Uysal 2026 — Patient-Level Gleason Grading from Individual Sections

Asks the question most Gleason-grading papers skip — how do you get from a model that reads one section to the single grade group that goes in the report — and answers it with slide packing rather than voting, on a 106-patient consecutive cohort whose reference standard is the routine report and whose institution is the same one that supplied half the training data.

Asks the question most Gleason-grading papers skip — how do you get from a model that reads one section to the single grade group that goes in the report — and answers it with slide packing rather than voting, on a 106-patient consecutive cohort whose reference standard is the routine report and whose institution is the same one that supplied half the training data.

Read status: full main text from the publisher PDF, but this is an Article in Press. Nature is providing an unedited manuscript for early access; the content may change before final publication. Supplementary Tables S1–S5 and Figures S1–S14 were not available and carry a real share of the paper’s numbers — cohort counts (S1), the mixing-voting result (S2), the section-count distribution (S3), the core-count subgroup statistics (S4), the MRI-targeted subgroup (S4/Fig. S4), and every TPR/FPR figure (S7, S8, S12). Claims resting on them are marked [supplementary, unread].

The problem it picks, which is the reason to read it

A pathologist does not report a section. They report a patient-level ISUP grade group, arrived at from multiple cores, each represented by several consecutive sections. Nearly every deep-learning Gleason paper is validated one section at a time, and the step from there to the number that actually reaches the urologist is left implicit — Silva et al. and Santa-Rosario et al. are cited as the two that did validate at patient level, and neither compared aggregation strategies. This paper’s contribution is to treat the aggregation rule as a design decision with measurable consequences rather than as bookkeeping.

That framing is the transferable part. The specific finding is that the obvious pathologist-mimicking rule — take the highest grade seen anywhere — is the worst-performing option available.

The two things being aggregated

H-ViT (classification). A hierarchical vision transformer from the group’s own prior work (Grisi 2025), three stages: a patch transformer over 256×256 px patches subdivided into 16×16 mini-patches, a region transformer over 2048×2048 regions, and a slide-level transformer. DINO self-supervised pretraining; the “local” configuration — patch transformer frozen, region and slide stages fine-tuned — beat the global one. Trained on all of PANDA.

Segmentation. A U-Net after Bulten 2020, reframed as six-class (benign epithelium plus Gleason patterns 3/4/5), patches of 1024×1024 at 0.5 µm/px. Grade is then computed by a rule: count pixels per pattern, normalise to total epithelium, take primary = most prevalent and secondary = most aggressive, sum. Trained only on the Radboud half of PANDA, because only that half has pixel-level masks.

The rule-based grade computation matters later: it is the one component that behaves consistently across levels, and the reason is that it never learned a level in the first place.

Slide packing, the mechanism that carries the paper

Rather than aggregating predictions, packing aggregates pixels. Aswolinskiy’s WSI packing algorithm rewrites the raw slides into synthetic WSIs at a chosen granularity: one section per image, or all sections of one core composited into a single image, or every section of every core from one patient composited into a single image. The model then makes one prediction on an image that already contains everything the pathologist would have looked at.

This is a genuinely different move from voting, and it is why the comparison is interesting: it lets a slide-level model see across sections without any architectural change, at the cost of feeding it a slide that looks nothing like its training data.

The fields that are usually buried

Training data	PANDA challenge — 10,616 H&E WSIs of prostate biopsies from Radboudumc and Karolinska. Full set for classification; Radboud subset only for segmentation (masks)
Test cohort	Radboudumc, consecutive, 1 Jan – 31 Dec 2022. 2,660 sections / 803 cores / 106 patients. Ethics 2022-15773, consent waived
Cohort shape	Cores per patient 1–6 per slide, most patients 10–12 cores (47%); every core ≥2 sections, 95% ≥3 sections. Exact numbers [supplementary, unread — Table S1]
Scanner / magnification	Not reported for the test cohort. The only resolution stated anywhere is 0.5 µm/px for segmentation training patches. Not a small omission — see appraisal 6
Reference standard	The routine diagnostic pathology report, written by uropathologists as part of clinical work. Patient-level GrG = highest, after lesion-level evaluation for MRI-targeted and side-based aggregation for systematic biopsies
Label granularity	Core-level. Sections inherit their core’s Gleason score — see appraisal 2
Validation strategy	Train on PANDA, test on the Radboudumc 2022 cohort. Patient-level separation explicitly asserted: “no biopsy cores or sections from the same patient were present across sets”
External validation	Partial, and not where the headline is — see appraisal 1
Metric	Cohen’s kappa with quadratic weights (QWK) on the 6-category ordinal scale (benign + ISUP 1–5). No confidence intervals anywhere

