkpoint by +3.71 HP [2.15, 5.63]. It exceeds narrow training with continued learning by only +0.35 HP [-0.42, 1.50], failing the predefined 3 HP improvement gate. Its difference from the training-selected fixed policy is +1.96 HP [-1.63, 5.56], which does not establish superiority. The decision is do not promote. The current game retains its original configuration.

Frozen policies branch before the whole test history, so these learning effects include updates during the first repeat phase. They do not isolate updates after the switch. The separately specified switch-boundary follow-up below adds that checkpoint. Player clear rate was 82.3% for both varied online and frozen conditions in the late switch window; damage gain alone did not establish a clear-rate benefit.

The feint-interactions-v1 diagnostic adds 96 actual encounters: all eight joint tactic combinations across three known controller styles and four existing worlds. Six matched action changes alter team damage without changing the acting role's observed reward. An offline outcome-table decomposition of original feint probabilities predicts -5.065 HP: ranger -2.709, flanker -2.183 and vanguard -0.172. This is an attribution of probability shifts under a fixed table, not proof of which learning mechanism caused the shifts or an oracle supplied to the live policy.

All 10,016 new measured combats matched full re-execution. The population verifier separately replayed all 29,760 policy decisions and reconstructed rewards from physical evidence. Across the six scored experiment/diagnostic records, there are 41,096 encounter executions, excluding reference and verification replays. The preselected watchable comparison is retained even though all five conditions inflict the same 24 HP in that particular encounter. These synthetic opponents are not human participants.

The now-examined reserved families become development/regression cases. Further tuning requires fresh reserved families for a new confirmatory claim. See the lab guide and verification.

Exact switch control and score-decay ablation

The switch-boundary-v1 follow-up adds 1,152 new frozen encounters and reuses 1,152 prior online outcomes. It reconstructs each checkpoint after repeat round 12 and freezes there, immediately before the strategy switch. The varied-training online-minus-boundary-frozen effect is +2.04 HP [0.33, 3.83]; narrow training gives +2.48 HP [0.44, 4.88]. The primary mean misses the 3 HP practical threshold. These known fixtures are a diagnostic, not untouched validation. The original +3.71 HP estimate remains valid for its earlier freeze point; the estimates have different interventions and should not be treated as independent studies.

The retention-v1 experiment changes only automatic score decay, from 0.025 to 0, with separately trained original/candidate learners. It executes 16,704 new encounters: 4,032 on familiar legacy cases with new policy seeds, and 12,672 on known and fresh synthetic cases. Two fresh movement rules (burst patrol and threat-triggered retreat) are crossed with two fresh map families. Switch and return comparisons each freeze at the exact phase boundary.

Decision: retain original, two of five locked gates pass. On the fresh late-switch aggregate, no-decay minus original is +0.13 HP [-0.13, 0.38]. On original-map feints, it gains +1.25 HP [0.63, 1.88], below the 3 HP gate, while continued learning remains -4.63 HP [-5.88, -3.38] versus its frozen checkpoint. Reversal gains +3.38 HP [1.75, 5.25] versus original in this secondary comparison, and cover remains unchanged. The full outcome pattern does not support installing the change.

The original configuration learns usefully on the new synthetic cases: +4.50 HP [2.35, 6.79] versus its exact switch checkpoint; no decay produces +4.48 HP [2.67, 6.48]. This supports post-switch adaptation in this defined generator, not the proposed retention fix. No-decay return gain versus original is +0.02 HP [-0.79, 0.71]. Learning from new rewards still overwrites sampled scores even when automatic decay is zero; the experiment does not test every kind of memory retention.

The two protocols add 17,856 scored executions. Across eight scored experiment/diagnostic records, the running total is 58,952, excluding reused online outcomes and all reconstruction/verification replays. Full verification records accompany each result. The replay was selected before outcomes and shows all four conditions; it is not a representative aggregate. All newly examined families now become regression fixtures. See the follow-up guide.

Six-direction research program

The completed program adds 72,000 encounters across six prospectively frozen protocols, followed by a separately specified 3,584-encounter opportunity audit. Each study has sixteen seed replicates. The six primary comparisons use nominal 99.1667% paired-bootstrap intervals, with cases and roles aggregated within seed; secondary comparisons remain exploratory at 95%.

• Individual adaptation, without teammates: +0.59 HP [+0.27, +0.97] online versus exact switch-frozen memory. A small signal below the 3 HP practical gate.
• Joint team choices versus independent choices with the same shared reward: −2.44 HP [−6.42, +1.41], with an 11.63 HP loss on one reserved case. No advancement.
• Terrain-specific versus pooled solo-ranger memory: 0 HP [0, 0]. No measured gain.
• Retained versus reset memory on a returning strategy: +0.23 HP [−0.09, +0.61] in the first four encounters. No clear recall advantage.
• Scripted baited versus reset memory: +0.28 HP [+0.05, +0.61], within the −3 HP harm margin. The audit found no reversal requiring a different best ranger action, so this does not establish deception resistance.
• Hardness-selected versus uniform training at equal total encounter budget: −1.13 HP [−2.42, +0.22]. Selection probes count toward cost; no demonstrated efficiency gain.

