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What the papers say

What the papers say that this project got wrong, or has not tried

Read on 2026-09-18 from the PDFs in papers/ (repository file). Not summaries: the specific places where this project does something different from the published method, and whether that difference was a decision or an oversight. Four of them are oversights.

1. The flood tracer moves the wrong way (Flood-Filling Networks, 2016)

roi/flood.py was written from the idea of an FFN — accept, move to the frontier, seed with what you accepted, repeat — without reading how FFN actually chooses the move. Four differences, and three of them are mistakes:

FFN (2016, §3.2) roi/flood.py as written verdict
where to move the single highest-valued mask voxel on each of the 6 planes at ±Δ, taken only if it reaches t_move = 0.9 the mean position of frontier voxels on each face, taken whenever any voxel is within 3 of the face wrong: chases a weak rim and dilutes a confident direction
order of moves a queue sorted by descending mask activation FIFO wrong: this is exactly why our walk fills a neighbourhood instead of following an axon
revisiting a voxel split bias: once a voxel is below 0.5 it can never be raised again, "to explicitly bias the network against merge errors" we keep the maximum over revisits wrong, and backwards: we bias toward merges, in a project where §97 says the benchmark cannot see a false merge
visited set positions rounded to (⌊x/Δx⌋, ⌊y/Δy⌋, ⌊z/Δz⌋) the same trick, at half-box cells matches

Also worth knowing: FFN's movement threshold (0.9) is much stricter than its acceptance threshold, and the final segmentation is thresholded at t_move too. We used 0.5 for both. And FFN's field of view is 33×33×17 with no pooling and depth chosen so the centre voxel sees the whole input; our ROI model is a pooled U-Net at (64, 96, 96). That last one is a design difference, not an error, but it means our "box" and their "field of view" are not the same object.

Done, and measured — including the part that says it made no difference. All three are fixed in roi/flood.py (move_thr, a priority queue, split_bias=True). On four starts in the middle of long fragments, with a budget of six boxes so that the order decides which six, the paper's rules traced exactly the same volumes and reached exactly the same distances as the old ones (median 10,365 µm³, 52 µm; individual reaches 76, 46, 42, 58 µm under both). On clean cable the frontier offers one or two viable faces, so ordering has nothing to decide and revisits are rare enough that the split bias never fires.

The paired runs also looked 2.3× faster under the new rules (7.2 s against 3.1 s median) and that number is not real: the two arms ran in sequence against the same imagery, so the second benefited from the first's chunk cache. A timing claim needs the arms interleaved or the cache cleared, which was not done.

So the rules are kept for the reason the paper gives, not for a measured gain: the split bias is the right default in a project where a false merge is the error the benchmark cannot see, and the confidence-ordered queue is what should decide a contested frontier — a branch point, a crowded bundle — which is exactly where this test had no cases. Finding such cases is the measurement still owed.

2. There is a published task for exactly what we cannot do (Zung, Tartavull, Lee & Seung, 2017)

Five statistics have failed to tell us whether a branch belongs (§327–§333). This paper defines the task properly and solves a version of it:

  • Error detection: input the raw image and a binary mask of a candidate object; output a map where a voxel is lit if a window centred on it contains a split or a merge error. They report high accuracy — and they also test a variant where the mask alone is the input, without the image.
  • Error correction / object mask pruning: input a mask assumed to be a superset of a true object; output the true object containing the central voxel.

Two things follow for us. First, every cue this project tried was computed at a point on a skeleton; theirs is computed over an object mask, which is a different and richer input — and our §332 conclusion ("the local cues were branch detectors") is a statement about skeleton features, not about mask features. Second, object mask pruning is precisely the operation we want for a merged fragment: hand it a fragment that spans two cells and the point we trust, get back the part that belongs. We have never trained such a model, and now that roi.flood produces masks we could.

