Eval Leakage Audit

Eval Leakage Audit — Verification Circularity Audit

Purpose

When some verification (eval/metric/experiment/holdout) gives you confidence that something "worked," this skill checks whether that confidence actually comes from independent external evidence, or whether the people who designed the verification and the model that scores it are just confirming each other (circularity) — via 28 concrete patterns. A passing gate is not proof of quality — it only proves what it was designed to check, and this skill is the executable tool that actually tests that principle in practice.

Dominant variable: does this verification actually receive independent external ground truth, or are the designer, the model, and the scorer mistaking self-confirmation for a result?

Discard if: the target has no evaluation/verification/benchmark concept at all (pure code refactor, doc changes, etc.).

Trigger

• "audit this eval for leakage", "check if this benchmark is circular", "is this evaluation biased?"
• "이 검증 순환논리 아닌지 봐줘", "이 평가 편파적이야?", "이 벤치마크 셀프체크야?"
• /eval-leakage-audit

Workflow

1. Identify the target verification (eval/metric/experiment/holdout/"how will we know it worked"). Name its components — what plays the model role, what plays the scorer role, what plays the designer role, and which dataset is involved.
2. Ask the core question: does independent external ground truth actually enter the loop?
3. Apply all 28 patterns below to the target and report only the ones that actually fire (don't list patterns that didn't fire):
   1. Recall, not reason — the answer was replayed from something already known, not actually derived
   2. Wrong null hypothesis — the ablation only strips the surface label while the actual leaking signal stays in place
   3. Shared hallucination — two components confirm each other and dress up the circularity as a number
   4. Tautology — the scorer grades the bucket it drew itself (precise term: checker_overfit)
   5. Verifier = designer — an unreproducible, undisclosed recipe is passed off as a holdout
   6. Shared-pool bias — train/holdout come from the same labeler pool, so the same bias enters both sides
   7. Frame injection — the question itself hints at the answer
   8. Demand characteristics — the subject being measured knows it's being measured and behaves differently as a result
   9. Dual-fail-flag — when two independent subjects (models/implementations) fail on exactly the same hidden case, suspect a defect in the scorer itself before blaming the subjects. Independent failures coinciding by chance is unlikely — a match more likely points to a shared cause (a scorer bug, or an error in the hidden case itself)
   10. Asymmetric-baseline self-falsification — if the metric itself uses a biased, asymmetric baseline statistic, the null expectation isn't 50%, producing false positives. Before reporting a result, self-falsify the metric with a symmetric check
   11. Evidence-burn — a fixture a model arm has already observed is spent: don't reuse it afterward as independent evidence, a holdout, or a replication fixture. Generate a new variant for the next round, or retire the fixture
   12. Ungraded grader — trusting the scorer/answer-key/rubric itself without self-verifying it first. Before trusting it, run 4 gates: (1) reference-pass — a known-correct implementation scores full marks; (2) buggy-baseline-fail — a deliberately flawed implementation scores in the expected low-to-mid band (too low or too high signals a miscalibrated grader); (3) mutation-kill — the grader actually catches ≥3 plausible wrong answers; (4) dual-fail-flag — if both arms of a comparison fail on the exact same case, treat it as a grader/fixture defect signal, not a candidate failure
   13. Ceiling task — misreading a benchmark saturated at full marks for every candidate (zero discriminative power) as "no difference." A single k=1 pilot showing both arms scoring ≥95% is too thin a sample to confirm a ceiling — flag it only as ceiling_suspected and require 1-2 decisive branching probes (k≥2, or reproduction under a different condition/task variant) before promoting it to confirmed ceiling_detected. Adding more fixtures of the same kind won't by itself recover discriminative power once a ceiling is actually confirmed. Respond by switching task families, promoting process-layer metrics (cost, verification cadence), or adding those branching probes. Post-hoc discriminative-power indicators: ceiling_rate, score_sd, bucket_entropy, winner_flip_rate
   14. Respawn masking — in systems with respawn/reset logic (games, simulations, state machines), scoring by an instant state snapshot lets a respawn disguise failure as a pass (for example: a character dies, auto-respawns, and the snapshot moment shows only alive — the death vanishes). Score by session-wide deterministic invariants instead (for example: death/reset event count = 0, no cumulative resource loss) rather than a state snapshot.
   15. Pseudo-replication — counting multiple probe cells drawn from the same arm as independent sample size n artificially inflates the sample and overstates statistical significance. Distinguish effective independent units (true independent observations) from raw probe cells (repeated measures within the same arm) and do not count the latter toward n.
   16. Stimulus calibration gap — the counterpart to pattern #12 (ungraded grader): even a perfect grader produces meaningless results if the test stimulus itself (question, scenario, prompt) never actually elicits the intended behavior. Run a calibration pass beforehand confirming the reference implementation actually triggers the target behavior for that stimulus.
   17. Unaudited cost-saving skips — leaving cost/time-saving skipped checks unaudited indefinitely lets not-checked quietly harden into no-problem. Even without full re-verification, periodically audit the skipped set via a deterministic minority sample (for example: sha256-minimum hashing).
