Deep slate report — 20261006

1. Evidence receipt and gaps

All 7 source_manifest entries are marked loaded:

• prediction review — 19,282 bytes; official outcomes and scoring errors.
• forensic deep audit — 45,953 bytes; probability, provenance, starter, and decision contracts.
• continuous learning — 280,749 bytes; pipeline-stage quality, calibration, probability lineage, score distribution, and starter comparisons.
• detailed report — 57,951 bytes; game and simulation rendering.
• ultra detailed player audit — 3,503,264 bytes; player-level prediction trace.
• structural audit — 240,335 bytes; invariant findings.
• integrity revision audit — 824,693 bytes; structural audits of seven post-start game revisions.

The diagnosis says 2 expected, 2 reviewed, and 2 structurally audited games; it also reports 2 continuous-learning games and starter comparisons for both. The coverage matrix is complete on those counts. The per-game audits both pass, and the revision audit is reported as loaded. No source-manifest entry is marked missing.

Important limitations and inconsistencies in the supplied evidence:

• There are only two settled games on this slate. Calibration and game-level conclusions are correspondingly fragile, even though some findings have separately escalated across slates.
• No source-labelled moneyline is available for the market cross-check. The market is also null in both game decision internals.
• The diagnosis provides selected player-level lines and aggregate player metrics, not a complete independently verifiable player-results feed. No unreported player results are inferred here.
• The MIL@SD probability lineage is internally unresolved: it reports a 0.6142 calibrated/governed pick probability but a 0.56643 published pick probability, a −4.777 percentage-point delta without a recorded transformation. This is a contract/evidence failure; it does not establish that the governor itself was bypassed.
• The MIL probability fields also do not form one transparently documented sequence: the lineage’s raw model pick probability is 0.6262, while the game trace’s raw pick probability is 0.646289; the trace separately records a starter-experience adjustment from 0.593317 to 0.578153. The evidence does not document how those values reconcile to the published 0.56643.
• For LAD@ATL, the blend diagnostic records a home-favouring blend probability of 0.568066 and a trained home probability of 0.641512, but the published home probability is 0.494846. The blend is marked as having changed the flagged winner, but that side did not survive publication. This is a recorded intermediate-to-final reversal, not evidence by itself of an unrecorded probability transformation.

2. Executive diagnosis

Winner accuracy: Both games were called correctly: 2/2 (100%). That is a slate result, not proof of reliable forecasting. The validated historical winner accuracy is 0.600414, with walk-forward accuracy 0.570149.

Calibration quality: The two published picks both won, while their pick-side published probabilities were 0.505154 and 0.56643. The slate-level weighted absolute calibration error is reported as 0.4642. The bucket table labels both observations underconfident because its definition is average published confidence minus observed hit rate; with one hit in each bucket, those two observations cannot establish a stable calibration curve. The MIL publication discrepancy is a separate critical lineage defect. A “lower confidence caps” action in the self-assessment should not be read as an established direction from these two outcomes: the current bucket observations are labelled underconfident, and the persistent calibration finding calls for a shadow experiment, not an untested production change.

Score accuracy: Both predicted totals were too high: LAD@ATL predicted 7, actual 4; MIL@SD predicted 9, actual 7. The supplied team-run absolute-error figures are 3 and 2, respectively. Both games had positive total-run bias, +3 and +2. The validated run models have near-zero holdout explanatory power: home-run R² 0.002143, away-run R² 0.030936, and total-run R² 0.002415 across 2,415 rows. Scores are weak estimates even when the winner is right.

Starter accuracy: All four starter identities matched. The two starters in LAD@ATL had ER errors of 0 and 1; the MIL@SD starters had ER errors of 3 and 1. The slate-level matchup pattern summarizes four starter comparisons as mean ERA error −1.4, with starter projections overall too pessimistic on this slate. Individual starter lines vary substantially, so that aggregate is not a basis for changing a starter lever by itself.

Artifact integrity: Both per-game structural audits pass with zero critical, error, or warning findings; each has one informational item. The overall structural summary is 0 critical, 0 error, 0 warning, and 2 info. The per-game diagnostics call both saved forecast artifacts clean. However, those clean file audits do not resolve the MIL probability-lineage contract failure. Audit coverage is complete, but the slate is not contract-clean.

