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REVIEW 3 major objections 4 minor 26 references

A randomly initialized ECG encoder can match state-of-the-art pre-trained models on many tasks, revealing that current benchmarks do not reliably measure representation quality.

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Current ECG representation benchmarks overstate the benefits of pretraining and produce unstable method rankings; a random encoder with linear probing is competitive on many tasks.

T0 review reviewed 2026-08-02 challenge →

load-bearing objection Random-encoder baseline is a genuine and useful finding; the single-seed estimate is the main gap before the headline claim is settled. the 3 major comments →

arxiv 2602.17531 v2 pith:GUTDD3JC submitted 2026-02-19 cs.LG cs.AI

Position: Evaluation of ECG Representations Must Be Fixed

Zachary Berger , Daniel Prakah-Asante , John Guttag , Collin M. Stultz This is my paper
classification cs.LG cs.AI
keywords ECG representation learningbenchmarkingself-supervised pre-trainingrandom baselinemacro-AUROCevaluation protocolclinical taskslinear probing
verification ladder T0 review T1 audit T2 compute T3 formal T4 reserved

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 position paper argues that current benchmarking of ECG representation learning is not measuring what the field thinks it measures. Across three standard public benchmarks and three broader clinical tasks, the authors show that a randomly initialized encoder, evaluated with a simple linear probe, matches the performance of state-of-the-art pre-trained ECG models on many individual tasks. Once confidence intervals and per-task metrics are reported, no pre-training method consistently beats the others, and method rankings shift with simple reporting choices such as whether rare labels are kept. The paper proposes a wider clinical task taxonomy—structural heart disease, hemodynamic state, patient forecasting—and a reporting protocol, contending that evaluation must be fixed before representation learning progress can be reliably judged.

Core claim

The central empirical discovery is that the standard ranking metric—macro-AUROC, the unweighted average of per-label AUROC scores—does not reliably separate ECG representations. Applying a consistent protocol with paired-bootstrap 95% confidence intervals and a randomly initialized 1D ResNet-18 encoder as baseline, the paper finds that the random encoder matches or exceeds the ECG-specific contrastive method CLOCS on several datasets at full training data, and is competitive with the multi-modal methods MERL and D-BETA on structural disease and hemodynamic inference tasks. Removing labels with fewer than ten positive test examples from the PTB-XL FORM benchmark reverses the apparent ordering

What carries the argument

The load-bearing device is the random baseline: a randomly initialized 1D ResNet-18 encoder whose frozen embeddings feed a linear logistic regression probe, so that no information is learned from data. It is the point of comparison that exposes whether pre-training actually helps. Supporting machinery includes paired-bootstrap confidence intervals, per-label AUROC and AUPRC, and the exclusion of labels with fewer than ten positive test examples, all of which alter method rankings when applied.

Load-bearing premise

The paper's conclusion that no pre-training method consistently prevails rests on three chosen methods (CLOCS, MERL, D-BETA) being representative of the 28 surveyed methods; if those three are atypical, the finding could be an artifact of method selection.

What would settle it

Evaluate a larger and more diverse set of pre-trained ECG encoders—contrastive, masked-reconstruction, and multi-modal—on the same six downstream settings. If most encoders beat a randomly initialized baseline with non-overlapping confidence intervals on most individual tasks, the paper's central claim is falsified.

Watch this falsifier. Get emailed when new claim-graph text bears on it.

If this is right

  • Pre-training gains that appear in macro-AUROC often shrink or vanish once uncertainty and a random baseline are included, so reported rankings should not be read as meaningful without these controls.
  • A randomly initialized encoder is a cheap, competitive baseline and should be reported in every ECG representation paper.
  • Benchmark suites should expand beyond arrhythmia and waveform labels to include structural disease, hemodynamic state, and patient forecasting, where currently no method shows consistent superiority.
  • Labels with very few positive test examples materially shift macro-averaged rankings and should be excluded or analyzed separately.
  • Claims of improvement over prior ECG methods should be supported by paired comparisons with confidence intervals, not point estimates.

Where Pith is reading between the lines

These are editorial extensions of the paper, not claims the author makes directly.

  • If the random baseline's competitiveness generalizes to other bio-signals (single-lead ECG, PPG, EEG), reported progress in self-supervised physiological representation learning may be similarly inflated.
  • The results imply that the apparent value of large-scale pre-training on MIMIC-IV may be partly an artifact of the linear probe and dataset composition; a direct test is to compare random encoders of varying architecture and depth on the same suite.
  • The paper's proposed remedy—hidden, containerized benchmarks with private endpoints—would work only if random baselines actually lose on audited, clinically meaningful tasks; otherwise the field should lower its confidence in pre-training benefits.
  • A practical extension: require every new ECG representation method to beat the random baseline with non-overlapping confidence intervals on a majority of endpoints in a fixed, publicly documented suite.
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Editorial analysis

A structured set of objections, weighed in public.

