AuditRepairBench: A Paired-Execution Trace Corpus for Evaluator-Channel Ranking Instability in Agent Repair

When can an agent failure be caught? A weak audit score alone cannot identify whether the record or the method is limiting. CatchBench therefore puts one auditor's question to three information states: the declared configuration before a run (PRE), a growing prefix of its trace (LIVE), and the finished trace (POST). Prior benchmarks fix one of these states or vary the telemetry; to our knowledge none scores all three under one task-method interface. Each state admits different questions, so seven task contracts carry their own labels and metrics rather than one leaderboard. Four are evidential; three are Gold-derived mechanism diagnostics. The release scores 72 entrants, from rule scanners and structural models to eleven LLM judges across nine model families (GPT, Claude, Gemini, Gemma, Llama, Qwen, DeepSeek, Mistral, Nova), over 1187 declared configurations and 1162 recorded runs. Every recorded comparison is published as a measured difference with its interval, uncorrected, and no board declares a winner it cannot show. The three sharpest results cut against our own data. One rule reads declaration order alone and reaches a perfect F1 on one of six configuration sources, so a score there measures how the corpus was built. Our admissibility bar then rejected one injected substrate and withheld evidential status from the other. A published structural gain also turns on which size reference it is measured against. A benchmark number is therefore not interpretable until the process behind its labels is published and tested for the shortcut it may leave. We report all three, and regenerate every ordering from released predictions with no model call.

Agentic computer-use RL is reported in single runs, and those numbers mislead. Using verifier-guided repair of a 35B computer-use agent (CUA) across five oracle-graded environments, we show a repaired policy's success rate is dominated by upstream variance: a variance-components decomposition across three cells (crossed data-draw $\times$ seed grid, bootstrap CIs) finds evaluation variance negligible ($σ_{\mathrm{eval}} \approx 0$) and the training-seed effect small everywhere ($\leq 10\%$); instead it splits between the data draw and run-to-run nondeterminism, the data draw's share rising to dominant ($48\%$) on the hardest cell. There the run-to-run distribution is bimodal (Hartigan dip $p=0.07$, $k=10$), so a single run has roughly a 30% chance of the failure mode and mean$\pm$std is the wrong summary. On that footing, two findings hold. First, repairability is two-tier in how constrained the corrective action is: a single fixed token installs reliably (done-detection $0.97\pm0.06$), while open-ended corrections are only partial -- spatial-coordinate clicks (grounding $0.53\pm0.35$) and a generative field-fill ($0.14\pm0.04$). Second, the frame-level repair transfers to task success only when the corrective action is the task's sole remaining blocker (LinkedIn 8/20 vs. base 0/15, Fisher $p=0.006$). We caught two of our own over-claims -- a sample-efficiency curve and a 'grounding cannot be bought' boundary -- only by replicating across seeds; a stress test makes the stakes external: a single-run improvement of the size this field publishes would have the wrong sign roughly one-third of the time in a comparable regime. We release a library (cua_reliability) for routine k-seed reporting. The apparatus is, to our knowledge, the first multimodal segment-aggregated on-policy self-distillation (SA-OPSD) update on a real 35B CUA policy.

When a repair agent runs a test and sees it pass, the result is treated as evidence about the reported defect. We measure how often that treatment is warranted. BSG-VA (buggy-state/candidate-state/gold-fix validation analysis) captures each validation command at its exact working-tree state, extracts a test-only patch, and replays the command on the original buggy code (B), the candidate state (S), and the developer gold fix (G). The captured outcome and the replay results assign every event an evidence role, from gold-aligned bug-discriminating through regression-only to misleading. Across 3,730 events in 643 rollouts on 110 tasks, 46.0% of positive comparable events carry no bug-discriminating information; 23.8% of baseline rollouts, with no feedback injected, close with a patch whose entire positive evidence base is of this kind. A three-arm experiment tests whether returning the B-replay outcome to the agent changes this pattern. Bug-contrast feedback reduces evidence-inadequate closure by 7.8 percentage points relative to an attention-matched reminder (p = 0.0029) and raises bug-discriminating evidence by 7.4 points (p = 0.011), with no detectable cost to repair success. Both estimates fall below the prespecified 10-percentage-point smallest effect size of interest, so practical magnitude remains uncertain. Roughly a third of the improvement traces to the reminder alone; across two exploratory replications, varying the scaffold and the model, the B-replay content adds a detectable increment only with gpt-5.6-sol under the unconstrained tool-use loop. BSG-VA applies post hoc to any replayable repair trajectory that preserves the required code states and execution environment. Keywords: program repair agents, validation evidence, test adequacy, large language models, software quality, controlled experiment.