The original independent learner still gains +6.05 HP [3.94, 8.39] over its own exact frozen checkpoint in the team study (secondary 95% interval). Failure of the joint candidate is not failure of all adaptation.

The post-hoc audit enumerates legal actions, preserves ties and cross-checks 46,080 existing fresh-case outcomes. Team choices change damage in every audited situation, and 56.3% of direction pairs require a different optimum. Several solo tasks have much weaker opportunity; the individual/context/return primary comparators have average offline headroom below their declared 3 HP gate. These are task-design limitations discovered after measurement, not grounds to relax gates retrospectively.

All 75,584 new fights matched full physical re-execution and independent policy/reward checks. The running total across fifteen scored experiment/diagnostic records is 134,536 executions, excluding reused evidence, reconstruction and verification replays. The fieldbook includes 35 preselected recordings reconstructed through 356 matching encounters. All examined cases now become development fixtures. The validated-opportunity follow-up below now tests that requirement. See the full guide and verification.

Validated opportunities and recovery

The opportunity-validation-v2 study qualifies tasks before evaluating learning. Every admitted A/B pair has non-overlapping optimal responses, at least 12 HP loss from retaining any former optimum in either direction, and an observable reward gap of at least 0.15. All 3,072 candidate pairs are retained; 598 qualify, yielding one first-qualified case in 94 of 96 group/seed combinations. No missing seed is replaced. This deliberately selected population is not a typical-player distribution.

The six primary effects are +8.25 HP [4.75, 12.58] for vanguard, +11.39 [6.21, 17.39] for flanker, +6.21 [4.15, 8.67] for ranger, +3.29 [−0.87, 8.95] for joint squad, +3.23 [2.23, 4.36] for flanker terrain memory and +4.00 [2.90, 5.35] for ranger terrain memory. Intervals are nominal 99.167% paired seed bootstraps; groups have 15–16 qualified seeds. The three solo and two context screens pass; joint squad remains inconclusive. Context beats both pooled and shuffled-label memory with matched capacity.

The newly added recovery metric requires three consecutive pre-choice distributions with expected regret at most 35% of the available action range. Of initially displaced learners, 14/15 vanguards, 16/16 flankers, 15/16 rangers and 2/13 joint squads reach it within 32 encounters. Unrecovered cases remain censored; initial competence is reported separately. Independent shared-reward squads recover in 10/13 cases and beat joint squads by 3.85 HP [1.41, 6.23] in an exploratory comparison.

Resetting cells at the externally signaled switch improves solo performance and speeds recovery. Returning to A also favors reset over retained solo memory. This exposes stale-preference interference; it does not implement automatic change detection. Unchanged-situation controls have near-zero mean learning gains, and terrain-specific frozen choices average about 71% optimal probability versus about 50% with pooled or shuffled memory.

The run adds 18,432 admission combats and 27,648 learning/control combats, plus 4,608 separately labeled development combats: 50,688 new executions, all fully replayed. The running total is 185,224 across seventeen experiment/development/diagnostic records, excluding verification and demonstration reconstructions. The viewer preserves the first-seed vanguard admission failure and shows 35 recordings from the other groups, reconstructed through 1,120 matching fights. The previous sources still match their hashes; no game learner was changed. Next evaluate change detection and selective forgetting on a newly frozen validation cohort.

Evidence we can use

Automatic change detection under noisy histories

The change-detection-v1 study adds 69,120 scored executions: 6,144 admission fights and 62,976 learner/control fights. All reproduce exactly, with 69,120 independently reconstructed policy decisions and a separate detector/reset verifier. All 48 role/seed cases qualify; 328 of 1,536 candidate pairs meet admission. Development used 14,432 cached transitions on eleven previously examined cases and adds zero new physical evidence.

Both automatic full reset and selective forgetting fail the declared advancement checks in all three isolated roles. Mean gains over unchanged learning across equally weighted abrupt, gradual and recurring histories are −0.37/−0.30 HP for vanguard, −0.48/−0.43 for flanker and −0.92/−0.69 for ranger (full/selective). Stable losses are larger for vanguard: −3.22/−4.37 HP. Stable false alarms range from 2.93 to 6.05 per 100 fights, above the cap of one. Full intervals and gates are retained in the guide and summary; they use nominal 99.5833% paired seed bootstrap adjustment for twelve improvement/stability comparisons.