3. Our clDice result was measured on a combination the paper never used (clDice, 2021)

§B5/§126 recorded that a topology-aware loss is "inert when small and harmful when large" and left it off by default. The paper's own recipe is

L = (1 − α)(1 − softDice) + α(1 − softclDice),   α ∈ [0, 0.5]

— clDice is combined with soft-Dice, and the baseline it beats is soft-Dice. Our roi/model.py combines cldice_weight with weighted BCE (pos_weight = 40), which is not what was validated: BCE with a large positive weight and Dice handle class imbalance in different ways, and the interaction of either with a centreline term is not transferable from one to the other. So the honest status of that negative result is narrower than it reads: it closes clDice-on-top-of-weighted-BCE, not clDice as published. The untried arm is soft-Dice plus soft-clDice at α ≤ 0.5.

4. The imaging paper is ours to read (ExA-SPIM, eLife 2025)

papers/exaspim_2025_elife.pdf is the microscope that produced this data — expansion plus a large-format light sheet, whole mouse brain without slicing. It is the reference for the expansion factor, the PSF and the voxel anisotropy that several measurements here assume rather than cite (§311's "our micrometres are expanded", the caliber work's PSF caveat in §244, and io/ccf.py's measured local scale ratio of 1.56 between this brain and the atlas). Reconciling those three numbers against what the paper states is an open item.

5. The join decision has a published recipe, and it is symmetric (FFN, Nature Methods 2018)

The 2018 preprint arrived on 2026-09-18 (papers/ffn_2018_preprint.pdf, CC-BY-NC-ND, obtained from bioRxiv after pacing a browser session past the 429s). It is not a restatement of the 2016 method paper: the parts that are new are exactly the parts this project has been reinventing.

Their join test is two seeds and an agreement, not one reach. To decide whether two segments are the same neurite they take the midpoint of the segments' closest approach, cut a 101 × 101 × 51 subvolume, remove both segments from it, and run inference twice — once seeded inside A, once inside B, each seed placed at the maximum of that segment's distance transform (retried up to 16 times if a run fails to recover 60 % of its own object). They merge only if every cross-recovery clears 0.6 (f_AA, f_AB, f_BA, f_BB), few voxels were "deleted" (driven from ≥ 0.8 down to ≤ 0.5 during inference), and the two predicted masks agree at Jaccard ≥ 0.8.

Ours is one-directional: seed at the reconstruction's end, follow the field, ask how near it came (§338). That throws away the half of the evidence their criterion leans on hardest — whether the candidate, seeded on its own side, comes back.

E435 tried it and the attempt is withdrawn (§349). Note the phrase above: their subvolume sits at the closest approach of two touching supervoxels, so it is tiny. E435 reused a fixed 40 µm box at the midpoint of pairs separated by up to 120 µm, and 49.7 % of them contained neither object — the test was never applied. Its apparent keeper, f_BB at 0.819, turned out to equal the pure boolean "is the candidate's cable inside the box" to four decimals, and to read exactly 0.500 where the box does contain it.

The idea is untested here, not refuted. Doing it properly means sizing the box to hold both objects — which join_levels_at_end already does for the ranking window — and scoring it against plain distance, which beats every cue measured on that panel (§346).

They treat the model's seed-sensitivity as a resource, not a defect. A merger that appears when segmentation runs A→B and not B→A is a "unidirectional merger"; running the volume forward and backward and keeping only the mergers present in both cut mergers by a factor of 82 for a doubling of splits. Adding runs at downsampled resolution (which enlarges the field of view in physical space) breaks more of them still. We have never ensembled over seed order or scale — our multi-scale channels put several scales inside one forward pass, which is a different thing from requiring several passes to agree.

They also do not train through rare damage. Imaging irregularities affect fewer than one voxel in a hundred — too rare to learn — so they are detected separately and the process is partitioned there, with the agglomeration stage reconnecting most of the resulting splits. And a separate classifier labels blood vessel, cell body, neuropil, myelin and out-of-bounds so the FFN cannot leave the neuropil. Our analogue of the second is the ignore mask; of the first we have nothing, and §333's "certification is safe or useful but not both" is the same problem from the other end.

