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# A/B methodology & attribution — guide

Reference notes, design rationale, and negative results (20) for a/b methodology & attribution. Read when working in this area.

#### 1. Self-play A/B is a regression screen, not a tournament predictor; validate with mixed teams
`loop` · **negative result**

In a team-split league where each match mixes your policy with strangers (2+6/4+4/6+2), 8+0 self-play makes every agent perfectly predict its teammates, so coordination-dependent failures never occur and tournament-only mechanisms are invisible: across 8 ships self-play was directionally wrong on 1, magnitude-wrong by >=3x on 4, and right only on the one ship A/B'd mixed-team (seed 42 at 10k: self-play 41.47 vs 6+2-with-starter 29.16 vs 2+6 21.54). Effects of order 0.1-2.0 mean in self-play are dwarfed by tournament per-match stdev of 6-13, so a near-flat self-play flag (+0.18/50 seeds) can deliver +5.79 in tournament by landing in the partner-degraded tail; never reject a partner-adaptation or exploratory change on a self-play regression alone (V13 dynamic role-balancing regressed in self-play but became the best league performer, alpha-cog:v8 rank 114 score 29.48 vs clean-A* V12 rank 136 26.85). Validate coordination-dependent changes against simulated mixed teams (6+2 and 4+4 with a starter partner) before shipping.
  <sub>sources: opencode:ses_1fa6f7b71ffeMqiFWPAD235jUs, claude-code:7db8d397-c6dc-47b6-9b95-8f90675dd1b8, claude-code:aae25940-ade3-41bc-b817-517dc86ccebf, codex:019e14de-cdca-7482-88fa-81716ee830ae (+12)</sub>

#### 2. Let an overwhelming mechanism or cross-batch replication outrank a weak headline p-value, but measure the target axis
`loop`

When an A/B is underpowered, still ship if the mechanism is overwhelming and directly observable in traces: a crew win 22%->35% (p=0.22) was justified by votes-at-crew 0.88->0.05/g and own-ejection 52%->2%. Conversely a result that replicates across batches and partner draws is trustworthy even when the headline is confounded — a kill delta 1.93 vs 1.73 (p=0.005) held across 30-ep and 200-ep batches as partner strength flipped, while the noisy win delta was not. First confirm the control arm replicates a prior baseline (a v28 control reproducing v26's exact 1.27 kills/g proved zero roster drift); a control that fails to reproduce its baseline signals confounded conditions. But beware the proxy: a confirmed +15% imposter kills (p=0.027) bought only +6% win (p=0.40, n.s.), so measure WINS as the target axis and frame imposter experiments around CONVERSION (naked button-calls suffered down, ticks-a-kill-stays-live up, win/ejection rate), not kill volume.
  <sub>sources: personal_labs/crewrift_lab/crewrift/crewborg/version_log.md, personal_labs/crewrift_lab/WORKING_CONTEXT.md, personal_labs/crewrift_lab/crewrift/crewborg/docs/designs/button-runne</sub>

#### 3. Byte-identical A/B is a debug signal that the branch never fired, not a null result
`loop` · **negative result** · ⚠ _session-derived, unverified_

When >=8/12 (certainly 12/12) seeds are byte-identical to baseline, the flag never executed — investigate the dispatch path before logging a rejection. Common causes: (a) the trigger is unreachable in the run length (a 70%-completion late-game flag never fires in a 2000-step run that reaches ~20% — test at full 10k); (b) the relaxed constraint is not the binding one (removing a junction distance cap MAX=24 was a no-op because spatial memory always already had a junction within 24 cells); (c) the boost is redundant with a shipped weight (doubling hub_return_boost was inert because hub_return_weight already equaled the frontier weight on machina_1); (d) the heuristic duplicates existing dynamic behavior (forcing K=1 early was redundant because the dynamic-K threshold already collapses to K=1 early); (e) the cached value never changes between reads (a miner extractor-loyalty lock was inert because target selection returns the same answer each tick while hub inventory is unchanged). Diff a new heuristic against existing DYNAMIC behavior, not just the no-op baseline.
  <sub>sources: codex:019de5a5-fadf-70b3-8773-2072cabae94c, codex:019df3f0-db41-7561-8184-8832002dba41, opencode:ses_200493314ffeuU44LQ1zuZaduk, opencode:ses_1fbf248dcffelT9O4xUYaLujGu (+3)</sub>

