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REVIEW 4 major objections 6 minor 34 references

Robustness of transferability estimation metrics for medical imaging

T0 review · 4 major / 6 minor · reviewed 2026-08-12 · deepseek-v4-flash

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Pith's one-line read Transferability estimation metric rankings in medical imaging are unstable to target resampling and to the evaluation metric used for the reference ranking.

desk verdict A careful, well-scoped negative result on transferability estimation in medical imaging; the seed-instability findings are solid, while the low-agreement claim needs reference-noise quantification. read the letter →

arxiv 2608.09999 v1 pith:GE5TE4W6 submitted 2026-08-07 eess.IV cs.CV

Niclas Cla{ss}en , Théo Sourget , Dovile Juodelyte , Rob van der Goot , Veronika Cheplygina This is my paper · ORCID
classification eess.IVcs.CV
keywords metricsdatasetevaluationimagingmedicalmetricmodelrankings
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

Transfer learning reuses a model trained on one dataset, the source, as a starting point for another dataset, the target. In medical imaging, choosing the wrong source wastes time and compute. Transferability estimation (TE) metrics promise to rank candidate source models cheaply, without fine-tuning all of them. The authors test seven TE metrics on eight MedMNIST targets plus ImageNet as source. They sample small versions of each target at 5, 10, 25, 50, and 75 percent of the training data, with five different random seeds. They then ask three questions: does a metric rank sources the same way across random seeds; does a metric's ranking from a subset agree with its ranking on the full dataset; and do different metrics agree with each other? They also fine-tune all sources on each target, optimizing once for accuracy and once for AUROC, and use those test results as the reference ranking. The results are negative in a useful way. Rankings from the same TE metric vary across random seeds for small targets such as Breast. The evaluation metric used for the reference ranking changes the order of sources substantially. Agreement between TE metrics and either reference ranking is low across nearly all targets. The authors note that some reference rankings rest on tiny performance differences, for example all sources reach AUROC above 0.99 on Blood. These findings mean that comparing TE metrics with a single random seed or a single evaluation metric can easily produce arbitrary conclusions.
Extended reading notes

Core claim

The paper states: "we observe a low agreement between rankings from TE metrics and reference" (Abstract) and shows that rankings from TE metrics change across random seeds and that the evaluation metric changes the reference rankings (Sections 4.1 and 4.2, Figures 3, 7, and 8). If correct, this means TE metric evaluations in medical imaging are not reliable when based on a single random seed or a single evaluation metric.

Load-bearing premise

The reference ranking from fine-tuning is treated as ground truth for transferability. Section 3.3 assumes that fine-tuning with Optuna and test-set evaluation produces a valid ranking, while Section 4.2 admits that on Blood all source models exceed 0.99 AUROC, so ranks rest on negligible differences. If the reference itself is noisy, the low TE/reference agreement could partly reflect reference noise rather than TE metric failure. In addition, only ResNet-18 and MedMNIST v2 are tested, so the generality of the instability finding is assumed rather than demonstrated.

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Editorial analysis

A structured set of objections, weighed in public.

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

Referee Report

4 major / 6 minor

Summary. The paper studies the robustness of seven transferability estimation (TE) metrics for medical imaging classification, focusing on two factors: variations in the target dataset representation (subset size and random seed) and the choice of evaluation metric used to construct the reference ranking. The authors use eight MedMNIST v2 targets and thirteen source models, compute TE rankings on nested stratified subsets with five seeds, and fine-tune ResNet-18 models with Optuna to obtain reference rankings under accuracy and AUROC. They report that TE rankings vary across seeds and subset sizes, that reference rankings depend on the evaluation metric, and that agreement between TE rankings and the fine-tuning reference is generally low. The paper also releases code and model checkpoints.