One method note worth copying immediately. They select the training checkpoint by expected run length among the checkpoints with zero mergers — a task metric with a hard safety constraint, not a validation loss. This repository learned the same lesson the expensive way (§153: validation loss pointed the wrong way three times) and picks checkpoints by validation loss anyway. E429 has just had to fix a narrower version of this bug.

6. Telling a real branch point from a merge — and why our junction geometry scored 0.52 (reviewed 2026-09-18)

A literature review, prompted by §360–§365: the production merge detector on 789202 cuts about fifteen genuine forks per merge, and a skeleton-only veto of those cuts failed (§365). What the field knows, and what it does not:

  • No published classifier separates a real fork from a merge at a three-arm junction in sparse light-sheet data. EM work mostly sidesteps the three-arm case: Motta et al. (2019, Science) flagged four-way "chiasmata" (a sphere around the axon crossed more than three times) because such configurations "occur rarely in branching neurites", and left three-arm junctions to a clean-up pass. https://www.science.org/doi/10.1126/science.aay3134
  • Our signal describes a real axon collateral as well as a merge. Axon side branches leave at roughly right angles (Szebenyi et al. 1998, J Neurosci), so "two arms straight through, a third at a large angle" — what junction_score rewards — is also the shape of an ordinary collateral. That is the mechanism behind §360's 0.52.
  • Orientation toward the soma is the missing piece. G-Cut (Li et al. 2019, Nat Commun) scores a junction by the angle between a branch and the line to the soma, learned from >70,000 NeuroMorpho cells. PointTree (Cai et al. 2025, eLife, fMOST and light-sheet axons) scores how straight the path from the root continues through each junction; with the true root it was lowest for 195 of 208 branches. In a real fork the soma-side arm continues into a child; a foreign fibre fused at a junction runs past it. The soma is known at run time — reconstruction starts there — so this needs no tracing. https://elifesciences.org/articles/102840
  • Hand-written EM rules that carry over: NEURD (Celii et al. 2025, Nature) keeps the one downstream branch within ~45° (+25° buffer) of the incoming one, and flags branches that turn back toward the soma by more than 120–140° and sister axons that stay parallel. Its width and "webbing" rules need EM resolution and do not. https://www.nature.com/articles/s41586-025-08660-5
  • Real sister branches diverge; a wrongly joined neighbour stays parallel. Measuring sister-arm separation at 5, 10 and 20 µm from the junction is a cheap skeleton test (NEURD's parallel-sister rule, in light-microscopy form).
  • Two-direction agreement before cutting. RoboEM (Schmidt et al. 2024, Nat Methods) keeps a result only when tracing forward and backward agree; FFN agglomeration (Januszewski et al. 2018) joins only when both reconstructions agree. https://www.nature.com/articles/s41592-024-02226-5
  • Calibre is not usable here. Measured axon bifurcation exponents are ~2.6, not Rall's 1.5, with wide scatter partly from light-microscope measurement error (Chklovskii & Stepanyants 2003); at ~1 µm it is not resolvable, and our skeleton radii are constant anyway (§244).
  • Transfer is poor for learned models and tuned rules; shape-only detectors claim to transfer. NEURD needed separate settings for MICrONS and H01; RoboEM was retrained per dataset; BigNeuron found no single best tracer.
  • EM operates where merges are common; we are the opposite. On MICrONS 87 % of excitatory-axon synapses came from merged material before proofreading, so over-cutting is cheap there. The arithmetic for us: precision = TPR / (TPR + FPR × N), N forks per merge. Even a detector at 90.6 % recall and 2.7 % FPR (Li et al. 2020, MICCAI) gives precision 0.69 at 15:1 and 0.14 at 200:1. Evaluate with precision–recall at each brain's own ratio, not ROC (Saito & Rehmsmeier 2015). Thresholds borrowed from EM will over-cut here.

What this changes. The skeleton veto (§365) failed with orientation-free features. The two cheap features the literature points to — the soma-oriented continuation angle and sister-arm divergence — were not in it, and are the next thing worth testing before paying for image reads.

