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Under review as a conference paper at ICLR 2027

LUCID: Frozen Unsupervised Diffusion Features for EEG Decoding

Abstract

EEG foundation models pretrain on large corpora to learn general representations that transfer to downstream decoding tasks. Yet they are typically evaluated after full fine-tuning, entangling what pretraining encodes with what task labels supply. To separate the two, we present (Latent Unsupervised Characterisation from Internal Diffusion): an unsupervised diffusion model trained from scratch on each dataset, then frozen, with its internal activations read by a small linear probe. Two properties of EEG shape 's denoiser. Along the time axis, the signal is densely sampled and autocorrelated, with rhythms spanning tens of milliseconds to seconds; patching or tokenizing it, as most foundation models do, coarsens these dynamics. Across electrodes, channel power and inter-channel coupling shift from window to window – a nonstationary covariance that no fixed spatial operator can follow. We therefore build a time-preserving denoiser from structured long convolutions and, within each block, introduce , a spatial-modulation operator that adapts to each window's own covariance. We evaluate on ten EEG decoding tasks across twelve datasets against seven task-specific supervised networks, a diffusion-based representation model, and six fully fine-tuned foundation models. On five of the twelve datasets, its frozen features tie the best of these foundation models. Re-evaluating each foundation model frozen, with only its head trained, reveals a pattern: ties where these models gain little from fine-tuning and trails where they gain most. It is also label-efficient, matching its full-label accuracy with a quarter of the labels on half of the datasets and keeping at least four fifths of it on the rest. These findings argue for evaluating EEG representations frozen, not only after full fine-tuning. Beyond decoding, generates synthetic EEGs that capture much of the spectral, temporal, and spatial structure of real recordings. Our source code is made available.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG, diffusion models, representation learning, unsupervised learning, brain decoding

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
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Paper summary

The authors train a diffusion model on EEG data in an unsupervised manner, then freeze it and use a linear classifier to categorize signals based on internal features extracted from various layers. Their contributions include an approach for adapting channel processing to signal covariance (CoSMO), an auxiliary task for feature learning across different layers (XLAP), and a comparison between frozen and fine-tuned models. Validation across 12 datasets demonstrated performance comparable to fine-tuned foundation models on five of them; cross-dataset transfer was not evaluated.

Critical strengths

A systematic investigation into the role of pre-training and fine-tuning: a comparison across 12 datasets reveals where frozen features are sufficient for competitive performance, and where label-based adaptation provides a significant advantage.

Critical weaknesses

Although CoSMO is presented as one of the key contributions, the ablation studies do not demonstrate a convincing, standalone improvement in balanced accuracy across the four datasets examined. Its benefits emerge primarily when combined with XLAP and in terms of certain additional metrics. Consequently, the main contribution of this work appears to be largely empirical - an analysis of the capabilities and limitations of frozen EEG representations - whereas the significance of the proposed architectural innovations is less compellingly justified.

Questions for authors
  • Could you provide a more compelling demonstration of the added value of CoSMO compared to XLAP (without CoSMO) - taking into account both the variance in results and the computational costs?
  • Why are the MAT results considered comparable, given that the average quality for LUCID is 6.6 percentage points lower? Can you demonstrate that this gap is practically insignificant, rather than simply falling within the range of a large variance in results?
1 comment
AuthorsOpenReview ↗

Contribution, CoSMO ablations and cost, and the MAT comparison

Thank you for the careful review and for highlighting the value of the frozen feature study. We address CoSMO's added accuracy and cost separately from the overall results, then revisit MAT.

W1: the contribution. LUCID learns without labels from one dataset's training recordings, freezes the diffusion model, and reads its features with one linear probe. As reported in the submission, its mean balanced accuracy exceeds its untrained copy on all twelve datasets, by 4 to 34 points. The method provides EEG features for linear decoding without supervised backbone adaptation. LUCID tests no transfer. Frozen versus fine tuned comparisons provide context.

CoSMO's seperate contribution remains a design hypothesis: the paper's four dataset ablation does not establish a standalone gain in balanced accuracy. We now test its added value on four more datasets.

W1 and Q1: adding CoSMO to XLAP. The base model has neither component and the full model has both. The last column compares Full with XLAP only. CoSMO only is not shown. Scores are balanced accuracy pooled over test windows, as proportions (mean ± SD over five seeds).

How all comparisons in this response are computed. Differences are percentage points. The 95% percentile intervals use 10,000 resamples of test subjects with replacement, within class groups on COMA, Mumtaz and TUEV. Models and settings stay fixed. We average balanced accuracy over five training seeds. Separated means p < .05 after Holm correction. This p value is a bootstrap tail area whose calibration has not been measured. Not separated does not mean equal.

Dataset (test subjects)Base modelXLAP onlyFullFull − XLAP only [95% interval]
COMA (41)0.3728 ± 0.01220.4170 ± 0.00790.4038 ± 0.0092−1.3 [−2.8, +0.2]
SLEEP (14)0.6900 ± 0.01900.6951 ± 0.02030.7071 ± 0.0077+1.2 [−2.4, +5.3]
Mumtaz (11)0.8972 ± 0.00850.9002 ± 0.00260.8995 ± 0.0068−0.1 [−1.0, +0.9]
TUEV (63)0.5099 ± 0.03400.5327 ± 0.02190.5744 ± 0.0104+4.2 [−1.1, +7.1]

The last column compares Full with XLAP only at the same readout settings. All four intervals include zero. Base scores provide context.

On TUEV, XLAP only exceeds Base by +2.3 [+0.7, +3.6] points, separated under the stated procedure after Holm correction over the original four TUEV component contrasts. This provides positive evidence for XLAP on this dataset at this readout.

