Counting Witnesses Across the Cohort: Recovering Slide Labels Under Extreme Noise in Gigapixel Pathology

Whole slide images in pathology are gigapixel scans, far too large to feed whole into a neural network. Standard practice cuts each slide into thousands of small patches, encodes them with a frozen feature extractor, and trains a small "aggregator" to predict one diagnosis per slide. This setup is called multiple instance learning (MIL): the slide is a "bag" of unlabeled patches, and only the bag carries a label. Every published MIL system assumes that slide label is correct. In practice, slide labels are often mined from pathology reports or health records, and small metastases are easily missed. Methods from the noisy-label literature that survive 80 to 90 percent corruption on natural images rely on two habits: picking out samples the network fits easily, and voting among similar neighbors. Both habits break on slides, because a correctly labeled positive slide with a tiny tumor is exactly the hard, atypical sample those methods throw away.

We propose to denoise slide labels by counting evidence across the whole cohort instead of judging each slide by its own loss. The two-sentence version is this. Cluster all patches from all slides without using labels. Under random label corruption, the statistical link between "this slide contains patches from cluster k" and "this slide is labeled class c" shrinks by a known factor but never changes sign, so with enough slides the clusters that are evidence for each class can still be found. Those evidence clusters then score each slide's true label, and a standard MIL model is trained on the re-estimated labels.

Core Claim

The claim is that, in gigapixel MIL, bag-level label noise is best fought with instance-level presence statistics pooled across many bags rather than with per-bag loss or confidence. The reason is a simple identity. Suppose a slide's label is replaced by a uniformly random class with probability $r$, independently of the image. Then for any label-free slide statistic $s$ (for example, how many of the slide's patches fall in cluster $k$), the covariance with the noisy class indicator $\tilde y$ is the clean covariance scaled down:

$$\mathrm{Cov}(s, \mathbb{1}[\tilde y = c]) = (1-r)\,\mathrm{Cov}(s, \mathbb{1}[y = c]).$$

This follows because $\mathbb{E}[\mathbb{1}[\tilde y=c]\mid y,s] = (1-r)\mathbb{1}[y=c] + r/C$ for $C$ classes. A cluster that marks tumor in clean data still marks tumor under noise; only the signal-to-noise ratio drops. Detecting a cluster whose clean correlation with the label is $\rho$ therefore needs roughly

$$N \gtrsim \frac{z^2}{(1-r)^2\rho^2}$$

slides, where $z$ is the critical value for the desired confidence level. This scaling comes from the standard error of a sample correlation, $1/\sqrt{N}$. The formula makes a falsifiable prediction: for a given cohort size there is a noise rate beyond which recovery fails, and that rate should be computable in advance from the clean-cohort correlations.

Three features make this suited to gigapixel data specifically. First, the statistic is about presence, the count of a slide's top-matching patches in a cluster, not about how much of the slide a feature covers. A slide with a micro-metastasis in 1 percent of its area therefore still scores as positive, which avoids the problem that its slide-level loss looks "noisy." Second, the method needs only $N$ slides by $K$ clusters of counts. That is cheap because patch features are frozen, which is exactly what the memory constraint forces anyway. Third, under the MIL assumption normal-tissue clusters appear in nearly every slide and carry no class signal, so they drop out automatically.

Relation to Prior Work

The proposal is motivated by a gap. No work in the file evaluates corrupted slide labels in MIL. The MIL architectures CLAM (Data Efficient and Weakly Supervised Computational Pathology on Whole Slide Images), which pseudo-labels its highest- and lowest-attention patches to train a clustering head, and DSMIL (Dual-Stream Multiple Instance Learning Network for Whole Slide Image Classification With Self-Supervised Contrastive Learning), which anchors on a max-scoring "critical" patch, both trust the bag label. Both should actively amplify noise: a mislabeled benign slide forces them to choose a benign patch as tumor evidence. Attention-based Multiple Instance Learning with Mixed Supervision on the Camelyon16 Dataset shows that CLAM's patch pseudo-labels are already poor with clean slide labels (mean Dice 0.215) and repairs this with pixel annotations. We assume neither clean slide labels nor pixel masks.