Causal issue register reconciliation:

• Critical — unexplained_probability_publication_delta; MIL@SD. Evidence: one game has an unexplained calibrated-to-published change of at least 2 percentage points; the measured change is −4.777 points. Action: block promotion until the missing transformation is recorded and reconciled. Guardrail: do not assume the governor was bypassed before tracing pick-side math.
• High — single_slate_calibration_instability; LAD@ATL and MIL@SD. Evidence: weighted absolute calibration error 0.4642 across two games. Action: watch the same buckets across the rolling window before changing calibration weight. Guardrail: this slate is too small to establish a stable calibration curve. Separately, the cross-slate record says this finding has persisted for four consecutive slates; that persistence warrants a bounded shadow experiment, not treating the single-slate estimate as precise.
• High — weak_run_model_signal; both games. Evidence: home/away/total R² = 0.0021/0.0309/0.0024. Action: investigate features and target in an isolated training backtest. Guardrail: low positive R² does not make exact scores reliable or justify tuning score tails as a substitute for improving run signal.
• Info — complete_slate_audit_coverage; both games. Evidence: 2/2 structurally audited. Action: retain per-game audit receipts. Guardrail: complete coverage does not cancel findings inside audited games.
• Info — simulation_inert_on_slate; both games. Evidence: zero flip candidates and zero published flips. Action: measure simulation contribution across rolling slates, separating score realization from winner flipping. Guardrail: zero winner flips is not itself a defect, nor proof that no score reconciliation occurred. The separately escalated 11-slate pattern and simulation implementation diagnosis make this an actionable diagnostic/code issue.

3. Every game

LAD@ATL

• Predicted and actual: LAD 4, ATL 3; actual LAD 3, ATL 1. LAD won, and the predicted winner was correct. This is a correct-winner/wrong-score game.
• Probability and conviction: Published pick-side probability for away LAD was 0.505154; published home probability was 0.494846. The system edge was 0.0103 in LAD’s direction, and the conviction bucket was toss-up. Brier score: 0.244873.
• Score errors: Away-run error 1; home-run error 2; supplied team-run absolute error 3. Predicted total 7 versus actual total 4: total bias +3. The model margin was LAD by 1; actual margin was LAD by 2, with signed margin error −1 as recorded in the margin distribution.
• Starter lines:
• LAD, Yoshinobu Yamamoto: projected 1 ER, 19 outs, 1.42 ERA; actual 1 ER, 21 outs, 1.29 ERA. ER error 0; ERA error −0.13. Identity matched.
• ATL, Chris Sale: projected 2 ER, 18 outs, 3.00 ERA; actual 3 ER, 15 outs, 5.40 ERA. ER error +1; ERA error +2.40. Identity matched.
• Pregame edges, home minus away: Season −0.6096; recent −0.314; pitcher −0.0609; composite −0.7278. Those supplied edges favoured LAD overall. Season-quality score adjustment was −0.256 toward the stronger team; recent quality edge was −0.664 and season quality edge −0.5802.
• Confidence/recency controls: Calibration sample size 566; reported empirical hit rate 0.5477. The trace records raw pick probability 0.5289, governed pick probability 0.5071, and governor applied. Recency guardrail applied; discount factor is null and no recency reason is supplied. Starter-experience shrink was not applied (minimum 28 games; shrink factor 1.0). Lineage records raw model pick probability 0.5, calibrated probability 0.5071, score-coherence probability 0.507133, and published probability 0.505154; it says the publication matches the calibrated/governed value, with no unexplained material delta. The different raw-probability fields (0.5 in lineage and 0.5289 in the game trace) are not reconciled in the supplied record.
• Score path and audit: Pipeline-stage quality shows historical ML at 0.5 winner accuracy, then variance-applied still at 0.5. At the transition to enhanced prediction the direction changed ATL → LAD; the transition improved LAD@ATL, and overall winner accuracy rose from 0.5 to 1.0. KPI, embedded Savant run environment, fundamental-edge target review, capped target, simulation result, and published final made no further measured change. Numeric intermediate score lines are not supplied. Structural audit: PASS, risk 0, 108 good, 1 info, no critical/error/warning findings. Forecast-file integrity is described as clean.
• Player-level and run-environment evidence: Pitcher run factors were 0.9802 for LAD runs versus ATL pitching and 0.9193 for ATL runs versus LAD pitching; Savant adjustment was applied. The game diagnostic says total runs were over-projected by 3 and score-volatility action was no_change. LAD’s lineup scored 2 home runs with lineup run delta −1; ATL’s lineup scored 0 home runs with lineup run delta −2. Bullpen ER is recorded as 0 for LAD and 0.0 for ATL. The listed player deviations include Freddie Freeman (+1.26 run impact; 1-for-4, 1 HR), Mookie Betts (+0.94; 2-for-5), Andy Pages (+0.94; 2-for-4), Miguel Rojas (−1.25; 0-for-3), and Matt Olson (−0.93; 1-for-4). Contact-quality review marks Freeman, Betts, and Pages as learnable above-average/elite profiles; these individual deviations are not enough to explain the full score miss.
• Audit findings and causes: No per-game structural findings. The primary/secondary driver fields are null. The best-supported diagnosis is a run-total overprojection, with a material ATL offensive shortfall relative to projection (notably lineup run delta −2), plus player-level variance. This did not cause a winner miss. The blend-stage probability reversal described in Section 1 is an intermediate probability-path finding; the published pick still favoured LAD.