UPDATED 2026-11-11: both were tested as a veto of merge-detector cuts on 789202 (E459, RESULTS 366: the soma-oriented features, sister-arm gaps included, at PR-AUC 1.00× chance). The soma-orientation half was then read as a JOIN identity cue on 685221 (soma angle, root-straightness, turn-back, at end decisions and fragment pairs, held out by neuron) and adds nothing to gap × turn or the join CNN (RESULTS 1118, EXPLORATORY NULL; closed in docs/CLOSED.md). Sister-arm divergence has not been read as a join cue.

What has not changed

Nothing here overturns a measured result. §332's finding that the failed cues detect branching rather than merging stands; §329 and §331 stand. What the reading changes is the list of things not yet tried, and it makes that list shorter and more specific than it was.

7. Pedigo: multiscale surface features, review coverage and contextual decisions (reviewed 2026-11-08)

Recommendation: test HKS as an additional shape/context factor, and borrow explicit tracking of reviewed arbor. Neither is evidence of improved exaSPIM tracing yet. Benjamin D. Pedigo's postsynaptic census preprint computes heat-kernel signatures (HKS) on an existing triangular surface mesh. The original bioRxiv v2 PDF is pedigo2026.pdf, with version, source, licence and checksum in the paper manifest. The public text, source audit and checked quotations are under scratchpad/pedigo_review/. The corresponding proposed review is browsable at the knowledge-base page.

What HKS supplies, and its relationship to FFN

At a surface vertex, HKS describes how much heat remains there after diffusion at several timescales. The spectral form is H_t(x,x) = sum_i exp(-lambda_i*t) * phi_i(x)^2. Small and large times describe different spatial contexts. Pedigo and colleagues use these descriptors, with distance to the nucleus, to classify postsynaptic sites as spine, shaft or soma. This is a morphological classification task on reconstructed meshes. An FFN instead consumes image voxels and a recurrent object mask to grow an individual segmentation; see the FFN review above. Their useful connection is compositional: a segmenter could supply a surface, and HKS could supply evidence about its shape.

Our method relies only on having a mesh representation of a neuron and avoids processing image or segmentation data directly.

— Pedigo et al., Abstract, PDF p. 1; HTML Abstract.

The pipeline simplifies and splits meshes with overlap, uses a robust Laplacian and a banded eigensolver, then compresses similar neighboring feature vectors. The paper explicitly motivates saving features for later classifier iteration. That fits our wish to turn expensive analysis into reusable inputs. It is not a persistent cache supplied automatically by the reviewed meshmash functions: our integration would need versioned storage and invalidation.

Retaining these HKS features (rather than just the classifications alone) enables rapid classifier iteration

— Pedigo et al., §2.2, PDF p. 4; HTML §2.2.

Two limitations matter before a tracing experiment. Gaps or erroneous connections alter diffusion; a robust Laplacian does not certify biological topology. Absolute scale also changes HKS, and chunking limits the longest context represented. The paper's local spine task does not demonstrate long-range axon identity. Its mouse MICrONS and human H01 classification results cannot be compared with our auto@soma, wrong-join or human-time metrics. Light-microscopy surfaces may not resolve the structures that make the EM classifier useful.

complete discontinuity causes long-timescale HKS features to be distorted by an artificial boundary.

— Pedigo et al., §3.2, PDF p. 16; HTML §3.2.

the model has some sensitivity to scale (e.g., dendritic shaft diameter or spine size)

— Pedigo et al., §3.2, PDF p. 16; HTML §3.2.

Implementation audit: meshmash at ccbfd212, and the model at 9841544f. The artifact uses HKS plus nucleus distance, drops small components, and contains scale-dependent thresholds. The supplied RF configuration sets balanced class weights, while paper §4.5 describes default parameters except tree count/depth. Pin the artifact and configuration rather than assuming the prose reproduces every setting. No external model weights were downloaded or executed for this review.

