Do Multiple Instance Learning Models Transfer?

Andrew H. Song; Daniel Shao; Faisal Mahmood; Joel Runevic; Ming Y. Lu; Richard J. Chen; Tong Ding

REVIEW 4 major objections 6 minor 61 references

Do Multiple Instance Learning Models Transfer?

T0 review · 4 major / 6 minor · reviewed 2026-08-07 · deepseek-v4-flash

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Pith's one-line read Supervised MIL models pretrained on pancancer tasks transfer across organs and beat slide foundation models while using far less data.

desk verdict A genuinely useful MIL transfer benchmark whose central empirical finding—pretraining helps on average—is solid, but the abstract oversells 'consistently' and the data-efficiency claim ignores the patch encoder's pretraining budget. read the letter →

arxiv 2506.09022 v2 pith:E3MOPJUJ submitted 2025-06-10 cs.CV

Daniel Shao , Richard J. Chen , Andrew H. Song , Joel Runevic , Ming Y. Lu , Tong Ding , Faisal Mahmood This is my paper

classification cs.CV

keywords multipleinstancelearningtransfercomputationalpathologywholeslideimagespancancerpretrainingfoundationmodelsweaklysupervisedattentionaggregation

verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

This paper asks whether a multiple instance learning (MIL) model trained on one weakly supervised pathology task can be reused for another, and finds that it can. Across 11 MIL architectures, 21 pretraining tasks, and 19 downstream benchmarks spanning four organs, the authors report that models started from any supervised pretrained weights—even from a different organ—beat the same architecture trained from random initialization on average. They further claim that a pancancer pretraining task (PC-108, a 108-class cancer-subtyping task on 3,944 slides) produces representations that transfer across organs and task types, outperform two large slide foundation models in most head-to-head comparisons, and do so with only about 6.5% and 2.3% of those models' pretraining data. The practical stakes are that supervised MIL transfer could be a data- and compute-efficient route to general slide-level models, and that the learned aggregation scheme, not the patch encoder, carries most of the transferred knowledge.

What carries the argument

The load-bearing object is the attention-based aggregation layer inside a MIL model, which pools thousands of patch embeddings into a slide-level representation. The paper's mechanistic evidence is that this layer's learned weights are what transfers: SVCCA shows the pretrained attention layer changes little during finetuning (97.7/100 similarity for standard ABMIL, versus 16.3 from random init), and re-initializing just that layer erases most of the transfer gain (-5.0 average points). The pancancer pretraining tasks PC-43 and PC-108, derived from a 108-class OncoTree hierarchical label set at a single institution, are the source of those initializations.

What would settle it

Re-run the 19-task benchmark reporting every task with a single metric (for example, AUROC computed for multiclass tasks by one-vs-rest averaging) and inspect the per-task pretraining-minus-random differences; if the average advantage vanishes or reverses, the commensurability premise behind 'consistently outperform' collapses. A second decisive test: pretrain a model on one organ and finetune on a large, clinically validated cohort from a different organ not represented in PC-108, and check whether the improvement over random initialization persists with narrow confidence intervals.

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Extended reading notes

Core claim

The central discovery is that supervised pretraining of MIL models transfers well in computational pathology, and that the transfer is carried by the aggregation module. The authors evaluate 11 MIL architectures and find that, averaged over 19 classification tasks, every architecture improves with PC-108 pretraining relative to random initialization (average +3.3%), with transformer-based models gaining the most (~5.8%) and simple attention-based ABMIL among the top overall. Pretrained models also excel in few-shot settings: at K=4 samples per class, gains over random initialization reach 171% for one architecture. Using singular-vector canonical correlation analysis and layer-reset experiments, the paper attributes the benefit to the pretrained attention-based aggregation layer: when initialized from PC-108, the attention layer retains near-perfect similarity after finetuning, while resetting it to random weights costs the largest single performance drop. The paper concludes that a pancancer supervised pretraining task can function as a slide foundation model, outperforming CHIEF and GigaPath in 12/15 and 13/15 KNN comparisons (and 11/15 and 10/15 finetuning comparisons) while using substantially less pretraining data.

Load-bearing premise

The summary numbers average AUROC, weighted kappa, and balanced accuracy across 19 tasks with different class counts and chance levels; if that averaging is not a fair way to compare, the exact headline gains (such as +3.3%) are not established, though many individual task comparisons still favor pretraining.