Several noisy-label methods constrain the design. DivideMix (DivideMix: Learning with Noisy Labels as Semi-supervised Learning) splits data by fitting a two-component mixture to per-sample losses and co-trains two networks. UNICON (UNICON: Combating Label Noise Through Uniform Selection and Contrastive Learning) adds class-balanced selection because loss-based selection discards hard classes. Both judge each sample by its own fit, which is the step we expect to fail on sparse positive slides. TrainRef (TrainRef: Curating Data with Label Distribution and Minimal Reference for Accurate Prediction and Reliable Confidence) and the graph method ICGNN (Identifying and Correcting Label Noise for Robust GNNs via Influence Contradiction) rely on neighbor voting. The ICGNN authors themselves report that it degrades near 80 percent noise and that its diffusion step costs cubic time. Slide-to-slide similarity is also dominated by shared normal tissue, so slide-level neighbors are a weak vote.

CLIPCleaner (CLIPCleaner: Cleaning Noisy Labels with CLIP) cleans labels with a frozen vision-language model and states that its guarantee depends on the domain gap. From Pretraining to Pathology: How Noise Leads to Catastrophic Inheritance in Medical Models shows that web-pretrained pathology encoders such as PLIP have flattened feature distributions that hide localized lesions. That paper supplies a diagnostic we reuse: feature skewness and kurtosis. It is also why we build the patch codebook on in-domain self-supervised features, following DSMIL's SimCLR setup. What our method shares with UNICON and TrainRef is the separation of representation learning from labels. What it adds is the cohort-level covariance test, which no prior method uses.

Research Program

The first stage is label-free. Using frozen self-supervised patch features, we cluster a subsample of patches from all slides into $K$ prototypes, with $K$ swept from 32 to 512. Each slide becomes a vector of top-$q$ presence counts: the number of its patches lying within a tight radius of each prototype. The count is capped so that a slide is not dominated by its tumor area.

The second stage finds witnesses. For each cluster and class, we compute the association between the presence count and the noisy label across the training cohort. We use permutation tests to control false discoveries, which matters because correlations shrink by $(1-r)$. Clusters that pass become class witnesses.

The third stage infers labels. A witness score for each slide gives a likelihood for each true class. We combine it with a noise transition matrix, the table of probabilities that a true class is recorded as each observed class, and obtain a posterior over the true label. We estimate this matrix from slides whose witness evidence is extreme in either direction. This estimation handles asymmetric noise, such as positives recorded as negative because a metastasis was missed.

The fourth stage trains any off-the-shelf aggregator (ABMIL, CLAM, or DSMIL) on soft posterior labels, weighting each slide by its posterior confidence. As an optional refinement round, attention scores from that aggregator replace the fixed prototypes, and witnesses are re-estimated. An ablation measures whether this round helps or reintroduces self-confirmation.

Alongside the method we will run an analysis. We will check whether the predicted break-even noise rate from the second equation, computed from clean-cohort correlations, matches where accuracy actually collapses. We will also check whether witness detectability tracks the kurtosis of the encoder's features, which would tie catastrophic inheritance to downstream label denoising.

Baselines

The naive reference point is the same aggregator (ABMIL, CLAM, and DSMIL) trained directly on noisy slide labels with standard early stopping on a noisy validation split. This baseline is a real threat, not a straw man. Random resampling noise preserves the ordering of the clean posterior, so ranking metrics like AUC may degrade gracefully when frozen features feed a small aggregator. Under clean labels, the published references are CLAM slide AUC 0.895 on Camelyon16 as re-run in the mixed-supervision paper, DSMIL accuracy 89.9 percent on Camelyon16, CLAM AUC 0.991 on TCGA-RCC and 0.956 on TCGA-NSCLC, and HAG-MIL AUC 0.946, 0.982, and 0.921 on the same three sets (Diagnose Like a Pathologist: Transformer-Enabled Hierarchical Attention-Guided Multiple Instance Learning for Whole Slide Image Classification). These figures are the clean ceilings. We found no reported result on Lacuna for any MIL method under corrupted slide labels, so every noisy-label number in this study will be new.

The strongest existing noisy-label competitor is DivideMix and UNICON adapted to the bag level. The per-slide loss of the attention aggregator is fed to the two-component mixture split, the two co-trained networks are attention aggregators, and patch-feature mixup within bags replaces image mixup. Their reported strength on natural images sets expectations: UNICON reaches 90.81 percent and DivideMix 76.0 percent top-1 on CIFAR-10 with 90 percent symmetric noise, and on CIFAR-100 at 90 percent noise UNICON is cited at 44.8 percent versus CLIPCleaner at 63.11 percent. A zero-shot cleaner in the style of CLIPCleaner, using PLIP prompts per patch and aggregated per slide, is the external-anchor baseline. TrainRef with one clean slide per class, and CLAM with mixed supervision on 10 percent of slides, are the reference-data baselines. Our method gets the same reference slides in a matched variant.