MIL@SD

• Predicted and actual: MIL 4, SD 5; actual MIL 3, SD 4. SD won, and the predicted winner was correct. This is a correct-winner/wrong-score game.
• Probability and conviction: Published pick-side probability for home SD was 0.56643; published home-minus-away edge +0.1329, conviction moderate. This is a moderate edge, not a near coin flip. Brier score: 0.187983.
• Score errors: Away-run error 1; home-run error 1; supplied team-run absolute error 2. Predicted total 9 versus actual total 7: total bias +2. Predicted and actual margin were both SD by 1; signed margin error 0.
• Starter lines:
• MIL, Dustin May: projected 5 ER, 12 outs, 11.25 ERA; actual 2 ER, 9 outs, 6.00 ERA. ER error −3; ERA error −5.25. Identity matched.
• SD, Nick Pivetta: projected 3 ER, 12 outs, 6.75 ERA; actual 2 ER, 13 outs, 4.15 ERA. ER error −1; ERA error −2.60. Identity matched. Pivetta had 9 prior appearances in the feed and is flagged as a thin-history starter; the evidence cautions that this is season-feed history, not career history.
• Pregame edges, home minus away: Season −0.723; recent +0.334; pitcher +0.0494; composite −0.0255. Season evidence favoured MIL; recent and pitcher edges favoured SD; composite was nearly neutral and slightly favoured MIL. The model nevertheless published SD as a moderate-confidence pick. Season margin adjustment was −0.3037; recent quality edge +0.124 and season quality edge −1.179.
• Confidence/recency controls and lineage: Calibration sample size 357; reported empirical hit rate 0.5714. The game trace gives raw pick probability 0.646289, governed probability 0.6142, and governor applied. Starter-experience shrink was applied: probability before 0.593317, after 0.578153, shrink factor 0.8375; winner unchanged. Recency guardrail was not applied and discount factor is null. The lineage instead reports raw model probability 0.6262, calibrated/governed probability 0.6142, score-coherence probability 0.593317, and published pick probability 0.56643. Its transformation field explicitly says no recorded transformation explains the publication delta. The −0.04777 published-minus-calibrated difference is unresolved; the probability record does not show how the trace’s starter-experience adjustment and score-coherence value yield the published result.
• Score path and audit: Historical ML and variance-applied winner accuracy were both 0.5. Enhanced prediction changed the LAD@ATL direction and improved that game; later stages through published final showed no further changes. Thus MIL’s SD winner call survived, while the overall stage result was 2/2. Structural audit: PASS, risk 0, 109 good, 1 info, and no critical/error/warning findings. The clean file audit does not cure the probability-lineage defect.
• Player-level and run-environment evidence: Pitcher run factors were 0.9442 for MIL and 0.9936 for SD; Savant adjustment was applied. Score-volatility action was no_change. Each lineup had lineup run delta −1; bullpen ER was 1 for each side. The matchup breakdown labels both sides closer to variance. May’s three fewer ER than projected is the registered contributing factor. Listed player deviations include William Contreras (+2.34; 3-for-4, 1 HR), Dustin Harris (−1.56; 0-for-2), Jake Bauers (−1.54; 0-for-4), Garrett Mitchell (−1.11; 0-for-4), and Jake Cronenworth (+1.07; 2-for-2, 1 HR). The learning review identifies Contreras as a strong hitter the projection may have under-rated, but individual events do not establish a general lineup adjustment.
• Audit findings and causes: No per-game structural findings. Primary/secondary driver fields are null. The run miss reflects a total overprojection and starter uncertainty/realization: May and Pivetta each allowed fewer ER than projected, while both lineup deltas were −1. That is a score miss, not a winner miss. Separately, the unexplained probability publication delta is the game’s critical contract defect.