The results

All values re-extracted from page geometry, not the text layer.

Table 1 — PANDA test set. This is the only place a geographic comparison appears.

Model	Radboud	Karolinska
Segmentation	0.83	0.52
Section-level H-ViT	0.93	0.90
Biopsy-level H-ViT	0.90	0.87

Table 2 — packed inputs on the Radboudumc test cohort, evaluated at each level. Section-level evaluation uses the biopsy-level reference standard.

Model	Section	Biopsy	Patient
Segmentation	0.67	0.69	0.65
Section-level H-ViT	0.80	0.77	0.69
Biopsy-level H-ViT	0.84	0.87	0.79

Tables 3 and 4 — voting. Table 3 aggregates section→biopsy→patient; Table 4 starts from biopsy-level packed images and votes only biopsy→patient.

Route	Model	Majority voting	Max voting
Section → patient	Segmentation	0.60	0.32
Section → patient	Section-level H-ViT	0.72	0.49
Packed biopsy → patient	Segmentation	0.61	0.43
Packed biopsy → patient	Biopsy-level H-ViT	0.76	0.74

Three orderings hold across every row, and they are the paper’s real output:

• Packing beats voting. 0.79 (Table 2) against 0.76 for the same model voted (Table 4).
• Majority voting beats max voting, always — by 0.28 QWK in the worst case. Max voting is the rule that most resembles clinical practice (“report the highest grade”), and it is comprehensively the worst, because a single spurious high-grade false positive anywhere in ~25 sections sets the patient’s grade.
• Supervising at the level you intend to aggregate at beats supervising below it. The biopsy-trained H-ViT beats the section-trained one at every level including section level (0.84 vs 0.80), which is the mildly surprising result.

Two subgroup findings, both consistent with the above:

• Heterogeneity. Patients split by entropy of GrG across their cores — 37 homogeneous (zero entropy) / 69 heterogeneous. Performance falls in the heterogeneous group for everything, but the strategies invert: majority voting does best when cores agree, packing does best when they do not. That inversion is the mechanistically satisfying result — voting is a consensus operator and fails exactly when there is no consensus to find.
• Core count. Group 1 (2–6 cores) vs Group 2 (9–12). Mean QWK difference between groups 0.03 ± 0.03 for packing, 0.18 ± 0.04 for max voting: more cores means more chances for max voting to catch a false positive. [supplementary, unread — Table S4]

Appraisal

1. The headline result is temporal validation, not geographic — and the paper never says so. PANDA contains Radboudumc data, and the test cohort is Radboudumc 2022. Patient-level independence is explicitly asserted and is the right check, but scanner, staining protocol, laboratory and case mix are shared with part of the training set. The one genuinely external readout is Table 1’s Karolinska column, and it is where the segmentation model collapses (0.83 → 0.52) while H-ViT barely moves (0.93 → 0.90). So the paper does contain strong evidence about generalisation — it is just not attached to the 0.79 that the abstract leads with. See wiki/concepts/external-validation.md.

2. The labels contradict the paper’s own premise. Figure 1 exists to show that Gleason score can vary between sections of one core — that is the motivation for the whole study. Yet “since the individual sections were consecutive, the biopsy-level Gleason score was also assigned to all the sections from that core biopsy.” Every section inherits the core’s grade, which is precisely the assumption Figure 1 says is false. Consequences: section-level training carries systematic label noise (a section without the high-grade focus is still labelled with it), and the section-level column of Table 2 is not a section-level accuracy at all — it is agreement with a core-level standard. This does not invalidate the biopsy- and patient-level results, which are the ones that matter, but it means no number in this paper measures section-level correctness, and the intrabiopsy variability the paper is about is never actually quantified.