Editorial extensions

If this is right

Any supervised MIL pretraining, including single-organ tasks on a different organ than the target, is a safe default over random initialization for the benchmarked architectures.
A 108-class pancancer pretraining task yields frozen slide-level features that are competitive or superior to features from slide foundation models trained on 10–40 times more slides.
Larger MIL models become more useful when pretrained: PC-108 initialization produces monotonically improving performance up to roughly 5 million parameters for ABMIL, whereas random initialization does not scale smoothly.
In low-data regimes, pretrained MIL models are markedly more sample-efficient, so transfer can make rare-disease and biomarker tasks feasible with only a handful of slides per class.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

If the attention layer is the main thing that transfers, then architecture research should shift toward better pretraining objectives for the aggregator rather than new pooling mechanisms.
A testable extension is whether even more diverse or multi-institution pancancer label sets push the scaling curve further, since PC-108 comes from a single hospital and may understate what larger supervised pretraining could do.
The same supervised-transfer recipe could apply to other weakly supervised gigapixel-imaging domains, such as radiology or dermatopathology, where slide-level labels are easier to obtain than pixel-level labels.
The paper's own single-institution pretraining caveat implies that out-of-distribution drift across hospitals, scanners, and populations remains an open risk that a multi-site replication would need to quantify.

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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Desk Editor's Note

read the letter

You should know this paper for the benchmark, not for its abstract. It is the first systematic look at whether supervised MIL models transfer across organs and tasks in computational pathology: 11 architectures, 21 pretraining tasks, 19 target tasks, with finetuning and frozen-feature evaluation, plus few-shot ablations, scaling studies, and an SVCCA analysis of what transfers. The MIL-Lab resource standardizing implementations and releasing weights is a real community contribution. The core finding—pretraining on pancancer tasks improves average performance over random initialization—is supported by a lot of per-task evidence, and the few-shot gains (DFTD at K=4) are striking. Give credit where due: this is a lot of careful experimental work. The soft spots are in the claims, not the experiment. First, "consistently outperform" is false as stated. Table 1 has several negative deltas (meanMIL on BRACS -8.0, ILRA on BRACS -3.9, WIKG on BCNB -1.0, and others). The average improvement is real, but "consistently" survives only if you average away the failures. Second, the data-efficiency comparison against CHIEF and GigaPath is misleading. The PC-108 models use UNI, GigaPath ViT, or CTransPath patch features, and those encoders were pretrained on huge corpora. Counting only the 3,944 slides for the MIL aggregator ignores most of the pipeline's pretraining budget. The per-aggregator transfer results with matched encoders are fine, but the "substantially less pretraining data" conclusion does not hold for the full slide-embedding model. Third, averaging AUROC, weighted kappa, and balanced accuracy on a single 0-100 scale is statistically dubious; the direction of the aggregate effect is probably right, but the precise magnitudes (+3.3%) are not meaningful. Minor issue: Section 3.2 says "standardized hyperparameters" while Appendix B.1 says "default hyperparameters" from official codebases, and B.2 gives yet another description—sloppy for a paper whose claims are about architecture comparisons. Also, the pretraining data are single-institution and not released, though weights are. Verdict: this deserves a serious referee, but it needs revision. The empirical backbone is valuable, and the resource should exist. The authors should soften the "consistently" and "substantially less data" claims, report per-task results without a single aggregate scale, and fix the hyperparameter description. Send it to review.

Referee Report

4 major / 6 minor

Summary. The paper presents a large empirical study of transfer learning for multiple instance learning (MIL) models in computational pathology. It evaluates 11 MIL architectures across 21 pretraining tasks and 19 target benchmarks, comparing random initialization to supervised pretraining on single-organ and pancancer tasks in both fine-tuning and frozen-feature (KNN) settings. The authors report that pretrained MIL models on average outperform randomly initialized models, that pancancer pretraining generalizes across organs and tasks, and that a PC-108 pretrained ABMIL can match or exceed slide foundation models (CHIEF, GigaPath) despite using a much smaller pretraining corpus. The paper also analyzes model scaling, few-shot performance, and layer-wise feature stability via SVCCA, and releases a public code and weight repository.

Significance. If the headline claims held as stated, this would be a valuable result: supervised MIL pretraining could be a cheap alternative to self-supervised slide foundation models, and the community would gain a large, standardized benchmark for MIL transfer. The study's scale is a strength: 11 architectures, 19 target tasks, multiple seeds, KNN and fine-tuning protocols, and a released repository. The per-task results showing frequent improvements from PC-108 pretraining are credible and useful. However, several load-bearing claims ('consistently outperform,' 'substantially less pretraining data') are not supported as stated, and an internal inconsistency between Table A4 and Table A6 weakens the robustness check. With corrected claims and analyses, the empirical resource would be a solid contribution.

major comments (4)