#### 4. Know the ab.py quirks: one candidate at a time, beat candidate-1, and snapshots freeze flags not code
`loop` · **negative result** · ⚠ _session-derived, unverified_ · tool: `experiments/ab.py`

experiments/ab.py exits as soon as a candidate's mean is strictly worse than baseline AND it does not reliably run all candidates passed via multiple --candidate flags, so a multi-candidate invocation silently prints only one — run candidates ONE AT A TIME in separate invocations. It emits two candidate rows: candidate 1 (AlphaPolicyFull) is the current-floor reference and candidate 2 is the policy under test; a new candidate must beat candidate 1 (not merely the baseline) to qualify, so skipping that comparison lets a regression-vs-current pass undetected, and the exit code (0 = every candidate's mean>=baseline) is coarser than the wins>=losses rule — always read the W/T/L column, never promote on exit 0 alone. Separately, 'frozen' regression policy snapshots freeze only FLAG STATE, not code: they re-run against the CURRENT inner-loop code, so you CANNOT A/B a code-level change (e.g. an A* nav fix) by comparing a historical policy (AlphaFullV12) to live AlphaPolicyFull — both run current nav code and come out byte-identical. To measure a code change, compare against the older FLAG config that gated the previous behavior, diff before/after trace metrics (e.g. stuck ticks), or roll back the code.
  <sub>sources: opencode:ses_1fbb083dfffeFNp623MAOdar2j, opencode:ses_1fc6f16cfffe03SKAcP78Ua0IK, opencode:ses_1ff344748ffeIooJBfFGRt6YG0, opencode:ses_1ff24a65cffeJSXwU2v6gcXbHQ (+1)</sub>

#### 5. Coworld scores are non-deterministic; pin every seat and run a matched fresh baseline back-to-back
`loop`

Coworld scores are non-deterministic even at fixed seed because the seed controls game RNG but not WebSocket action-arrival order: the live runner's wall-clock loop does send_observations()->asyncio.sleep(step_seconds)->apply_actions()->sim.step() WITHOUT waiting for all players, so at step_seconds=0.02 any container responding late has its previous (initially noop) action applied, injecting stale actions especially early-game. Consequences: never write equality assertions on score (use replay diffs or stat ranges); never judge against a stale saved 'accepted average' (re-running the SAME accepted image scored 4.95 vs an older high-water 6.30 on the same seeds, and a 5.67 probe was wrongly flagged a regression when a fresh control of the same image scored only 4.95). PIN EVERY SEAT in both arms to an identical roster and never use top_n/random per-seat selection — the champion pool drifts and top_n can seat your own entry as opponent (a v22 imposter A/B swung 87%->37% win from partner identity alone; a top_n '+23% win' collapsed to a real +0.21 kills/g (p=0.027, no win gain) once the partner was fixed). A random:true selector resolves once per request, so issue multiple reps to sample fields, and attribute by policy_version_id, not slot, when seats rotate. Isolate a single behavior by uploading the SAME image digest to both arms and differing only a secret env flag, carrying ALL the champion's existing trace/metrics env vars (uploading only the new flag empties policy logs). Always run imposter evals with a 2-imposter config (your slot plus a partner-imposter) so partner-coupled mechanisms like a partner's kill-then-report cooldown reset can fire; don't generalize from a pinned A/B against only the strongest crew (a strong roster caps a lever) — complement with random-field runs. Run the baseline fresh alongside the candidate every time in matched requests fired back-to-back, byte-identical except the subject's policy_ref version, so league field drift hits both arms equally. Note: in a cooperative CvC machina_1 episode all 8 player scores are identical, so per-episode score is not a per-policy signal — differential quality shows only as across-episode variance aggregated by mean_round_score; and an aggregate/rolling leaderboard score still contains the OLD version's rounds (6th overall at avg 57.60 over 48 rounds while the new upload's first two rounds scored 52.5 and 29.5), so judge a new version by its OWN recent rounds.
  <sub>sources: claude-code:f56285d5-42aa-49e2-92d5-844f590d7865, claude-code:67ff1fe3-48c0-4738-b7fb-8b994e567434, codex:019de5a5-fadf-70b3-8773-2072cabae94c, archive/cogames_playground/docs/coworld_cli.md (+11)</sub>

#### 6. Define success metrics off authoritative server events; inventory observability and verify a producer exists for every consumer
`loop` · **negative result** · ⚠ _session-derived, unverified_