The detector raises alarms in 190/192 change windows, but this proximity measure does not establish useful detection: it also resets on stationary surprises and normal reward increases. The unchanged learner still beats frozen memory after abrupt change by 3.50, 6.08 and 6.70 HP for vanguard, flanker and ranger in exploratory comparisons. Privileged reset timing yields modest gains. Do not promote automatic forgetting. Calibrate intervention cost on these now-known development cases before spending another reserve.

Across 18 scored experiment/development/diagnostic records, the running physical execution total is 254,344. Cached policy development, duplicated reference outcomes, verification and visualization reconstructions are excluded. The research compares experimental memory rules; the playable game uses version 0.3.0. The viewer, full verification and clean-extraction kit checks preserve the outcome.

What the game currently learns

It updates preferences among six authored tactics in one shared arena context. It does not invent maneuvers, model an individual player's route history, rewrite combat code, or increase stats. It optimizes authored rewards based largely on damage and survival of the acting enemy; those rewards are not a measure of fun.

Interpretation and next investigation

The post-hoc diagnostic identifies a reward-attribution problem worth testing: against feints, the flanker receives the same reward for either direction, although its direction changes damage dealt by the vanguard. Continued learning loses a useful left-flank preference. Ranger and vanguard preferences also change, so this does not isolate the complete cause of the regression.

The first reward comparison is now complete and unfavorable. Its post-hoc interpretation identifies a concrete tradeoff: the blend adds a weak team contribution signal while reducing the existing reward difference between useful and ineffective individual tactics. The final left-flank preference rises slightly relative to the original, while rush and lead probabilities fall. This is consistent with the weaker damage result but is not a complete causal decomposition.

The additive follow-up is now complete. Preserving personal credit avoided the earlier blend's reversal regression but did not repair the original feint failure. The small observed gain does not meet the predeclared practical improvement threshold. Reward weighting alone has not solved the interaction in these tests. The retention follow-up also fails its improvement gates. The six-direction program has now tested joint choices with a matched-reward control; that candidate also failed. The opportunity audit motivated the validated-opportunity follow-up. That study establishes useful solo/context behavior but leaves team sampling and stale-memory interference unresolved. The noisy change-detection follow-up rejects short-window automatic full/selective resets; detecting reward differences does not by itself justify forgetting. None of these failures proves representation is the sole cause.

No human-player data has been collected for the human study protocol. Two automated production-browser sessions exercise both orders and 52 encounters; their responses are labeled synthetic and excluded from human analysis. Human sample size remains zero. See the protocol and release quick start.

Rules for subsequent iterations

1. Preserve protocols, unfavorable outcomes, incomplete human sessions and exclusion reasons.
2. Select comparison policies and thresholds before reading the new test results. Disclose familiar fixtures and exploratory analysis.
3. Change one substantive mechanism at a time and assign a new protocol/implementation identity. Verify the same source and binary artifacts used for measurement.
4. Report uncertainty at the independent unit: policy seed for this simulator, participant for human sessions, and scenario/map where varied. Repeated frames and rounds do not create independent people or worlds.
5. Show representative demos with aggregate results nearby. Never select a spectacular run and describe it as typical without checking.
6. Keep measurable enemy effectiveness, fairness, comprehension and enjoyment as distinct outcomes.

The emphasis on uncertainty rather than isolated point estimates is consistent with Agarwal et al., Deep Reinforcement Learning at the Edge of the Statistical Precipice. This prototype is a small bandit in one arena; it does not reproduce that paper's broad multi-task benchmark or claim that bootstrap intervals remove its sampling limitations.

See the roadmap for validated learning opportunities, fresh confirmation and reusable releases.

Conservative-intervention development

The completed follow-up reuses all 48 examined change-detection cases for 259,584 cached transitions, with longer stable and recurring histories. It adds zero new scored physical encounters, leaving the physical workload total at 254,344 across eighteen scored records. This additional record is cached development.

Down-only reset, down-only score softening and separate-batch softening all have negative changing-history mean gains in every role. The separate-batch candidate passes the declared stability and stress gates, with 0.93, 0.56 and 0.71 interventions per hundred stable fights for vanguard, flanker and ranger. It fails the 1 HP benefit gate in all roles. Both overlapping-window candidates also fail the pre-run single-outlier stress check. No candidate advances; no fresh validation is consumed.

All cached transitions reproduce. Verification repeats 192 physical table fights and 8,160 trajectory fights; these are not new scored evidence. A separate Python check matches means, pairs, rates, budget and eligibility, without independently recomputing bootstrap intervals. The viewer displays 126 reconstructed fights, with post-results selection disclosed and all-seed data beside them. The article and research report incorporate the outcome.