[Section 4.5 / Table 2] The claim that PC-108 uses 'substantially less pretraining data' than CHIEF and GigaPath (Abstract and Section 4.5) is not supported as stated. The PC-108 models evaluated in Table 2 are built on GigaPath's ViT and CTransPath patch encoders, and the main experiments use UNI features (Section 3.2). Those encoders were pretrained on large corpora (GigaPath: 171,189 WSIs; CTransPath: ~15M patches; UNI: >100M patches). Counting only the 3,944 slides used for the MIL aggregator while ignoring the patch encoder's pretraining budget conflates aggregator cost with full-pipeline cost. When the encoder's data are included, PC-108's total pretraining data is comparable to or larger than GigaPath's, not 2.3% of it. The comparison is also asymmetric: GigaPath and CHIEF must learn their patch representations from their own data, whereas the PC-108 models inherit those encoders for free. The per-aggregator comparisons against random initialization remain valid, but the data-efficiency conclusion should be reworded to refer only to aggregator pretraining data, or the full pipeline cost should be counted.
[Abstract / Section 4.2 / Table 1] The abstract and the introduction bullet claim that pretrained MIL models 'consistently outperform' models trained from scratch. Table 1 reports negative deltas for several architecture-task combinations (e.g., meanMIL BRACS -8.0, ILRA BRACS -3.9, CLAM BRCA -2.7, maxMIL PANDA -0.8). Table A4, the five-seed robustness study, also contains many negative deltas (e.g., ABMIL BRACS-C -2.6, DFTD BCNB-ER -1.0, RRT BCNB-PR -6.2, TransMIL BRCA-ER -4.2). The data support a claim of improvements on average or in the majority of tasks, not 'consistently.' The abstract and Section 4.2 should be revised to match the reported per-task results.
[Section 4.2 / Table A4 vs Table A6] The robustness statement in Section 4.2 ('In all cases, the performance gains from pretraining remained consistent') is contradicted by Table A4, which shows negative deltas for several tasks. Moreover, Table A4 and Table A6 disagree on the same quantity: Table A4 reports ABMIL BRACS-C Base = 71.4 and PC-108 = 68.8 (delta -2.6), while Table A6 reports Base = 64.1 and PC-108 = 68.5 (delta +4.4). This is a large discrepancy (7.3 points in the Base value) that is not explained by seed variation. The authors should reconcile these tables or clarify whether they use different splits/protocols; as written, the robustness claim is not verifiable.
[Section 4.2 / Figure 1 / Table 1] The headline average improvements (e.g., +3.3%, +9.8%) average three different metrics (AUROC, weighted kappa, balanced accuracy) across tasks with different chance levels and variances on a single 0-100 scale. This makes the exact averages hard to interpret and potentially dominated by tasks with lower chance baselines. The authors should report per-metric aggregates or a standardized effect size (e.g., difference from chance level) in addition to the raw average. This does not invalidate the qualitative per-task improvements, but it weakens the specific numeric claims in the abstract.

minor comments (6)

[Section 3.1] Typo: 'tranferrability' should be 'transferability'.
[Section 2.1] Typo: 'auxilliary' should be 'auxiliary'.
[Impact Statement] Typo: 'pancancercer' should be 'pancancer'.
[Section B.1] Typo: 'paramaterized' should be 'parameterized'.
[Section 3.2] Typo: 'optimzier' should be 'optimizer'.
[Figure 1 / Table A4 captions] The captions contain 'A verage' with a stray space; please fix to 'Average'.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: transfer gains are measured against random initialization and external baselines, not derived from fitted quantities.

full rationale

This is an empirical benchmarking study, not a derivation. The central claim that PC-108-pretrained MIL models outperform random initialization is evaluated by direct per-task experiments on 19 public benchmarks with fixed training protocols; the pretrained weights are obtained by supervised training on a separate pancancer label set, and the random-init control uses identical architecture and data, so the comparison is not definitional. The comparison against CHIEF and GigaPath is a head-to-head benchmark on held-out tasks rather than a prediction derived from the paper's own fitted values. Self-citations to the UNI study supply the PC-108/PC-43 tasks and the default UNI patch encoder, but the paper also re-runs key experiments with CTransPath, GigaPath ViT, ResNet-50, UNIv2, and CONCHv1.5 encoders, so the main transfer finding is not forced by a self-citation. One caveat, which is a correctness/accounting issue rather than circularity: the 'substantially less pretraining data' claim in Section 4.5 counts only the 3,944-slide MIL aggregator pretraining set and excludes the patch encoders (UNI, GigaPath ViT, CTransPath) that the evaluated models inherit, so the data-efficiency comparison is asymmetric; however, this does not make the measured transfer deltas circular, since the underlying per-task comparisons remain valid. No equation or fitted input is reused as an output, and no uniqueness theorem or ansatz is imported from the authors' prior work to force the conclusion.