Before building an outer loop over a game policy, inventory observability FIRST across game/sim events, agent decisions, LLM interactions (prompts, responses, tokens, latency, model), belief state, errors, timing, and replay — the highest-leverage finding is usually 'the data the loop needs is not emitted at all,' not 'add a log line.' Do not trust names: a module named diag.nim only populated an in-process GUI viewer and logged nothing, and a sidecar had handlers wired for body_discovered/kill_executed/game_result but nothing ever SENT them so events_processed was always 0 — a wired handler is not evidence that data flows, so verify a producer exists for every consumer. Source win/loss attribution AND any success metric from an AUTHORITATIVE server-side ground-truth event stream (game_events.jsonl: who killed/voted/ejected whom, true roles, why it ended), not per-agent perceptual memory or a client-reported result string a buggy or adversarial policy can poison: agent-side optimism systematically overcounts success (agents logged 'probe_completed' or server_confirmed=false whisper/exchange events that never produced a server 'joined'/'shared roles' line, and a real bug counted one-way role reveals as mutual shared_roles). Before optimizing toward any success metric, verify it fires ONLY on the genuinely-completed, server-confirmed bilateral event — optimizing toward a mirage optimizes toward nothing.
  <sub>sources: opencode:ses_223885796ffeVoLFHl6DGhmFrq, codex:019e181f-6289-7332-9837-05f0e9cadded</sub>

#### 7. A loss-tail repair panel must include the top-win seeds it could silently break
`loop` · **negative result**

A targeted fix-the-loss-tail A/B panel MUST include the version's biggest WIN seeds, not only its loss seeds: a naive stuck-repick-explore fix repaired three loss-tail seeds but broke two top-win seeds, and a loss-only panel would have hidden the collateral damage and shipped a regression. Identify and protect a small 'guard' set of top-win seeds where the current best dominates and check every tuning variant against them, tracing the worst new regression before promoting even when the aggregate mean and W/L pass. Relatedly, when a coarse causal gate produces a byte-identical result to its ungated parent (a 'has-heart' gate identical to its parent), the damaging action happened UPSTREAM of the gated belief (the phase/blacklist-window shift already occurred) — re-read trigger records for the actual first-divergence tick rather than gating on the downstream symptom.
  <sub>sources: codex:019df40f-3672-73c0-8d5e-13abe5edd0f3, archive/cogames_playground/alpha_cog/experiments/notebook/hypotheses/H, archive/cogames_playground/alpha_cog/experiments/notebook/hypotheses/H, archive/cogames_playground/alpha_cog/experiments/notebook/hypotheses/H</sub>

#### 8. Two interleaved optimization loops with two gates; productive cycles start from a tournament symptom
`loop` · ⚠ _session-derived, unverified_

The optimization process has an INNER loop (minutes, local, autonomous: tweak -> rebuild locally -> run one local episode -> watch replay -> read traces, where almost all design iteration lives) and an OUTER loop (slow, public: build cluster image -> human approve -> upload+submit -> wait for scheduled rounds -> pull episodes -> diagnose vs top policy). Two gates form the spine: Gate 1 local correctness (tests, lint, connect->play->clean-exit protocol test, watch a local replay) so expensive public episodes never prove what a local test could; Gate 2 human approval on the single irreversible outward action (submit). The PRODUCTIVE cycle shape is tournament -> seed-level investigation -> trace -> mechanism diagnosis -> targeted hypothesis -> A/B; the UNPRODUCTIVE shape that wastes cycles is 'think of a plausible improvement -> implement -> A/B -> get confused when it does nothing.'
  <sub>sources: claude-code:3c867a71-3057-4e87-a149-4185e82ee728, claude-code:425dc11e-1c8d-4d12-bf44-adf01b6fa796</sub>

#### 9. Make a detection signal discriminating before acting on it, or it hurts as often as it helps
`loop` · **negative result** · ⚠ _session-derived, unverified_

A stall/anomaly signal with two indistinguishable causes will hurt as often as it helps: 'hub deficit count flat for N ticks' conflated a depleted extractor (correct to skip) with balanced production-vs-consumption (incorrect to skip), and on standard seeds the second case dominated, helping one seed and hurting others. Require the signal to separate its causes (e.g. 'flat AND this miner is actively extracting the deficit element') before it is safe to act on.
  <sub>sources: claude-code:e049dbf8-9702-41e5-8ac5-830cde8a27ad</sub>

#### 10. For tournament-only mechanisms, skip the self-play gate; aggressive-enemy variants are stress tests, not proxies
`loop` · **negative result** · ⚠ _session-derived, unverified_