Significance. If the claims are established, this is a useful and cautionary empirical study for the transferability estimation community, particularly for medical imaging where data scarcity makes TE metrics attractive. The paper has notable strengths: it covers seven TE metrics, uses three correlation coefficients, constructs nested stratified subsets with multiple seeds, and provides open code, checkpoints, and data splits. The evidence that TE rankings are seed-sensitive and that reference rankings depend on the evaluation metric is compelling in its qualitative patterns. However, the headline claim of low TE-reference agreement is weakened by the absence of any quantification of reference-ranking noise and by ambiguities in how the reference seeds are handled in the analysis. As written, the central conclusion is not fully separated from measurement error.

major comments (4)
  1. [Section 3.3, Section 4.2, Figure 8] The reference ranking is treated as ground truth, but its noise is not quantified. Section 3.3 states that the reference is built from a single Optuna run per source-target-metric combination on the full train set, and Section 4.2 concedes that on Blood all source models exceed 0.99 AUROC and that reference rankings change across subset sizes and seeds. Since rank-correlation measures are attenuated by noise in one of the two rankings being compared, the low TE-reference agreement in Figure 8 and the abstract could partly reflect reference noise rather than genuine failure of the TE metrics. The authors should quantify reference noise, for example by repeating fine-tuning runs (even for a subset of conditions) or by comparing the observed TE-reference correlations to the reference-reference stability across the two 5% seeds already available in Appendix F. Without such a comparison, the central 'low agreement' conclusion is not established.
  2. [Section 3.3, Figures 3, 4, 6, 8] All stability values are reported as averages over seeds with no measure of dispersion, confidence interval, or significance test. For example, Figure 3 averages pairwise Kendall's Tau over five seeds, but no standard deviation, per-seed values, or confidence intervals are shown. This makes it impossible to judge whether the differences between TE metrics or subset sizes are meaningful, and whether the 'low agreement' values in Figure 8 are statistically distinguishable from zero or from each other. Please provide error bars or bootstrap confidence intervals, and include per-seed results in an appendix.
  3. [Section 3.3 (Ex2), Figure 8 caption] The number of seeds used for the reference ranking in Ex2 is ambiguous. The text says that fine-tuning on 5% subsets is repeated for only two random seeds (Section 3.3), yet Figure 8's caption says that the stability is averaged over five random seeds for subsets smaller than 100%. If only two reference rankings exist for the 5% condition, the five-seed average cannot be computed unless TE rankings on seeds without a corresponding reference are compared against one of the two available references, which would conflate seed variation with TE-reference agreement. Clarify the exact pairing of TE and reference rankings, and if necessary compute the average only over the two seeds for which both TE and reference rankings are available.
  4. [Section 4.2, Appendix A] The reference rankings are based on test-set scores rounded to three decimal places (Appendix A), and for some targets the ranking differences are extremely small (e.g., Blood AUROC values from 0.997 to 0.999). Rank correlations computed on such near-ties are dominated by measurement noise, yet no sensitivity analysis is provided on how the ranking would change under small perturbations of the scores. A tie-aware or confidence-interval-aware reference would help establish whether the reference itself is meaningful, especially for the 100% condition in Figure 8 where a single reference run is used.
minor comments (6)
  1. [Equation (2)] There is a typo in the text: 'both from a the same TE metric' should read 'both from the same TE metric'.
  2. [Section 4.1] Several missing spaces appear, for example 'NLEEPandSFDA', 'ForNLEEPthis', and 'SFDA, this is due'.
  3. [Section 2.2] The related work describes the LPFU metric from Juodelyte et al. [13], but LPFU is not included in the seven evaluated metrics; the authors should clarify why it is omitted from the experiments.
  4. [Section 3.3, Equation (1)] The summation indices in Equation (1) are written as 'u-1 X i=1 u X j=i+1', which is hard to parse; consider using a clearer notation such as summing over all pairs i < j.
  5. [Appendix C] The NLEEP adjustment in Appendix C is presented post hoc, changing the PCA energy and number of Gaussian components to improve stability. Please state explicitly whether these modified settings are used in any of the main results, or clearly label the appendix as a supplementary diagnostic.
  6. [References] Several reference entries have awkward line breaks in the DOI or URL fields (e.g., references 20 and 25); please ensure the bibliographic formatting is clean.

