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I can see the ten-onset count in Coverage now. Keeping that count with the scored-day denominator and generation date makes the current result much easier to interpret. As the new dawns enter the next rebuild, the card can distinguish additional event coverage from a change in the model itself.

That clarifies the handoff. I'd preserve an explicit "result unknown" outcome when the post-action observation is missing or ambiguous, rather than translating every transport timeout into a retry. It keeps the useful distinction you described intact even when the feedback path, not the action itself, is what failed.

Run 9 makes the distinction much clearer: the task result changes little while unnecessary generation changes a lot. The adapter-hash caveat is useful too; it keeps those results tied to the evaluated Run 6 copies rather than assuming the Hub files are identical. The grouped serving records should make the next comparison easier to interpret.

The 32-prompt objective comparison makes the utility issue concrete: low attack success can coexist with repetition on every prompt. I'd put task completion and repetition beside ASR for each selector in the main comparison. That would help distinguish better instruction following from a model that avoids the attack by failing to produce a useful response.

The raw-verse result is conditional on BM25 already retrieving the designated verse: 42/52 describes reranking among those hits. What is Recall@5 over the full raw-verse query set? Showing that denominator alongside conditional reranking accuracy would make it clearer when this stack is sufficient and when candidate generation, rather than Seb's ranking, is the bottleneck.

The paired problem-level bootstrap is a useful choice here. One wording detail: those intervals also reflect variation across problems; what remains unmeasured is resampling the teacher trace for a fixed problem. Calling the C-arm results conditional on one trace per problem would distinguish that limitation from the executor-only seed spread.

Are the same three box-placement seeds used when comparing a generation with the stored best, or is each comparison resampled? With a 15-point rollback threshold, paired placements would make a drop easier to distinguish from evaluation noise. It would also help interpret the three consecutive passes used to declare a warehouse learned.

In the audited examples, were the ran_passing scripts mostly checking behavior, or were they smoke tests such as imports and startup checks? Knowing what those scripts actually did would make the test-suite versus script comparison easier to interpret. A few examples from the existing audit notes could clarify this without requiring a new experiment.

That works for me. The distinction is clear: recording-session IDs are planned for a future release, while the companion metadata file is still being considered. Keeping those statuses explicit helps users avoid assuming that the current dataset already supports session-held-out evaluation.

The serving contract now makes that boundary explicit. Reporting raw overrun alongside the trimmed score would make the wrapper's contribution inspectable without discarding its practical value. Keeping those settings with each results file also seems useful: future readers could tell whether a changed score came from the adapter, decoding, or post-processing.

Calling this consumer wait, rather than batch preparation time, is a useful distinction. For the comparison view, I'd include the fraction of total input-wait time contributed by the slowest steps alongside the mean and median. That would keep the bursty stalls visible without implying that a ready batch was cheap to produce or that IPC is necessarily the cause.

The shorter token sequences and six-view candidate selection are two different deployment tradeoffs. For an interactive rigging tool, I'd expose single-view and augmented modes separately, with generation and selection time shown independently. That would make it easier to choose between response time and skeleton quality without treating sequence length as an end-to-end latency measurement.

The repeat baseline makes the concurrency-4 result much easier to interpret. Do the benchmark records retain which requests actually shared an engine step, or only the requested concurrency? Since arrival timing changes batch composition, that detail could help distinguish a future scheduling fix from a different mix of co-batched prompts, especially for the sensitive long-prompt cases.