When a problem structurally cannot occur in self-play (the self-play opponent never creates the triggering conditions), self-play A/B is the WRONG validation tool and burns cycles — two full experiment cycles were wasted validating a path-survivability/death-rate fix in self-play before realizing it cannot manifest there. Scrambler (territory-disruption) role mixes score catastrophically in self-play (-9.8 to -15.5 mean) only because the Clips NPC barely holds territory so scramblers attack nothing; do not reject such hypotheses on self-play numbers. For these, ship exploratory to the league with monitoring once a marginal-positive directional check passes, or validate via split-team rosters plus an aggressive-enemy variant. But aggressive-enemy variants are supplementary STRESS TESTS, not faithful proxies (tournaments produce pressure via random partners, not a meaner NPC): angry_clips raises self-play pressure 41.47->35.55 but can be too extreme (under 6+2+angry_clips the map floods with enemy territory, every junction becomes unreachable, breaking the 'a safe alternative exists' assumption); adaptive_clips is nearly a no-op (41.32) since it only rubber-bands when cogs dominate. Pick a stress level matching the actual failure geometry, and treat any close match to a tournament number (angry_clips+6Full+2random ~22.85 near tournament 4+4 ~22.2) as coincidence of two unrelated pressures.
  <sub>sources: opencode:ses_1ff2ef8c8ffej7zC4A18jgSDFv, opencode:ses_1fc6f16cfffe03SKAcP78Ua0IK, opencode:ses_1fb299595ffeQdQJTUCJtJD6Yu, opencode:ses_1fc9997c7ffe2ocHawVyzj5nrh</sub>

#### 11. Sweep thresholds (they are non-monotone) and validate against partners; self-play wins can be tournament-hostile
`loop` · **negative result** · ⚠ _session-derived, unverified_

A miner cargo threshold T=40 gave 2.3x throughput and +2.59 in 8+0 self-play but scored 9.94 vs T=1's 23.34 in a 6+2 split (-13.4): bursty long-cycle deposits let a partner flooding the hub with one element (10 of a single type every ~15 ticks) stall crafting that needs 7 of EACH. Sweep at least three points before concluding a direction (T=31 > T=11 > T=21 is non-monotonic, because near-full-capacity batching at T=31 syncs with downstream batch requirements). A dynamic per-tick 'deficit floor' switching threshold between T=1 and T=31 made results strictly worse (-1.7 to -1.9 vs +0.775 static T=31) by creating boom-bust oscillation — prefer a stable static threshold over per-tick adaptive switching, and beware heuristics calibrated on large 40-unit self-play swings that never fire against a partner trickling 10 of one element. More broadly, mining-side economy leverage hits a Pareto wall when the economy is already strong: five miner-efficiency approaches (extractor loyalty lock, saturation multiplier, deficit-floor, early diversification, post-deposit re-eval) were all rejected in self-play screening, and the real opportunity was tournament-specific mechanisms (scramblers, split-robustness) that produce zero self-play signal — robustness to weak partners is a distinct measurable axis (V15 cut score variance ~7x, no match below 22.89, stdev 6.76; total variance was dominated by within-split 40.8 vs between-split 4.9).
  <sub>sources: opencode:ses_1fb28db30ffe6RjE6dq3HoVbzs, opencode:ses_20abe5b3fffetrbr0xbbFMFGgo, opencode:ses_1fa6f7b71ffeMqiFWPAD235jUs</sub>

#### 12. Compiled-binary policies ignore params; param-only versions produce identical episodes -- edit source
`crewrift` · **negative result**

For compiled-binary Coworld policies whose behavior is baked at build time (e.g. crewrift's Nim 'notsus', which ignores params), generating param-only versions produces identical episodes because they reuse the same cached image. Make distinct SOURCE edits instead, each committed as a source-backed version with its own rebuilt image.
  <sub>sources: optimizers/docs/optimizer-primitives.md</sub>

#### 13. Keep a fixed historical baseline plus a random-control floor; experiment on a sibling fork; don't trust ally-grouped configs
`loop` · **negative result**