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

Referee Report

3 major / 4 minor

Summary. The paper is a position paper arguing that benchmarking practices for 12-lead ECG representation learning need to be revised. It proposes (i) expanding evaluation beyond arrhythmia/waveform benchmarks to structural disease, hemodynamic inference, and patient forecasting; (ii) reporting per-task AUROC/AUPRC with bootstrapped confidence intervals rather than macro-averaged point estimates; (iii) excluding low-support labels; and (iv) comparing against a randomly initialized encoder baseline. The empirical study evaluates three pre-trained encoders (CLOCS, MERL, D-BETA) plus a random 1D ResNet-18 baseline across six settings, with linear probing at 1%, 10%, and 100% of training labels. The headline claim is that a random encoder matches state-of-the-art pre-training on many individual tasks, and that no pre-training method consistently prevails once uncertainty is quantified. The paper also reports that macro-averaged metrics are sensitive to low-prevalence labels, with a concrete demonstration on PTB-XL FORM where removing four low-support labels flips the MERL/D-BETA ordering.

Significance. If the central claim is sustained, the paper makes a timely and substantive contribution: it would show that the field's standard ranking protocol is not reliably measuring pretraining value, and that a trivial baseline should be included in ECG benchmarking. The work is empirically careful in several respects: paired bootstrap CIs, per-task reporting, label-exclusion sensitivity analysis, standard splits, and a hyperparameter sweep for linear probing. The use of public checkpoints (MERL, D-BETA) and retraining CLOCS on a common corpus is a strength. The main risk is that the random-encoder claim rests on a single initialization and that the 'matches SOTA' language is stronger than the tables support.

major comments (3)
  1. [§5.1, §5.3, §5.4.1] The random encoder baseline is a single randomly initialized 1D ResNet-18. The paired bootstrap CIs in §5.3 condition on that one draw; they do not reflect variance across random initializations. This is load-bearing because the abstract and §1 claim that a random encoder 'matches the performance of state-of-the-art ECG pre-training methods on many tasks.' The paper's own §4 recommendation to 'carefully characterize uncertainty' is not applied to the initialization distribution. Please report results over multiple random seeds (e.g., 5–10) and show the distribution of the headline macro-AUROC and of the task-level results that support the claim. Without this, the central finding could be a lucky draw, and the proposed baseline becomes unstable.
  2. [Abstract, §5.4.1, Table 1] The claim that the random encoder 'matches' state-of-the-art pre-training is stronger than the presented evidence. In Table 1, on PTB-XL SUPER at 100% data, Random (0.861, CI 0.852–0.870) does not overlap with MERL (0.903, CI 0.896–0.910) or D-BETA (0.893); on CPSC2018 at 100%, Random (0.849) is far below MERL (0.931) and D-BETA (0.957). The random baseline is competitive with CLOCS and with the multi-modal methods on some individual tasks (e.g., LVH, CLBBB, hemodynamic tasks at 100%), but calling this 'matches state-of-the-art on many tasks' overstates the support. Please quantify the fraction of tasks where the random encoder is within sampling noise of the best method, and soften the abstract/introduction accordingly.
  3. [§2, Appendix A] The empirical study evaluates only three of the 28 surveyed methods (CLOCS, MERL, D-BETA). The general statement that 'the literature's current conclusion about which representations perform best is altered' depends on these three being representative of the field's SOTA. The selection is justified by public checkpoints, but the paper should explicitly acknowledge which other surveyed methods have available weights and why they were excluded, and avoid extrapolating 'no method consistently prevails' to the full survey set. At minimum, the claims about altering the field's ranking should be scoped to the three evaluated methods.
minor comments (4)
  1. [Abstract] The paper contains two conflicting counts: the abstract at the top says 'five representative ECG pre-training approaches,' while the full-text abstract and §1 say 'three.' Please correct.
  2. [Table 1] Some CI values appear as concatenated strings (e.g., '0.8610.852–0.861'), making them difficult to parse. Please typeset the table with clear separators.
  3. [§4, recommendation 4] The threshold of 'fewer than 10 positive test examples' for label exclusion is presented without justification. Since Table 4 shows that this threshold can flip method rankings, a sensitivity analysis over thresholds (e.g., 5, 10, 20) would strengthen the recommendation.
  4. [§C.2] The CLOCS implementation is modified for 12-lead CMSC (treating leads as channels) and does not apply the perturbations used in the original paper. It would be useful to include a sanity check (e.g., published PTB-XL numbers) to confirm the retrained model is a faithful CLOCS representative.