   18. Goodhart co-evolution in self-improving loops — in a self-improving harness, if the loop designs the very scorer that grades its own improvements, the gate can drift lenient across iterations with no single discrete failure to point to — the loop is quietly reshaping the measure around its own output rather than the measure holding still. Guard with two layers together: fixed anchor tasks the loop never designed and never sees in advance (user-picked, undisclosed), plus a judge the loop doesn't control. Periodically re-check the self-improvement gate for lenient drift instead of trusting a one-time calibration. Ship a deliberately-broken fixture alongside every new capability so the gate's ability to actually fail something stays exercised, not assumed. Credit a harness improvement only against a fresh held-out task, never against the task that produced the improvement in the first place.
   19. Success provenance gap — when an agent lands on the "correct" answer, not distinguishing whether it followed the intended reasoning from the context it was given (authorized context) versus simply picked up the target value in passing during evaluation or retrieval (acquired target) lets one accuracy number hide two different sources of "success." Re-run the same items under three conditions — CLEAN (no target value exposed), GOLD (the correct target value exposed), SHAM (a decoy wrong value exposed) — and measure the GOLD–SHAM gap: a large gap signals the accuracy is coming from value dependence rather than reasoning. [borrowed from arXiv 2607.24054]
   20. Lenient-judge-mode non-disclosure — a self-LLM judge defaults to a lenient grading prompt (partial credit, near-match acceptance, etc.) and the headline number gets reported without ever disclosing that lenient mode was on. Without a strict-mode re-score for comparison, there's no way to tell whether the headline reflects real performance or just grading generosity. Before citing a headline number, confirm whether the grading mode (strict/lenient) is even stated. [borrowed from OpenViking benchmark analysis]
   21. Hardest-category denominator exclusion — a headline accuracy is presented as "M correct out of N total" while the hardest or most adversarial category has quietly been dropped from the denominator (N) before the division. If the exclusion lives only in a footnote or appendix — or isn't disclosed at all — readers can't tell whether the headline means "performance on the easy subset" or "performance overall." Demand per-category numerator/denominator breakdowns, and where a category was excluded, also check that category's own standalone accuracy. [borrowed from OpenViking benchmark analysis]
   22. Underpowered null reported as no effect — before interpreting "no effect," "marginal improvement," or any small effect, compute the minimum detectable effect (MDE) from the sample size n and the observed variance. If the MDE is more than 2x the observed effect, label the result INCONCLUSIVE(underpowered) and state in one line the n needed to detect that effect — do not report it as "no effect." For event-level metrics (hit/miss transitions), compute from the number of events. When citing an external benchmark figure, record its "M tasks x t repeats" allocation; if the repeat count is not disclosed, mark it unverified (repeats undisclosed). [borrowed from arXiv 2609.01519, 2608.20290, 2609.29140 (converging)]
   23. Degenerate strategy passes — before trusting a threshold or metric, run constant strategies (always reject, always pass, empty output) through the same scorer. If any of them clears the pass line, the metric rules nothing out and must be redesigned. A "zero violations + zero adoptions" signal is a post-hoc symptom; this is the pre-adoption check. [borrowed from arXiv 2608.27167]
   24. Retry-inflated headline — check whether the headline success rate includes retries, best-of-k, or an automatic recovery loop. If it does, ask for the first-attempt pass rate (pass@1) separately; if none is given, label the figure an "upper bound." Same disclosure family as #20 and #21. [borrowed from arXiv 2609.00050]
   25. Non-common item sets across compared runs — if ground-truth filtering or preprocessing leaves a different set of items for each compared subject (model, setting, version), recompute on the intersection of common items. If that is impossible, label the comparison "not comparable across runs." [borrowed from arXiv 2608.28623]
   26. Bundled-change attribution — before crediting an improvement to one factor, list everything that changed in the same round (instructions, schema, examples, scripts). If no comparison changed only one of them, report the effect as the effect of the whole bundle. [borrowed from arXiv 2609.01519]
   27. Stability-only validity — if the only evidence for a judge's or gate's quality is agreement rate or test-retest consistency, check whether responsiveness was also measured: does the verdict actually flip on a minimal pair of inputs that differ by a meaning-changing edit? If not measured, the judge cannot be told apart from a constant judge. [borrowed from arXiv 2608.24419]
   28. Selective-gate attribution — when claiming the value of a conditionally applied gate (selective revision, retry, escalation), check that it was compared against an "always apply" baseline as well as against "no gate (initial)". Reporting the gain over the initial state alone credits the revision procedure's own gain to the gate. Also ask for the 4-cell transition table (C->C, C->W, W->C, W->W) so correct answers destroyed (C->W) are not hidden inside a net gain. [borrowed from arXiv 2609.35832]
4. For every pattern that fires, propose a concrete fix aimed at restoring independence.
5. Self-check this audit itself against patterns 3–5: is this auditor grading a bucket it drew itself? Is the verifier actually the designer?