All methods share the same frozen patch features, the same splits, five seeds, and an equal hyperparameter budget of 20 trials tuned on a held-out split. That split carries noisy labels only, since a clean validation set would be unavailable in practice. Training time is capped at that of the slowest baseline. Our method beats a baseline if, averaged over seeds, it closes at least half of that baseline's AUC gap to the clean-label ceiling at 60 and 80 percent noise, with a paired bootstrap confidence interval excluding zero.

The key ablation isolates the cohort covariance test. A plain logistic regression on the same presence-count vectors, trained directly on noisy labels, uses identical features but no witness selection, posterior inference, or transition matrix. If this ablation matches the full method, the contribution is the presence-count representation rather than the inference, and we will report it that way. A second ablation replaces capped presence counts with mean-pooled proportions to test the sparse-positive argument directly.

Why not just…?

Why not just train CLAM or ABMIL on the noisy labels and rely on the fact that random noise preserves ranking? This may well work at moderate noise, and the proposal does not assume otherwise. The noise sweep will locate the rate at which plain training departs from the clean ceiling. Our claim is restricted to the regime past that point and to asymmetric "missed metastasis" noise, which does not preserve ranking. If plain training stays within the confidence interval of our method at 80 percent noise, we will report that bag-level noise is benign for frozen-feature MIL. That finding would itself be useful to the field.

Why not just run DivideMix or UNICON at the slide level? The file gives a specific reason to expect failure but no measurement. Positive slides with sub-5 percent tumor area have high loss early in training, so a loss-based split should push them into the "noisy" pool, as UNICON's clean-versus-easy analysis predicts. We will test this directly by reporting, for each method, the fraction of truly positive Camelyon16 slides retained as clean, stratified by annotated tumor area. Co-training also doubles aggregator cost, though with frozen features that cost is tolerable, so compute alone is not a decisive objection.

Why not just filter slides with a pathology vision-language model? CLIPCleaner states its own dependence on domain gap, and the catastrophic-inheritance study shows that PLIP's features are flattened in a way that obscures localized lesions. Both points predict misses on subtle positives. The PLIP-filter baseline, and its kurtosis measurement, will show whether this matters at slide scale.

Why not just annotate a few clean slides and use TrainRef or mixed supervision? Mixed supervision with 10 percent of slides annotated lifts CLAM's clean-label AUC from 0.895 to 0.924. A small clean set is a strong, cheap fix, so we treat it as a complement rather than a rival. The matched comparison asks whether our method with zero reference slides approaches TrainRef with one per class, and whether adding the same reference slides to our transition-matrix estimate helps further.

Proposed Experiments

We use Camelyon16 (270 training and 129 test slides, binary, with pixel annotations), TCGA-RCC (940 slides, three subtypes), and TCGA-NSCLC (1,053 slides, two subtypes). Noise is injected into training labels only, under three models. Uniform resampling uses $r \in \{0, 0.4, 0.6, 0.8, 0.9\}$; for binary tasks this keeps the effective flip rate below one half, where labels remain identifiable. A missed-positive model flips positives to negative at up to 80 percent on Camelyon16. A pair-flip model swaps subtype labels on TCGA. Test labels stay clean. The metrics are slide AUC and accuracy, label-recovery accuracy on the training set, and, on Camelyon16, localization of the recovered witness patches against pixel annotations using Dice and FROC. The localization metrics test whether witnesses are tumor or artifacts.

The decisive checks are three. First, at 80 percent resampling on TCGA-RCC and TCGA-NSCLC, does the method close at least half of plain CLAM's and bag-level UNICON's gap to the clean ceiling? Second, on Camelyon16 under missed-positive noise, does it retain small-tumor positive slides that loss-based splitting discards? Third, does the collapse point observed in the noise sweep fall where the $N \gtrsim z^2/((1-r)^2\rho^2)$ prediction places it? We test the third check by subsampling TCGA cohorts to 250, 500, and 1,000 slides. If the third check fails, the method's success would be unexplained, and we would treat that as a reason to doubt the mechanism even if the accuracy gains hold.