Assumptions & free parameters 0 free parameters · 4 assumptions · 0 invented entities

The paper's claims are empirical and benchmark-based, so there are no fitted constants being passed off as derivations. The main load-bearing assumptions are about the evaluation protocol: the sufficiency of fixed patch encoders, the commensurability of mixed metrics, the integrity of dataset splits, and the validity of SVCCA as an interpretability tool. No new physical or conceptual entities are introduced.

assumptions (4)

domain assumption Pre-extracted patch features from pretrained encoders (UNI, CTransPath, ResNet, GigaPath ViT, UNIv2, CONCHv1.5) are sufficient to capture the information needed for slide-level tasks.
The evaluation pipeline fixes the patch encoder and only trains the MIL aggregator; if patch features discard task-relevant information, the transfer comparisons are upper-bounded by the encoder. The paper mitigates this by testing five encoders, but the assumption is core to the protocol (Section 3.2, Section 4.6).
domain assumption The 19 target tasks and the mixed metrics used (AUROC, weighted kappa, balanced accuracy) can be combined into a single average performance across tasks.
Table 1 and Figure 1 average metrics with different chance levels and scales; this is assumed without statistical justification and is load-bearing for the 'average improvement' and 'consistently outperform' claims.
domain assumption The standard or custom multi-label splits are free of slide-level leakage between training and evaluation.
The paper detects and fixes overlap in NSCLC, BRCA, and BCNB for the shared-split experiments (Appendix C), but for main experiments it relies on official splits; any hidden slide overlap would inflate transfer performance.
standard math SVCCA is a valid tool for quantifying feature stability in MIL networks.
Section 4.9.1 uses SVCCA to argue that the attention layer's stability after fine-tuning explains transfer gains; this assumes SVCCA linear similarity captures the functionally relevant change in the aggregation mechanism.

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Cite this review

Pith. "Pith review of Do Multiple Instance Learning Models Transfer?." pith.science (2026). https://pith.science/paper/E3MOPJUJ

@misc{pith2026250609022,
  author       = {Pith},
  title        = {Pith review of: Do Multiple Instance Learning Models Transfer?},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/E3MOPJUJ}},
  note         = {Machine review of arXiv:2506.09022}
}

read the original abstract

Multiple Instance Learning (MIL) is a cornerstone approach in computational pathology (CPath) for generating clinically meaningful slide-level embeddings from gigapixel tissue images. However, MIL often struggles with small, weakly supervised clinical datasets. In contrast to fields such as NLP and conventional computer vision, where transfer learning is widely used to address data scarcity, the transferability of MIL models remains poorly understood. In this study, we systematically evaluate the transfer learning capabilities of pretrained MIL models by assessing 11 models across 21 pretraining tasks for morphological and molecular subtype prediction. Our results show that pretrained MIL models, even when trained on different organs than the target task, consistently outperform models trained from scratch. Moreover, pretraining on pancancer datasets enables strong generalization across organs and tasks, outperforming slide foundation models while using substantially less pretraining data. These findings highlight the robust adaptability of MIL models and demonstrate the benefits of leveraging transfer learning to boost performance in CPath. Lastly, we provide a resource which standardizes the implementation of MIL models and collection of pretrained model weights on popular CPath tasks, available at https://github.com/mahmoodlab/MIL-Lab

Figures

Figures reproduced from arXiv: 2506.09022 by the authors.

**Figure 1.** Average performance with supervised pretraining vs. random initialization. Performance of MIL models trained from random initialization (black) vs. initialized with weights from a model pretrained (red) on a 108-class pancancer task (n=3,944 WSIs). Performance is averaged across the 19 classification tasks, using AUROC for the binary classification tasks, weighted kappa for grading, and balanced accuracy for the mul… view at source ↗

**Figure 2.** Transfer performance across pretrain tasks. The contingency table shows the average KNN performance of three MIL models (ABMIL, TransMIL, Transformer) transferring from the 21 pretrain tasks (columns, bottom axis) to the 19 target tasks (rows, left axis). The rightmost column (colored gray) shows the baseline of random weights. We use AUROC for binary classification, Cohen’s weighted kappa for prostate grading, an… view at source ↗

**Figure 4.** Transfer at different model scales. Average performance of different ABMIL scales across 19 evaluation tasks with initialization from random weights and PC-108 pretraining. GigaPath, a LongNet-based model (Ding et al., 2023), was pretrained on 171,189 WSIs via a self-supervised masked autoencoder approach, with a ViT patch encoder pretrained on over 1.3 million patches using DINOv2. For a fair comparison, we benchm… view at source ↗

Figures from the paper (2 more)

**Figure 5.** Figure 5: t-SNE of slide-level features. Visualization of the slidelevel features from randomly initialized ABMIL compared to ABMIL pretrained on PC-108 for 12-class brain subtyping for rare brain disease classification. 4.9. What features are being transferred? Supervised MIL…

**Figure 6.** Figure 6: Heatmaps for visualizing attention transfer. Visualization of the three different ABMIL attention heatmaps for lung squamous cell carcinoma: ABMIL with randomly-initialized weights, PC-108 pretrained weights, and finetuned with NSCLC TP53 mutation prediction from PC-1…

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