LEARNINGTO BUILD

All six classical builders receive the same 24 recipes, target channels, calibration references and permitted environment. They can all search the complete bank. The proposed update changes candidate order using donor experience; it does not discover new segmentation operators.

The six policies used four distinct orders. A separately frozen cached-score replay tested 33 order/settings interventions (30 unique orders): all exhausted the same 24 failing candidates and selected r12. This explains convergence through the shared recipe bank and fallback rule; it is not agreement among independently prompted models or fresh image inference.

The primary contrast is a supplied greedy-coverage order versus conventional empirical ranking from the same donor table. A local advantage requires an accepted successor and fewer candidate executions without losing acceptance. Full enumeration is a complete conventional control. The CellposeDINO specialist brings additional pretrained stock and is assessed separately.

Each arm is executed separately; target scores are not shared.

The first instrument must meet instance F1, foreground Dice and count-error gates on both the official 50-field validation and 50-field test sets. The successor must also recover internal boundaries, with F1 of at least 0.60 both across all fields and across fields containing true internal boundaries, on calibration and test separately.

High foreground overlap or an adequate count cannot replace the missing boundaries between cells. Area values are segmentation-derived pixel estimates; these gates do not establish biological area accuracy or physical units.

Applying the unchanged nucleus artifact to the successor gives boundary F1 0.072995. Supplying manual nuclei and foreground to the selected cell recipe gives boundary F1 0.671256, Dice 0.999933 and count error 0.159935 on the twelve test fields.

The latter uses privileged reference-derived inputs and is not a qualified raw-channel instrument. A follow-up fixed-r12 diagnostic separated the branches on only the four already exposed calibration fields. Raw inputs gave boundary F1 0.250398; reference nuclei alone gave 0.195353; reference foreground alone gave 0.615828; both reference inputs gave 0.714909. Separate scoring implementations agreed on every component mask. The seed branch also contributes to foreground, so these are software-branch interventions, not isolated biological causal effects.

Foreground recovery was the better next lead. One separately frozen ordinary composition used the specialist’s actual retained mask union as foreground for the original watershed. It reached boundary F1 0.296809, below the required 0.60 and below the unchanged specialist’s calibration score. The stop rule halted it with zero test fields scored, no tuning and no new neural inference. The failure is retained; an unexecuted complete raw-input command is not claimed as a demonstrated capability.

Inspect the frozen diagnostics · Inspect the failed practical composition. All cases remain exposed, and reference-assisted passes do not establish a deployable raw-input solution.

The original BBBC007 boundary benchmark permits manual inputs and reports a different proximity measure. Its historical percentage is not directly comparable to this raw-input symmetric F1.

The completed classical phases record 696.935 CPU seconds and 696.703 wall seconds, including donor construction and the labelled diagnostics. The completed 116-field specialist session records 4,969.507 CPU seconds and 4,970.035 wall seconds. These stage or session measurements exclude dependency setup, acquisition, independent verification, authoring, upstream pretraining, unavailable historical costs and economic costs. The classical ledger records no interrupted attempt, but the origin of 138 residual files remains unknown. Byte identity cannot distinguish copying from additional execution; any associated unrecorded work and cost remain unknown.

The reported local reproduction uses a dedicated Python 3.12.14 virtual environment with registered package versions and source hashes checked. It enables --system-site-packages, so it is not fully isolated and does not freeze every transitive binary or host component. The default isolated installer was checked separately; it did not replace the environment that produced these results. Setup receipts preserve the actual configurations.

The published history records a Boolean-outline decoding failure and a scalar/RGB observation mismatch. Narrow, versioned amendments repaired the interfaces before target test prediction or scoring. The shared RGB-to-L convention is generally lossy; it does not recover physical fluorescence.

The source and compact preregistration records were preserved. The original final raw-output package was not available for byte verification, so this edition uses new execution outputs. Historical costs that cannot be recovered remain unknown. The reproduction does not convert the exposed comparison into fresh hidden evidence.

The raw classical tree contained 416 files and failed the strict file-set check because 138 residual attempt-file copies remained alongside 278 canonical files. Every residual matched its canonical counterpart byte for byte; the cause is unknown.

The publication projection retains the 278 canonical files unchanged. All residual files and the reconstruction mapping are also retained, with no changes to reported metrics or costs. The manuscript appendix and construction guide explain the rejected raw tree and the separate checked projection.

Four programs generated from supplied arithmetic specifications pass 4,000 finite input checks. Across 288 authored resource conditions, the conventional equal-content planner ties every corresponding constructor-state decision. Retention can expand or contract attainable delivery once maintenance is charged.

Those are exact results in an authored finite model, not empirical success probabilities or evidence of learned-constructor superiority. Read the unchanged first edition →