Methylation-Adjudicated Tumor Boundaries in Histopathology

When several pathologists outline the same tumor on a microscope slide, their outlines agree in the tumor's core and diverge at its edge. At that edge, cancer cells blend into normal or inflamed tissue that looks almost the same. Current methods treat this disagreement as something to average away, or as personal style to be modeled. Neither approach can say who was right, because no measurement independent of human eyes exists at the edge. This proposal supplies one. Certain cancers switch off tumor-suppressor genes by adding methyl groups to their on/off control regions (promoter hypermethylation). Healthy tissue of the same organ almost never shows this mark. We would physically sample small tissue cores from the strip where pathologists disagree, measure the fraction of cells carrying cancer-specific methylation, and use those measurements both to adjudicate the disagreement and to train a segmentation model.

The core technical idea is simple. A methylation assay on a punched tissue core cannot say which pixel is tumor, but it can say what fraction of the cells in that core are tumor. A segmentation network predicts a tumor probability for every cell. The average of those predictions over the core should therefore match the molecular fraction. Matching it acts as a weak but biologically grounded constraint on where the boundary lies. The constraint is strongest exactly where human labels are weakest. The same measurements also settle an open empirical question: whether boundary disagreement reflects real, continuous biological transition or observer bias.

Core Claim

Our claim is that bulk tumor-specific methylation, measured on small cores taken from inter-observer disagreement zones, does two things. First, it can identify which annotators' boundaries match molecularly transformed tissue. Second, it can be turned into a training signal of the "learning from label proportions" kind (supervision that gives only the class fraction of a group, not per-item labels). We expect a model trained this way to place infiltrative boundaries more accurately than models trained on rater consensus or on rater-specific distributions. Accuracy here is judged against held-out molecular measurements, not against the raters.

The motivation comes from two places. On the molecular side, promoter hypermethylation of genes such as Cyclin D2 is reported absent in normal gastric tissue (Absence of cyclin D2 expression is associated with promoter hypermethylation in gastric cancer). FBLN1, SFRP2 and DLEC1 are frequently silenced this way in gastric and colon carcinoma (Fibulin 1 is downregulated through promoter hypermethylation in gastric cancer; Frequent epigenetic inactivation of SFRP2 by promoter methylation in human gastric cancer; DLEC1 is a functional 3p22.3 tumour suppressor silenced by promoter CpG methylation in colon and gastric cancers). Methylated SEPT9 is a high-specificity colorectal marker (Cell-Free Circulating Methylated SEPT9 for Noninvasive Diagnosis and Monitoring of Colorectal Cancer). These studies supply the near-binary switch we need, but they all digest tissue or blood into a single number and discard space. We reintroduce space by choosing where to sample.

On the imaging side, two papers attack exactly this disagreement. Pionono models each rater as a Gaussian in a learned latent space and generates rater-specific masks (Probabilistic Modeling of Inter- and Intra-observer Variability in Medical Image Segmentation). DiFF chooses the "ground truth" mask that best helps a downstream diagnostic classifier (Calibrate the Inter-Observer Segmentation Uncertainty via Diagnosis-First Principle). Pionono describes rater behavior but has no external reference: it cannot tell whether an over-segmenter sees real infiltration or outlines reactive stroma. DiFF does have a reference, but it is a slide-level diagnosis. Such a reference rewards masks that capture the obvious tumor bulk and is indifferent to millimeters of margin. Its own authors note the need to relate its learned ground truth to clinical biomarkers. Our reference is spatial and molecular, and it is measured at the margin itself.

Research Program

The program has three parts: a data-collection protocol, a training objective, and an analysis of what disagreement means.

The protocol targets colorectal and gastric adenocarcinoma resections, where the file documents both strong methylation markers and known boundary difficulty. In the GlaS challenge, top methods reach F1 around 0.91 on benign-looking glands but drop sharply on deformed malignant glands (Gland Segmentation in Colon Histology Images: The GlaS Challenge Contest). Each case proceeds in four steps.

  1. Several pathologists, mixing gastrointestinal subspecialists and general pathologists, independently outline tumor on a digitized H&E section.
  2. We compute the disagreement band: pixels called tumor by some raters but not all.
  3. On the matched tissue block or adjacent section, we take small macrodissected or laser-captured cores at three kinds of location: the agreed tumor core, the agreed normal far field, and several points sampled across the disagreement band.
  4. We run a small targeted bisulfite qMSP panel (methylation-specific quantitative PCR) on each core.