4. Miss reconstruction

There were no final winner losses: both published winners were correct. Therefore there is no final loss for which to identify a wrong-result prediction stage. This must not be substituted for a claim of good score or probability quality.

The measured intermediate winner-direction regression is in LAD@ATL: historical ML and variance-applied stages were 0.5 winner-accurate, and variance-applied had no winner-hit improvement. The transition from variance-applied to enhanced prediction changed LAD@ATL ATL → LAD, improving the winner result; later stages retained that direction. This is a real intermediate direction change, but the diagnosis does not provide numeric per-stage score lines or enough evidence to assign it to a specific bad input, weighting, or player adjustment. Later recovery does not erase it.

Across the two games:

• Bad input: No bad starter identity is indicated; identity matched for all four. Market input is unavailable. The MIL publication math is incomplete, but that is a publication-lineage defect, not proof that an input value was wrong.
• Bad weighting: The slate alone cannot establish incorrect season/recent/pitcher weights. MIL’s season edge favoured MIL while recent and pitcher edges favoured SD; LAD’s composite favoured LAD. The stage transition that recovered LAD is measured, but the supplied fields do not identify the responsible weight.
• Calibration: MIL has a documented unexplained 4.777-point calibrated-to-published delta. Across the slate, two one-game buckets both hit, which yields a very high absolute calibration error under the stated definition but cannot estimate a reliable curve. The four-slate calibration escalation is a broader reason to test a bounded shadow change.
• Starter error: Starter ER projections were high relative to actual ER for both MIL@SD starters and for the slate in aggregate. In LAD@ATL, Yamamoto’s ER projection was exact; Sale allowed one more ER than projected. The largest individual ER discrepancy was May, projected 5 and actual 2. These facts affect score analysis but did not change either winner call.
• Offense/bullpen miss: LAD@ATL’s ATL lineup run delta was −2; the other three side-level lineup deltas were −1 each. Bullpen ER was 0/0 in LAD@ATL and 1/1 in MIL@SD. The evidence supports lineup underproduction on this slate, but not a universal lineup-weight adjustment.
• Run environment: Both totals were overprojected (+3 and +2). The slate player metrics also show overprojection in AB, H, RBI, R, and 2B, while BB, SO, and HR totals were underprojected. Those are broad one-slate diagnostics, not evidence for shifting all run means by a fixed amount.
• Irreducible variance: The player forensics classify three of four side assessments as closer to variance and one as offense; the MIL side descriptions say neither side broke materially. This is a reasonable residual explanation for individual outcomes, not a substitute for the systematic run-model and probability-lineage findings.

Pipeline stages and transitions, all audited (each stage has 2 games):

Variance application regressed team-run MAE by +0.3317 and total-run MAE by +0.6634 relative to historical ML; margin MAE increased by 0.0021. The later enhanced-prediction transition improved team-run MAE by 0.5 and margin MAE by 1.0 and changed one winner direction. All subsequent score-stage transitions were measured as unchanged. This later recovery does not erase the variance-stage regression. The simulation stage had no measured score-stage improvement on this slate.