Circularity Check

0 steps flagged

No significant circularity; the empirical findings are self-contained and not derived from their inputs.

full rationale

The paper's central claims are empirical: applying a fixed evaluation protocol (linear probing, paired bootstrap CIs, per-task reporting) to public checkpoints (MERL, D-BETA) and a retrained CLOCS, and comparing against a randomly initialized 1D ResNet-18 encoder. Nothing in the derivation defines a predicted quantity in terms of a fitted input, and no parameter is fitted to a subset and then renamed as a prediction. The random-encoder baseline is a frozen, untrained network; it is not constructed from the downstream labels or from the pretraining objectives. The comparison tables are straightforward measurements, not algebraic consequences of the paper's own definitions. The self-citations to Schlesinger et al. (2022) and Bergamaschi et al. (2025) provide the private hemodynamic and forecasting datasets; these are external data sources from prior work by overlapping authors, and using them is standard scientific practice. The current paper's conclusions do not reduce to those citations: they depend on running the same evaluation protocol on those datasets, and the results are reported with confidence intervals. Potential concerns such as reliance on a single random initialization, the representativeness of three exemplar pretraining methods, and the non-public nature of the MGH datasets are validity, robustness, or auditability limitations, not circular reasoning. I find no step where the paper's output is equivalent to its input by construction.

Axiom & Free-Parameter Ledger

1 free parameters · 4 axioms · 0 invented entities

The central claims rest on evaluation choices (threshold of 10 positives) and domain assumptions about label validity and method representativeness, but not on any new theoretical entities. The paper's empirical conclusions are therefore sensitive to these choices and assumptions.

free parameters (1)
  • low-support label exclusion threshold = 10 positive test examples
    Section 4 recommends excluding labels with fewer than 10 positive test examples; the CLEAN variant in Table 4/Appendix D.2 uses this cutoff. The choice of 10 is hand-chosen, and the ranking reversal (MERL vs D-BETA on FORM) depends on this threshold.
axioms (4)
  • domain assumption Linear probing on frozen embeddings is a meaningful measure of representation quality.
    Invoked throughout Section 5.3; the paper evaluates all methods with a single linear layer, which favors certain pretraining objectives and may not reflect full fine-tuning behavior.
  • domain assumption The three selected methods (CLOCS, MERL, D-BETA) are representative of the surveyed 28 ECG representation learning methods.
    Stated in Section 2 and 5.1 as exemplars; the conclusions about 'no method consistently prevails' are extrapolated from this small set.
  • domain assumption Right heart catheterization and echocardiography ground truth labels in the private MGH datasets are sufficiently accurate for benchmarking.
    Used in Sections B.5 and B.6; the paper does not provide label-noise analysis for these tasks.
  • standard math Paired bootstrap confidence intervals correctly capture sampling variability of AUROC/AUPRC.
    Used throughout Section 5.3; standard statistical technique, assumed valid for this setting.

reviewed 2026-08-02 · how reviews work

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Cite this review

Pith. "Pith review of Position: Evaluation of ECG Representations Must Be Fixed." pith.science (2026). https://pith.science/paper/GUTDD3JC

@misc{pith2026260217531,
  author       = {Pith},
  title        = {Pith review of: Position: Evaluation of ECG Representations Must Be Fixed},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/GUTDD3JC}},
  note         = {Machine review of arXiv:2602.17531}
}
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read the original abstract

This position paper argues that current benchmarking practice in 12-lead ECG representation learning must be fixed to ensure progress is reliable and aligned with clinically meaningful objectives. The field has largely converged on three public multi-label benchmarks (PTB-XL, CPSC2018, CSN) dominated by arrhythmia and waveform-morphology labels, even though the ECG is known to encode substantially broader clinical information. We argue that downstream evaluation should expand to include an assessment of structural heart disease and patient-level forecasting, in addition to other evolving ECG-related endpoints, as relevant clinical targets. Next, we outline evaluation best practices for multi-label, imbalanced settings, and show that when they are applied, the literature's current conclusion about which representations perform best is altered. Furthermore, we demonstrate the surprising result that a randomly initialized encoder with linear evaluation matches state-of-the-art pre-training on many tasks. This motivates the use of a random encoder as a reasonable baseline model. We substantiate our observations with an empirical evaluation of five representative ECG pre-training approaches across six evaluation settings: the three standard benchmarks, a structural disease dataset, hemodynamic inference, and patient forecasting.

Figures

Figures reproduced from arXiv: 2602.17531 by Collin M. Stultz, Daniel Prakah-Asante, John Guttag, Zachary Berger.

Figure 1
Figure 1. Figure 1: Overview of the evaluation pipeline for 12-lead ECG representations. (a) Current practice focuses on arrhythmia/waveform tasks and macro-AUROC point estimates, which can produce misleading method rankings. (b) We propose a broader set of clinically relevant tasks and evaluation best-practices that more reliably assess methods. We find that no method consistently prevails and for many tasks, many methods ov… view at source ↗

discussion (0)

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Reference graph

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This paper was first reviewed by deepseek-v4-flash on August 2, 2026.