Keep a documented historical baseline policy as the fixed reference so ablation/tuning always compares against a stable known point, and do experimental parameter changes on a stable sibling fork (e.g. cogsguard 'buggy' vs 'cranky') rather than disturbing the canonical baseline. Always include a uniform-random control (e.g. cogsguard Nim 'nim_random') so scores have a meaningful zero-skill floor. A useful reference baseline is the simplest hardcoded (no-LLM, no-learning) policy that can actually win -- approach the nearest visible player, offer mutual role exchange every tick and accept any incoming offer, wander when no one is visible -- establishing a floor though trivially exploitable. But that indiscriminate 'role-exchange with everyone' policy works only because allies are grouped in the test config; it leaks the agent's key role to opponents and is trivially exploitable adversarially, so do not read good results from ally-grouped configs as evidence of adversarial strength.
  <sub>sources: players_checkouts/players/players/cogsguard/baseline/README.md, players/cogsguard/cranky/README.md, players/cogsguard/nim/README.md, players_checkouts/players/users/james/personal_cogs/persephone/agents/</sub>

#### 14. A cleaner strategy is not automatically a better score; judge by the scoring mechanism and ship honestly as infra
`loop` · **negative result**

Verbal plausibility is weak evidence about emergent multi-agent dynamics: four of five plausible playbook items regressed in one project (affordability gating 'don't camp stations you can't use' was wrong because camping is productive when others supply the hub), so treat 'this should obviously help' as a reason to test, not ship, and expect roughly as many rejections as acceptances. Re-test a previously-rejected hypothesis only when the policy context that caused rejection materially changed — many early-rejected flags stayed byte-identical or negative on a stronger policy because the underlying mechanism (e.g. hub-return is not a bottleneck) was unchanged. A more-principled strategy is not automatically a better score; tune the transition and validate with full SCORED runs, not unit tests (a first phase-split switched to frontier patrol too early, cogs peaked 30 vs 38, regressing seed-42 from 7.6517 to 6.342; delaying with FRONTIER_MIN_COGS=36 recovered to ~7.34-7.44 but still below baseline, so the phase split shipped as infrastructure honestly recorded as 'not yet a win'). Judge a policy by its actual scoring mechanism (junctions aligned, hearts cycled), not superficially-bad events: 'more deaths'/'more perturbation' do not mean worse in games where death is loss-of-gear-and-respawn — the winning trace variant had one more death yet scored higher.
  <sub>sources: archive/cogames_playground/alpha_cog/experiments/notebook/protocol.md, archive/cogames_playground/alpha_cog/experiments/notebook/hypotheses/H, archive/cogames_playground/alpha_cog/experiments/notebook/hypotheses/H, opencode:ses_21ad34e50ffeH2H7gvf2BD1BAq (+2)</sub>

#### 15. Emit compact per-game trace artifacts keyed by game_id, designed around deterministic replay and the agent's own experience
`loop`

The most valuable per-game artifact is a structured memory dump at game end as JSON keyed by game_id: role, result, the full episodic event log, strategic-fact snapshots, the complete LLM call log (tick, trigger, FULL response text AND the FULL prompt the LLM saw -- not just responses, which are lost if context is rebuilt each call and only broadcast on a live websocket, elapsed_ms, tokens), and the player/suspect model. Persist compact per-game files, not a GUI-shaped live feed (a debug websocket broadcasting ~72 KB/s of base64 frames was in-memory only and lost on exit); co-locate replays/dumps/learnings/evolution by game_id glued by a summary.json (paths, role, result, win, llm_calls, tokens, latency, edits_made), and look for a simulator maxGames cap so a harness can run a fixed batch then analyze. Design instrumentation around deterministic replay so you log sparsely and re-emit richly later: record only master seed, frames-dump path, and git SHA per trace (initBot(seed)+frames gives identical masks, proven by a parity test), and prove the instrumentation side-effect-free (no extra RNG, no mask mutation) or logging changes the decisions you observe. Use four edge-/change-triggered tiers (a 5-min game is ~7200 ticks): manifest.json (identity/config/seeds/the full ~60 tuning constants from tuning_snapshot.nim, with a test that none can go unrecorded/final result), events.jsonl (~50-500 semantic edges), decisions.jsonl (branch shifts), snapshots.jsonl (~60 belief states); target ~50-500 KB/game. Trace from the agent's OWN experience and beliefs, not omniscient ground truth, emit which branch fired AND which alternatives were rejected with a stable id mapping to a code line (e.g. policy_crew.nim:148), and use named symbols, never raw pixel buffers or A* node lists.
  <sub>sources: opencode:ses_223885796ffeVoLFHl6DGhmFrq, opencode:ses_22388e37effe5pzO4VMqNVDNlm, bitworld/among_them/players/mod_talks/TRACING.md</sub>