Circularity Check

0 steps flagged · score 2.0 of 10

No significant circularity: TE rankings are compared against an external fine-tuning reference, and no claimed prediction is constructed from its own inputs.

full rationale

The central comparison in this paper is not circular. TE metric rankings are measured against a reference ranking produced by actual fine-tuning and test-set evaluation, which is independent of the TE scores. The paper does not fit TE metrics to the reference, nor does it define transferability in terms of the TE scores. The instability results across random seeds (Fig. 3, Eq. 1) are self-contained and do not depend on the reference at all. The low-agreement result in Fig. 8 uses the fine-tuning reference as an external benchmark; even though the reference may be noisy, that is a measurement-validity concern, not a circularity. The only overlapping self-citations are to Juodelyte et al. [13], used for grouping TE metrics, for the known SFDA degeneracy, and for LPFU; these are contextual and not load-bearing for the paper's new findings. The NLEEP adjustment in Appendix C is a post-hoc hyperparameter change presented as a robustness check, not as a validated prediction, and it does not drive the central conclusion. Overall, the derivation chain is self-contained against an external benchmark, so no part of the claimed result is equivalent to its inputs by construction.

Assumptions & free parameters 6 free parameters · 4 assumptions · 0 invented entities

The study is empirical, so the ledger lists the experimental choices and domain assumptions that define scope. No invented entities and no fitted constants enter the central claim.

free parameters (6)
  • subset_fractions = 5%, 10%, 25%, 50%, 75%
    Hand-chosen fractions define miniature populations; results are specific to these sizes.
  • n_random_seeds = 5
    Five stratified nested subsets per fraction; Ex2 uses only 2 seeds for 5%, which limits precision.
  • architecture = ResNet-18
    All source and fine-tuned models use ResNet-18; generalization to other architectures is assumed.
  • NLEEP_pca_energy = 0.9 (Appendix C; default 0.8)
    Post-hoc adjustment to reduce NaN values; alters NLEEP rankings in the sensitivity appendix.
  • NLEEP_gaussian_components = 1 per class
    Post-hoc adjustment from the default of 5 components per class.
  • hyperparameter_search_ranges = lr 1e-5 to 1e-2; weight decay 1e-6 to 1e-2; batch 128
    Chosen ranges and batch size are experimental constants, not fitted to the conclusion.
assumptions (4)
  • domain assumption MedMNIST v2 2D datasets and ImageNet are representative of medical transfer learning settings.
    Section 3.2 selects eight MedMNIST targets and five source-only datasets; the paper generalizes its conclusions to medical imaging from this pool.
  • domain assumption Fine-tuned test accuracy and AUROC, after hyperparameter optimization, are valid reference rankings of transferability.
    Section 3.3 defines the reference ranking from fine-tuning; the authors note in Section 4.2 that these rankings can rest on negligible performance differences.
  • domain assumption The seven TE metric implementations from original papers are correct and comparable in their default forms.
    Section 3.3 says implementations come from original or related work with minor adjustments; the paper does not revalidate them.
  • standard math Spearman, Kendall, and weighted Kendall correlations are appropriate agreement measures for rankings.
    Section 3.3 uses these three correlation coefficients; their properties are standard, but the choice of coefficient affects results.