5. Cross-game counterfactuals

Each listed tension entry is accounted for:

1. score.variance_multiplier / score.variance_floor (widen run distributions): Helps: none recorded. Hurts: none recorded. Net slate evidence: 0 helped, 0 hurt. This entry does not establish that widening improves either game or fix their overprojected run means. The separate stage-quality comparison shows variance-applied run-error regression, so any variance experiment should be a shadow test, not a direct production change.
2. player.pitcher.v4 form weights / player.pitcher_prior_games: Helps: MIL@SD, where the starter ER was off by 3. Hurts: LAD@ATL, where Yamamoto’s ER projection was exact and the starter projection was described as accurate within one ER. Net evidence: one help, one risk; no cross-game case for a global form-weight change.
3. recent.* / season.* run-mean weighting: Helps: none recorded. Hurts: MIL@SD, where team runs were already close (off by 2 total supplied team-run absolute error) and reweighting could disturb them. Net evidence: no slate support for changing these weights.

Tempting one-game fixes to avoid: Do not globally raise or lower pitcher form weighting because of May alone; it risks disrupting the more accurate LAD starter estimate. Do not shift recent/season run means to chase LAD@ATL’s three-run overprojection when the tension record marks MIL@SD as a risk and reports no helped game. Do not lower confidence solely because both hits received a high two-game calibration error: the observed buckets are labelled underconfident, and the sample is one observation per bucket. Do not assert a governor bypass or alter its setting to explain MIL; the documented problem is the missing probability transformation. Do not tune player projections to one-game hit/miss deviations unsupported by the player’s own contact quality.

6. Data and contract defects

Coverage reconciliation: The coverage matrix reports all expected games loaded and structurally audited: 2 expected, 2 canonical artifacts, 2 forensic audits, 2 continuous-learning games, 2 starter comparisons, and 2 completed structural audits. Both game audits pass. Complete coverage is not a clean bill of health: MIL has a critical lineage finding.

Findings by severity:

• Critical — unexplained probability publication delta (MIL@SD). Calibrated/governed probability is 0.6142; published probability is 0.56643; delta is −0.04777. No recorded transformation explains it. Block promotion until the transformation is recorded and reconciled. Do not infer that the governor was bypassed without tracing the pick-side math.
• Error — none reported. The structural summary has zero errors.
• Warning — none reported. The structural summary has zero warnings.
• Info — complete slate audit coverage. Both games received structural QA. Retain the receipts, while still acting on internal findings.
• Info — simulation produced no winner-direction intervention. Zero flip candidates and zero published flips on the slate. By itself this is not a defect. In combination with the 11-slate escalation and the supplied implementation diagnosis, it warrants the code/diagnostic action in Sections 7–8.
• Per-game audit info items: LAD@ATL has 1 info finding and MIL@SD has 1 info finding; their structural summaries report no finding details, so their content cannot be specified without inventing it.

Prediction-model defects versus presentation/contract issues:

• The near-zero holdout run R² and the variance-stage run-error regression are model/pipeline quality risks, not artifact-file failures.
• The MIL calibrated-to-published discrepancy is a probability contract/provenance defect. Clean saved forecasts and clean structural audit status do not settle its missing transformation.
• The LAD blend-side reversal is a recorded intermediate-to-published difference: blend home probability 0.568066, trained home probability 0.641512, published home probability 0.494846. The data calls one blend overwrite but does not establish an unrecorded material transformation for this final value; do not label it a bypass based only on the reversal.
• The score-stage transitions show later stages unchanged after enhanced prediction. A zero simulation flip count is not proof the simulation did no score work; the diagnosis separately reports no score-stage metric change at the simulation stage.

Complete pick-side probability lineage from supplied records:

• LAD@ATL: Lineage raw 0.5000 → calibrated 0.5071 → governor output 0.5071 → score-coherence 0.507133 → published 0.505154. Published-minus-calibrated is −0.001946; lineage says the publication matches the calibrated/governed value, with no unexplained material delta. The game trace separately gives raw 0.5289 and says recency guardrail applied with no numeric discount factor. That raw field does not reconcile to lineage raw 0.5000, but no material calibrated-to-published delta is recorded.
• MIL@SD: Lineage raw 0.6262 → calibrated 0.6142 → governor output 0.6142 → score-coherence 0.593317 → published 0.56643. Trace raw is 0.646289, governor input 0.646289, and starter-experience shrink is recorded from 0.593317 to 0.578153; the published probability remains 0.56643. The score-coherence, starter-shrink, and final publication steps do not have a complete recorded reconciliation. The lineage itself marks the −0.04777 calibrated-to-published delta unexplained. Call this a material unrecorded transformation in the publication path, not a proven governor bypass.