3. The reference standard is one routine report, not a consensus re-read. Author contributions: the histology was “assessed by uropathologists … as part of routine diagnostics, generating a report used as reference.” No panel, no re-review, no second reader. So the interobserver ceiling is unmeasured, and a QWK of 0.79 cannot be placed against pathologist-versus-pathologist agreement on the same cases — which for Gleason grading is itself well below 1.0. Contrast the majority-of-six-GU-pathologists reference standard in the TRICARE note. Cheap to have fixed on a subset, and its absence is the single biggest limit on interpreting the headline. See wiki/concepts/interobserver-agreement.md.

4. No dispersion on any headline number. Tables 1–4 are bare point estimates. With 106 patients on a six-category ordinal scale, the confidence interval on a patient-level QWK is wide, and differences like 0.79 vs 0.76 (packing vs voting for the same model) are being read as real without any evidence that they exceed noise. The paper does report mean ± SD for the between-group differences in Figs. 6–7, which makes the omission on the primary results more conspicuous rather than less. A bootstrap over patients would have cost nothing.

5. Self-flagged supervision–inference mismatch. The best patient-level number comes from a model supervised at biopsy level and evaluated at patient level. The authors state this plainly as a limitation and call for further validation — credit where due, but 0.79 should not be quoted without it.

6. Scanner and magnification are not reported for the test cohort. This is normally a routine gap; here it is load-bearing, because the paper’s own explanation for the segmentation model’s Karolinska collapse is “domain shifts from staining and scanner variations.” An argument that rests on scanner differences needs the scanners named.

7. A subgroup gap that is never explained: 7–8 cores. Group 1 is 2–6 cores and Group 2 is 9–12. Patients with 7 or 8 cores appear in neither. The stated reason for grouping at all is “small and imbalanced sample sizes per core count,” so this is plausibly a sparse-cell decision rather than an error — but whether those patients were excluded from the subgroup analysis or simply absent from the cohort is not stated. [unverified — would need Table S3/S4]

8. Nothing here is reproducible from the paper. No code availability statement at all. The two components that would be needed — H-ViT and the packing algorithm — are both other people’s prior work, credited in prose and in the acknowledgments but never linked. H-ViT is in fact public (computationalpathologygroup/hvit, no licence declared); the packing implementation was provided privately by its author and has no stated route to obtaining it. The test cohort is available on request only. So the packing method, which is the paper’s central mechanism, is the least obtainable thing in it.

Recorded, not investigated: G.L. reports equity in Aiosyn BV, the Radboud computational pathology spinout. First author N.U. is funded by the Turkish Ministry of National Education’s YLSY scholarship; G.L. by NWO, the ERC and Oncode.

What it would change here

The finding worth carrying forward is not the 0.79. It is that the aggregation rule is a free parameter that moves performance by up to 0.28 QWK — more than most architecture choices would — and that the clinically intuitive rule (take the maximum) is the worst one. Any local work that runs a section-level model and then reduces to a case-level answer inherits this question, and prostate is not special: the same structure appears wherever several blocks, levels or cores from one specimen must collapse into one reported result.

Packing is the cheaper half of the lesson. It needs no new architecture — only a compositing step before inference — so it is testable against any existing slide-level model, and it is the strategy that held up under heterogeneity, which is the case that actually matters.

Open questions

• Does packing survive a change of institution? Every packing number in the paper comes from the cohort that shares an institution with the training data, and packed slides are exactly the kind of out-of-distribution input where a domain shift would be expected to bite hardest.
• What is the interobserver ceiling on this cohort? Without it, 0.79 has no scale.
• Is there an aggregation rule that is neither max nor majority — a calibrated one that weights a core’s prediction by tumour extent, as pathologists effectively do? The paper’s “custom majority voting” (majority over malignant cores only) is a step in that direction and is the best-performing voting variant, but the space is barely explored.
• How is packing affected by the amount of empty background it introduces? Not discussed, and it bears directly on any attention-based model.