Other work worth borrowing

Work and evidence Transfer to Exaproof Limitation
Zhang et al., canonical cortical microcircuit, Pedigo coauthor; Methods, “Manual proofreading strategies and status,” PDF p. 22 Guidebook / Tourguide: mark branch points and terminal tips, record which arbor regions were reviewed, retain extension opportunities Human proofreading workflow in EM; it does not establish an automated error detector or completion under an hour
Pedigo and Danskin, local compartment classifier, model card, “Training Procedure” and “Intended uses & limitations” Combine local features with neighborhood context; make compartment uncertainty an input to factor selection A model artifact, not a paper; trained on a small set of EM boxes with synapse features unavailable here; generalization explicitly uncertain
Pedigo et al., bisected graph matching, Results and Discussion, PDF pp. 9–10 Evaluate joint consistency across competing assignments; repeated solutions can expose unstable cases for review Matches bilateral whole-neuron connectomes in worms and larval fly, not local neurite joins; helpful context requires real correlation, and stability is not calibrated correctness
Gopalakrishnan et al., multiscale comparative connectomics, Pedigo coauthor; Introduction, PDF pp. 1–2 Audit errors at local, regional and population scales with explicit denominators and multiple-comparison control Compares networks across subjects; “multiscale” here does not mean adaptive zoom in an image tracer

on-demand highlighting of branch points and terminal tips within user-defined regions based on rapid skeletonization

— Zhang et al., Methods, “Manual proofreading strategies and status,” PDF p. 22.

it is unclear to what extent this model will generalize.

— local compartment model card, “Intended uses & limitations.”

For a new organism (or possibly even just a new sample), this will not be known in practice.

— Pedigo et al., Discussion, “Limitations,” PDF p. 10; refers to sufficient contralateral correlation.

Concrete next reads and reusable factors

These are proposed, not adopted tools or registered improvement attempts. Before any experimental output, freeze the population, reading rule, seeds and run budget through the usual experiment workflow.

  1. Measure surface availability first. On a fixed sample of actual join/conflict cases, count which have usable image-derived masks/meshes at the relevant physical scale. Record units, expansion/voxel calibration, mesh source, gaps, dropped components and processing parameters. A cylinder manufactured around a skeleton supplies no independent image evidence. If reliable surfaces are unavailable, the published classifier is not immediately usable.
  2. Test numerical behavior before biological accuracy. On small meshes, check rigid-transform invariance, physical rescaling, broken/false bridges, simplification and chunk-boundary sensitivity. Preserve raw features and timings. A proposed initial ceiling is one CPU worker, 4 GB, 256 tasks and ten minutes; actual cost is unmeasured. A synthetic mesh check can validate the interface, not claim tracing performance.
  3. Test incremental decision value. Use identical candidate sets and full competitor populations; compare the current geometry rule, simple mesh size/calibre features, and HKS added to those features. Separate end identity from side-exit identity, hold out whole brains and use each changed arm's own seeds. Evaluate calibration, recall at held wrong-join risk, retained foreign cable and cost; include shuffled/uninformative-feature controls. This tests a surface signal absent from the older skeleton-only rules without reopening all closed geometry claims.
  4. Measure human completion. Track reviewed regions, unresolved tips, edits, review reasons and active minutes. Compare uncertainty/impact routing with an equal-budget control, then independently assess completed neurons and censor unfinished ones. Include audits of accepted and deferred decisions. Region highlighting alone is not evidence that a neuron can be proofread in under an hour.

Candidate reusable factors are surface_integrity, shape_across_scales, compartment_context, assignment_stability, and reviewed_arbor_coverage. Each needs an applicability rule, extractor/configuration version, units, missing-data state, supporting/contradicting observations and later outcome. Shape and compartment features computed from the same mesh belong to the same evidence group: do not multiply them as independent likelihoods. An adversarial review can challenge mesh integrity, scale, rival hypotheses and missing context, then produce concise evidence-backed factor revisions. Debate agreement itself supplies no calibrated probability. An eventual RL policy could choose which view or factor to acquire next; none of these papers demonstrates that such a policy improves this tracer. A cheaper fixed or contextual policy remains a required comparison.