7. Cross-slate persistence

The cross-slate record covers 11 slates, with 10 prior slates loaded. Persistent escalations are established failures or patterns under the supplied guardrails; they should not be dismissed as noise from this one slate.

Every finding_streaks entry:

Escalated findings and required interpretation:

• simulation_inert_on_slate, 11 consecutive slates. Target lever listed: simulation.allow_score; target metrics: team-run MAE and total-run MAE. The escalation explicitly says to confirm the simulation is running and not silently no-oping. The detailed diagnosis says the score-realization loop and winner-probability distribution share draws, and the loop can early-exit after finding a target-realizing play-by-play, leaving a draw set too small to provide a meaningful win-rate. The named response is a code/diagnostic fix, not an arbitrary parameter move.
• single_slate_calibration_instability, 4 consecutive slates, present now. Target levers: confidence.empirical_max_weight, confidence.base_cap, confidence.moderate_cap; target metrics: Brier and calibration error. Its registered direction is increased empirical shrinkage. This persistence supports a bounded shadow experiment.
• weak_run_model_signal, 4 consecutive slates, present now. Target levers listed are XGBoost estimator count, depth, and learning rate, but the escalation says this is not parameter-actionable: investigate features/target using an isolated training backtest. Holdout total/home/away run R² are all near zero. The evidence calls for a feature/target code and training-contract investigation rather than nightly parameter tuning.

Raw structural blocks:

• Margin distribution: Actual absolute margins were 2 for LAD@ATL and 1 for MIL@SD; predicted margins were 1 and 1. No actual margin was at least 4, and both predicted margins were at most 2. LAD@ATL signed margin error is −1; MIL@SD is 0. This slate does not itself show a large-margin miss.
• Pipeline transitions: Historical ML → variance applied increased team-run MAE by 0.3317 and margin MAE by 0.0021 versus historical ML. Variance applied → enhanced prediction improved margin MAE by 1.0, team-run MAE by 0.5, and winner accuracy by 0.5, with LAD changing ATL → LAD. Later stages were unchanged. The intermediate regression remains relevant despite recovery.
• Calibration monitoring: Two settled games, two one-game buckets (published average confidence 0.5052 and 0.5664), both hits, weighted absolute calibration error 0.4642. The bucket directions are labelled underconfident under the stated confidence-minus-hit-rate definition. This is noisy at slate level, but the four-slate escalation establishes that a persistent calibration issue merits a controlled test.
• High-raw cluster: Zero games at the 0.65 threshold; zero hits and no rows. There is no current high-raw cluster in this block.
• Simulation control: Diagnostic-only status without independent support; 2 observed games, 0 flip candidates, 0 published flips. Considered alone, this is not evidence of failure; the 11-slate escalation and implementation diagnosis make it actionable as a code/diagnostic issue.

Cross-slate bias and trends:

• cross_slate_bias does not mark either supplied bias as persistent. Starter ERA error is negative on 5 of 10 slates, mean −0.225, z −0.57. Lineup run delta is negative on 6 of 10 slates, mean −0.447, z −1.39. Both are held as not separable from slate-to-slate noise; do not turn them into global mean shifts on this evidence alone.
• Metric trends: margin bias improving (mean −1.7579); mean team-run error on losses improving (mean 3.6934); weighted calibration error regressing (mean 0.3771); winner accuracy improving (mean 0.7146). The directions coexist: improving accuracy does not cancel regressing calibration.
• The top_confidence_pick loss streak is 0. The current 20261006 top pick is a hit; the prior listed 20261005 top pick is a miss. Other recorded results include a miss on 20260926 and hits on 20260927, 20260929, 20260930, 20261001, 20261003, and 20261004; two dates have unknown results. A latest hit means no current loss streak, not that top-pick performance is proven reliable.