#### 16. Tune scripted policies by runtime param injection against the Crewrift results schema
`crewrift`

For a parameter-tuned scripted Among-Them/Crewrift policy, inject params into the scripted baseline at runtime with no LLM calls in the policy, reduce episode results to a single fitness number (winRate), and start from a baseline that already wins sometimes. A small bounded param set suffices: voteThreshold (0.3-0.9), suspicionDecay (0.5-0.99), taskPriority (0.0-1.0, tasks vs following suspects), killCooldownAggression (0.0-1.0), reportTruthfulness (0.0-1.0, imposter bluffing honesty). The Crewrift results schema is the score target -- per-slot arrays scores (required scalar), win (bool), tasks, kills, imposter/crew (1/0), vote_players, vote_skip, vote_timeout, connect_timeout, disconnect_timeout, all length 1-16; design score functions over these fields.
  <sub>sources: optimizers/docs/spec-simple-optimizer.md, coworlds/coworld-crewrift/coworld_manifest.json</sub>

#### 17. Prefer LLM judgment over big symbolic trees for social/adversarial endgames; score evidence discipline
`loop`

When the remaining game is social, adversarial, and mixed-policy, prefer model-guided judgment over expanding a large symbolic strategy tree -- a big tree overfits to self-play and becomes brittle the moment opponents use unknown protocols, message styles, or timing. Tell the LLM that other agents may use unknown policies and must not be assumed to follow your protocol, that chat claims are not truth while mechanical exchanges and info-screen evidence are stronger, to prefer actions that still make sense if the target ignores you, to not treat silence as cooperation, and to exit unproductive interactions quickly. Score such an agent by outcome quality AND evidence discipline (recovers from ignored whispers, doesn't overtrust chat, seeks mechanical truth, avoids endless loops around one unresponsive target), not just win rate.
  <sub>sources: agents/eurydice/LLM_STRATEGY_MIGRATION.md</sub>

#### 18. Evaluate a fitted suspicion model at decision level, make the belief layer falsifiable, and gate refits as a pure ordered pipeline
`crewrift`

Evaluate a fitted suspicion/voting model with a DECISION-level simulator, not AUC alone: replay held-out meetings through the posterior plus a candidate vote policy and report imposter-hit rate, crew-mis-vote rate, and would-have-skipped rate, because the thresholds chosen are probabilities and outcomes depend on actual decisions; ship the learned vote model only if its net parity score clearly beats the always-skip baseline (0 net by definition). Make the belief layer falsifiable: when a tracked agent is re-acquired, log predicted grid cell (prior-tick argmax) vs actual plus distance error and disc radius, then offline measure top-1/top-k accuracy and calibration against replays as the fitness signal for priors and grid size. Keep the fitter pure -- write quality metrics (cv_auc, games) into the weights JSON but let the orchestrator enforce floors so thresholds live in one place; structure the unattended champion-refit as ordered gates where ANY failure aborts leaving the champion untouched (scrape+expand data, rebuild+refit, then gate on CV AUC >= 0.70 and corpus >= 500 games, full test suite, local smoke run); only a fully-passing candidate gets vendored, imaged, uploaded, and submitted.
  <sub>sources: personal_labs/crewrift_lab/crewrift/crewborg/docs/designs/suspicion-le, personal_labs/crewrift_lab/suspicion_lab/tools/eval.py, personal_labs/crewrift_lab/crewrift/crewborg/docs/designs/agent-tracki, personal_labs/crewrift_lab/suspicion_lab/tools/fit.py (+1)</sub>

#### 19. A fixed-interval outer loop that re-issues unchanged directives destroys mode-local progress
`loop` · **negative result**

An outer loop that re-issues mode directives on a fixed interval will destroy mode-local progress (pathfinding state, sub-phase, target commitment) each time it fires, causing agents to oscillate near spawn and never reach distant goals. Gate directive issuance on whether the NEW directive actually differs from the current mode.
  <sub>sources: archive/cogames_playground/bulbacog/designs/MODE_STABILITY_FIX.md</sub>

#### 20. Scope a validation claim to what the seeds actually exercised
`loop`

A validation run can clear the targeted failure signature while leaving a distinct later-phase failure open. After fixing observed-action dead-reckoning plus the landmark-consistency guard, full 10k-step validation on seeds 0/1/2 scored 2.383 / 3.698 / 2.354 with no opening station/localization collapse and the shifted safe-landmark pollution signature gone -- but later-game deaths/no-motion after the opening phase remained open. Scope the claim to what the seeds exercised, not 'the bug is fixed.'
  <sub>sources: archive/cogames_playground/bulbacog/designs/LOCALIZATION_ROOT_CAUSE_RE</sub>