The panel uses a few markers, for example SEPT9, SFRP2, DLEC1 and FBLN1, so that no single marker's tumor-to-tumor variability dominates. Tumor-core punches calibrate each marker's methylation level in pure tumor for that patient. Far-field punches give the normal baseline. The molecular tumor fraction of a band core is the background-subtracted methylated signal divided by the patient-specific tumor level, averaged across informative markers. Cryopreservation can distort methylation readouts (Degradation of methylation signals in cryopreserved DNA). We therefore fix one pre-analytical pipeline, preferring fresh formalin-fixed blocks, and record DNA input per core.

The training objective combines two kinds of supervision. Ordinary rater masks supervise pixels outside the disagreement band. Inside the band, supervision comes only from molecular fractions. For core $k$, let $C_k$ be the set of cells (detected nuclei) inside the core footprint, $p_\theta(c)$ the network's tumor probability for cell $c$, and $m_k$ the molecular tumor fraction. We add

$$ \mathcal{L}_{\text{meth}} = \sum_k w_k \left( \frac{1}{|C_k|}\sum_{c \in C_k} p_\theta(c) - m_k \right)^2, $$

where $w_k$ is the inverse of the assay variance of $m_k$, estimated from technical replicates. Low-input or high-variance cores therefore constrain the model less.

The backbone is a rater-conditioned segmentation network in the style of Pionono. This lets us keep rater identity explicit. We can then ask which point in the rater latent space best satisfies the molecular constraint, rather than collapsing raters before training. Unlabeled band regions, where no core was taken, inherit the boundary geometry learned from cored regions. Choosing the next core location to maximize information is a natural extension but is not in scope.

The analysis component tests the tension the file identifies between rater-distribution models and SpaTIE. SpaTIE found that tumor morphology varies along a continuous progression axis correlated with bulk molecular features (Learning latent progression states from spatial heterogeneity in uterine histopathology). For every band core we have both the fraction of raters who called it tumor and its molecular fraction. Three outcomes are possible, and each is informative.

If molecular fraction rises smoothly with rater vote fraction, disagreement tracks a real biological gradient. Consensus averaging is then roughly calibrated, and soft labels suffice. If molecular fraction is bimodal (near zero or near tumor level) and unrelated to vote fraction, disagreement is mostly perceptual error. Specific raters will be systematically right, and the molecular data identifies them. If some raters' extra territory is consistently methylated, over-segmentation captures true infiltration that consensus discards. This is the situation behind the near-zero Gleason grade 5 Dice under consensus reported in Pathological Image Segmentation with Noisy Labels.

Baselines

The naive reference is a standard U-Net-style segmenter trained on the majority-vote mask with cross-entropy plus Dice. This is what a practitioner would do by default. The consensus reference is the same network trained on STAPLE masks. Both use the same backbone, the same stain-normalized training patches, and the same tuning budget, a fixed number of hyperparameter trials on a validation split, as the proposed model.

The strongest competitor for modeling rater disagreement is Pionono. On Gleason 2019 it reports unweighted Cohen's kappa of 0.758 against a prior best of 0.750, and 0.711 on a 25-rater breast dataset (Probabilistic Modeling of Inter- and Intra-observer Variability in Medical Image Segmentation). It is the strongest because it already represents each rater's boundary tendency. A Pionono mask sampled from the "best" rater could match our model without any molecular data. We will run Pionono on our cohort in two forms. One uses the consensus latent. The other is an oracle: the single rater latent that best fits the held-out molecular fractions, chosen post hoc. Our model must beat the oracle form to show that molecular supervision does more than pick a rater.

The second image-only competitor is HRNet18 with pixel-wise rater reweighting and Gaussian attention focal loss. On Gleason 2019 it reports mean Dice of 66.21 and lifts Gleason grade 5 Dice from 0.58% to 29.37% (Pathological Image Segmentation with Noisy Labels). It targets exactly the contested, textured borders but uses image roughness as its proxy. A third competitor is the distance-map boundary loss of Boundary loss for highly unbalanced segmentation, which lifted ISLES Dice from 0.575 to 0.656. It is computed here from the consensus contour, since it needs a single contour. We include DiFF as the diagnosis-anchored alternative. Its published gains are diagnostic-AUC improvements on fundus, ultrasound and dermoscopy (2.73%, 2.51%, 2.04%). No reported result was found on Lacuna for DiFF on histopathology, so its numbers there will be ours.