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Cite this review

Pith. "Pith review of Robustness of transferability estimation metrics for medical imaging." pith.science (2026). https://pith.science/paper/GE5TE4W6

@misc{pith2026260809999,
  author       = {Pith},
  title        = {Pith review of: Robustness of transferability estimation metrics for medical imaging},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/GE5TE4W6}},
  note         = {Machine review of arXiv:2608.09999}
}
read the original abstract

In transfer learning, the choice of source model largely influences the performance on a target dataset. Still, selecting a fitting source remains a challenging task, especially in medical imaging where one has to decide between models pre-trained on off-the-shelf options, such as ImageNet, and domain specific datasets. Transferability estimation (TE) metrics address this problem by aiming to predict the best performing source model in a computationally cost effective way. However, previous work has reported conflicting TE metric performances due to differences in experimental setups. Moreover, most TE metrics are designed for and evaluated on natural images, while being optimized for accuracy, whereas in medical imaging metrics that are more robust to class imbalance are typically used. We study the impact of varying the target dataset as an isolated factor, by constructing miniature populations of different sample sizes and random seeds. In addition, we investigate the influence of the evaluation metric used to obtain the reference ranking. We find that small modifications to the target dataset change the rankings. Furthermore, we show that the choice of evaluation metric affects the reference rankings and therefore the evaluation of TE metrics. Overall, we observe a low agreement between rankings from TE metrics and reference. The code, model checkpoints and data splits used in this work are available through https://github.com/niclasclassen/robustness-of-transferability-estimation-metrics-for-medical-imaging.

Figures

Figures reproduced from arXiv: 2608.09999 by the authors.

Figure 1
Figure 1. Illustration of our study. We asses the robustness of existing TE metrics with regards to different target dataset representations, as well as the evaluation metric used for the reference ranking. In this work, we take a step back and focus on the robustness of existing TE metrics [PITH_FULL_IMAGE:figures/full_fig_p002_1.png] view at source ↗
Figure 2
Figure 2. Comparing Spearman’s rank correlation coefficient ρ, Kendall’s Tau τ , and weighted Kendall’s Tau τw under different ranking scenarios. In A we have a moderate agreement according to ρ, while τ and τw indicate a weak correlation. Moreover, C is superior over B when looking at τ , whereas B outperforms C when considering τw. All correlation coefficients range from −1 to 1, where −1 = perfect negative correlation, 0 =… view at source ↗
Figure 3
Figure 3. Average (over 5 random seeds) pairwise Kendall’s Tau (stabilityintra) across target subsets of varying sizes for different TE metrics. The target datasets are sorted by absolute train set size in ascending order. Blank fields indicate NaN values. picture. Looking at how the TE metrics behave across target datasets and sub￾set sizes, we find greater variability among smaller target representations among all TE metric… view at source ↗
Figures from the paper (5 more)
Figure 4
Figure 4. Figure 4: Average (over 5 random seeds) pairwise Kendall’s Tau (stabilityref ) between rankings obtained from target subsets of varying fraction sizes and the ranking obtained using 100% of the data. The target datasets are sorted by absolute train set size in ascending order. B…
Figure 5
Figure 5. Figure 5: Source model rankings based on TE metrics LEEP, LogME, and H-score for Breast subsets with fraction size 5%. The subsets are generated with five different random seeds. is more extreme for LogME for which Blood is ranked as both the most and least suitable source for d…
Figure 6
Figure 6. Figure 6: Average pairwise Kendall’s Tau (stabilityinter) between rankings from different TE metrics. For subset sizes < 100%, agreement is computed between subsets generated with identical random seeds and then averaged over 5 seeds. Low agreement between TE metrics and referen…
Figure 7
Figure 7. Figure 7: Stability of rankings obtained from two fine-tuning runs, optimized separately for accuracy (ACC) and AUROC on the full train set, considering Kendall’s Tau τ , weighted Kendall’s Tau τw, and Spearman’s rho ρ. representations, meaning that a source model’s position can…
Figure 8
Figure 8. Figure 8: Average (over 5 random seeds for subsets < 100%) pairwise Kendall’s Tau (stabilityref ) between TE metrics and reference ranking from fine-tuning, optimized separately for accuracy and AUROC. Blank fields indicate NaN values. Although this study provides valuable insig…

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Pith tools

Reviewed August 12, 2026 · model on record in the stance chip above.