8. Adjustments for today

Ranked by persistence and severity first, then scope, expected metrics, affected games, and regression risk. These are recommendations for controlled work; no configuration or code is changed here.

1. Persistent probability calibration pattern — bounded shadow experiment.

Exact parameter: confidence.empirical_max_weight. Direction and magnitude: increase by 0.02 absolute from the current registered value, within its valid range, in a shadow-only comparison; do not promote from this slate alone. Expected metric/direction: reduce rolling Brier score and calibration error if the escalation’s shrinkage diagnosis is causal. Games / tension: apply comparison to LAD@ATL and MIL@SD; neither game is explicitly marked as helped or hurt by this calibration lever in lever_tension. Both were hits, so the immediate regression risk is attenuating otherwise correct pick confidence; evaluate on the rolling window and retain the baseline. The shadow gate and rollback monitor, not this analysis, should determine whether the effect is causal.

1. Persistent simulation inactivity — code/diagnostic action, not a forced parameter move.

Registered target: simulation.allow_score is listed, but the escalation and self-assessment say this is not parameter-actionable and explicitly call for confirming the module is running rather than forcing a parameter move. Action: instrument and repair the simulation distribution path so the win-probability distribution comes from an independent, unsteered draw batch or a supported closed-form distribution, does not early-exit after finding a score realization, and reports its contribution to score and winner outputs. Register any batch-size control if introduced. Expected metrics/direction: make simulation contribution measurable and assess team-run MAE and total-run MAE; no improvement is assumed before measurement. Games / tension: both slate games had zero simulation winner flips and no measured simulation-stage score change. The variance lever tension has no helped or hurt games, so there is no game-level evidence to claim a beneficial simulation adjustment. This is an 11-slate established failure pattern, not single-slate noise.

1. Persistent weak run-model signal — isolated feature/target backtest, not a nightly parameter tweak.

Target levers listed: training.xgb.n_estimators, training.xgb.max_depth, and training.xgb.learning_rate; the escalation marks this finding non-actionable by parameter and calls for an isolated training investigation. Action: do not change those parameters as a stand-in for missing predictive signal. Test the shared feature contract and target in an isolated same-fingerprint backtest, with the specified candidate data such as properly source-labelled no-vig market probability, park/weather environment, bullpen rest/fatigue, and platoon-adjusted lineup quality; bump the model schema version if semantics change. Expected metric/direction: seek better holdout home/away/total run R² and team-run/total-run MAE; require measured improvement before use. Games / tension: the affected slate games are LAD@ATL and MIL@SD, both with total overprojection; the run-mean tension has no recorded helpful game and marks MIL@SD as a risk. Do not tune a feature from a single player or game.

1. Strongest single-slate contract driver — repair MIL probability publication lineage before promotion.

Parameter: none is registered for the unexplained probability delta; forcing a confidence or governor adjustment would conceal rather than resolve the contract defect. Action: reconcile and record every pick-side transformation between calibrated/governed, score-coherence, starter-experience/other controls, and published probability, including the trace-versus-lineage raw values; add a reconciliation check that blocks publication or promotion when a material delta is unexplained. Expected metric/direction: eliminate unexplained material lineage deltas and restore auditable published probability, rather than claiming an immediate accuracy gain. Game / tension: MIL@SD is the affected game. No listed lever-tension entry supports changing a model weight for this defect. This is the safest immediate intervention because it addresses a critical evidence/contract failure.

9. Bottom line

Known: both published winners were correct, both predicted scores were too high, all starter identities matched, and the structural audit coverage is complete. The run models have near-zero holdout signal, variance application worsened run MAE relative to the historical stage before later stages recovered, and a material MIL@SD probability publication delta is not documented. Simulation inactivity and weak run-model signal are persistent escalations; calibration instability has persisted for four slates and merits a bounded shadow test.

Uncertain: two games cannot establish calibration direction or a stable run-environment bias; the listed per-game player deviations do not isolate a generalizable lineup or starter adjustment; and the supplied probability records do not fully reconcile several raw and intermediate values. Clean artifact checks do not resolve those uncertainties.

Single safest next action for the very next slate: block promotion until the MIL-style published-probability lineage has a complete, auditable transformation record and a check that rejects unexplained material deltas.