The decisive ablation keeps every ingredient but swaps the molecular target $m_k$ for a pathologist's visual tumor-cellularity estimate of the same core. A second ablation permutes $m_k$ across cores of the same case, which isolates whether the molecular content, rather than extra loss terms, drives any gain. A third replaces the proportion loss with hard relabeling, marking a band core as tumor if $m_k$ exceeds 0.5. This tests whether the proportion formulation matters.

On the molecular test set, beating a baseline means lower error in predicting held-out band-core molecular fractions, and higher agreement with molecularly adjudicated band labels. The improvement must exceed the across-seed standard deviation, with no loss of Dice in agreed regions.

Why not just…?

Why not just collect more raters and use STAPLE or Pionono? More raters sharpen the estimate of what humans think, not of what the tissue is. Pionono's latent space can encode that one rater systematically over-segments. Nothing in its training can say whether that tendency is right. Consensus is also known to erase rare but real malignant structure; the grade 5 collapse to 0.58% Dice is the documented example. This alternative is a real threat in one scenario: if our analysis finds that molecular fraction tracks vote fraction smoothly, then soft consensus from enough raters is as good as methylation and much cheaper. We would report that as a finding, and the oracle-Pionono baseline is designed to expose it.

Why not use immunohistochemistry or a subspecialist panel as the reference instead? Subspecialist review is still visual reading of the same ambiguous morphology. The file documents that general and subspecialist pathologists differ (Yiping Wang et al.), which makes subspecialists another rater group rather than an external truth. Immunohistochemistry (antibody staining for a protein) is a stronger threat. Where a stain cleanly separates tumor from reactive epithelium, it gives a pixel-level reference that methylation cannot. Two considerations favor methylation. Many stains mark lineage rather than transformation, and stain scoring itself drifts with cutoffs (Wenhui Wang et al.). Methylation marks are reported near-absent in normal tissue of the same organ. We will not argue this abstractly: where a suitable stain exists for a subset of cases, we stain the adjacent section and compare stain-derived and methylation-derived fractions on the same cores. If they agree, the cheaper stain should replace our assay for that cancer type.

Why not train a slide-level model on bulk methylation, as receptor-status models do for IHC? Slide-level multiple-instance learning can predict molecular status from morphology with high accuracy; Clinical utility of receptor status prediction in breast cancer reports AUC 0.95 for estrogen receptor. That paper also shows the weakness: the model outputs one score per slide, delineates no boundary, and struggles with low-expression borderline cases. SpaTIE likewise linked morphology to bulk methylation but performed no contour delineation. A slide-level label carries no information about where within the slide the boundary lies. Spatially targeted cores do, which is why the sampling location, not the assay, is the key ingredient.

Proposed Experiments

The first experiment is a feasibility gate run before any model training. We ask two questions. Does the far-field normal tissue show near-baseline methylation for the chosen markers? Do band cores span a measurable range of fractions? A field effect would show up as substantial methylation in histologically normal far-field mucosa. If we find one, the anchor is confounded and that marker is dropped. If no marker survives for a cancer type, the proposal stops for that type.

The second experiment is the disagreement analysis: molecular fraction against rater vote fraction and against each rater's inclusion of the core. We use per-rater calibration curves and a mixed model with case as a random effect.

The third experiment is the main comparison. We split by patient, hold out a fraction of band cores per patient as test targets, and evaluate every baseline and ablation above. The metrics are error on held-out molecular fractions, accuracy on molecularly adjudicated band labels, and Dice and Hausdorff distance in agreed regions. Hausdorff distance measures the worst-case distance between predicted and reference boundaries.

To show the model does not degrade where public benchmarks apply, we train the image-only parts on Gleason 2019 and GlaS. We report kappa against Pionono's 0.758 and Dice against the 66.21 of the reweighted HRNet model on Gleason 2019, and F1 on GlaS Parts A and B. These benchmarks contain no methylation data, so they test only that the rater-conditioned backbone is competitive, not the central claim.

Finally, as a retrospective pilot requiring no new wet-lab work, we apply only the proportion loss on TCGA-UCEC. There, slide-level bulk methylation exists alongside diagnostic slides, as used by SpaTIE. Profiled and imaged tissue are not the same section, so this pilot can only test whether whole-slide predicted tumor fraction correlates with methylation-derived purity better under our training than under consensus training. The decisive tests remain the band cores.