The displayed TUEV Full exceeds XLAP only by +4.2 points, with positive differences in all five seed pairs. This is descriptive support, since the patient interval includes zero. The difference is negative on COMA, near zero on Mumtaz and positive with a wide interval on SLEEP. CoSMO's added value therefore remains uncertain.

On the paper's original four ablation datasets (MAT, BCIC-IV-2a, SEED-V, PhysioNet-MI), Full has the highest five seed mean, above Base and XLAP only on each. This supports the combined model descriptively. CoSMO only's AUC-PR and AUROC gains on MAT are also descriptive. MAT and BCIC-IV-2a have 4 and 2 test subjects, so receive no interval. The ablation analyses for TUAB (253 test subjects), FACED and BCIC2020-3 are pending.

Q1: computational cost. At inference, CoSMO adds 16 to 18% of paramters and about 20% of operations on SLEEP, Mumtaz and TUEV. XLAP is used only during training. With XLAP enabled, adding CoSMO multiplies training time per epoch by 1.43 on TUEV, 1.47 on SLEEP and 1.65 on Mumtaz. The new datasets do not establish an accuracy return for this cost.

Q2: MAT. LUCID scores 0.7000 against fine tuned REVE's published 0.7660 (El Ouahidi et al., 2025), a 6.6 point deficit. Our tie rule favoured LUCID because of its larger seed spread (0.0731). AUC-PR is also lower (0.5984 against 0.7470).

With four test subjects we give no interval, and no equivalence margin was set in advance. We cannot show that the gap is "practically insignificant" and withdraw the tie rule and the "five ties". With fewer than five test subjects, we report per subject scores without a verdict.

Changes to the paper. We will foreground the dataset specific learner and its frozen features, add the component contrasts and costs, and replace the tie claims with measured differences.

These findings provide positive evidence for XLAP on TUEV and descriptive support for the combined model. They do not establish a general CoSMO advantage or synergy. We would welcome your perspective on this contribution and our interpretation of the component results. We will post the TUAB, FACED and BCIC2020-3 tables when their analyses finsih.

Reference

El Ouahidi et al. (2025). REVE: A Foundation Model for EEG Adapting to Any Setup with Large-Scale Pretraining on 25,000 Subjects. NeurIPS 2025.

Reviewer_KQEfOpenReview ↗
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Paper summary

This paper questions whether fine-tuned performance reflect the pre-trained representations on EEG domain. Authors propose LUCID, dataset-specific diffusion denoiser with time-preserving SLConv backbone, covariance adapting spatial modulation (CoSMO), and a training-only objective (XLAP). Frozen and fine-tuned features are evaluated across 12 datasets, and LUCID's frozen features approach to the best fine-tuned models where fine-tuning gains are small and fall behind where the gains are large.

Critical strengths
  1. The rich comparison of frozen and fine-tuned EEG models on many datasets.
  2. The clear presentation and detailed explanations of methods with controlled ablations on CosMO and XLAP.
  3. The authors discuss limitations of the dataset-specific training comparison, and of the window level label subsampling.
Critical weaknesses
  1. The initial problem statement, the proposed method, and experimental validation is not logically clear. Separating pretraining from FT does not seem to connect to non-patch processing, convolution replacing attention, and diffusion objective. The claimed harm from patching is not directly tested. EEG is a non-stationary domain, but attention already provides input-dependent mixing, so the non-stationarity argument does not establish an advantage of the proposed spatial mixing instead of attention.

  2. It is not clear what do we earn from comparing frozen/FT features and finding LUCID fails in datasets where FT gain is large. Since the idea of comparing frozen/FT itself is not a new approach, just applying this comparison broader in EEG domain alone doesnt seem to be that much of a contribution, unless it gives a new insight in pretrain-FT dynamics or feature representations. Authors clarify that the task does not transfer, but still the contribution withis this dataset-specific setting seems to be narrow.

  3. Label-efficiency results do not directly seem to reduce annotation costs. Subsampling labeled windows does not necessarily reduce the number of annotated recordings or trials. Even though authors acknowledge this, it still limits the connection to the contribution to clinical labeling cost.

Questions for authors
  1. Is there any ablations to show that non-patch processing performs better than patch-based processing? And does replacing attention with SLConv have additional advantage?

  2. What is the advantage of CoSMO over spatial attention, which already has input-dependent mixing?

  3. What novel insights or conclusions can be earned from the FT-gain ordering, beyond the frozen/FT comparison itself, and would it be consistent under different fine-tuning settings?

  4. Does label efficiency advantage still applies when independently annotated recordings or trials are reduced, while keeping the pretraining the same?

4 comments
AuthorsOpenReview ↗

Response (1/2): scope, design choices, Q1

Thank you for the careful review. Your questions help separate measured benefits from architectural motivations.

W1 and W2: contribution and scope. LUCID learns EEG features from each dataset's unlabelled training recordings, freezes the diffusion model, and reads its features with one linear probe. It needs no external corpus or supervised backbone adaptation. As reported in the submission, its mean balanced accuracy exceeds that of its untrained copy on all twelve datasets, by 4 to 34 points. It requires training per dataset and tests no transfer.

Our contribution is this learner and its frozen features. The frozen versus fine tuned benchmark provides context, not a justification for the architecture.

Q1: patching and SLConv. We have no patching or attention ablation and claim no advantage over either. Their rationale is:

  • Patch free input. Hwang et al. (2026) argue that tokenisation makes a model learn how chunks follow each other rather than how the waveform unfolds. This motivates retaining sample level temporal resolution.
  • Long convolutions. Attention costs time quadratic in window length. Patching lowers that cost by coarsening time. Structured long convolutions build on state space models (Gu et al., 2022). They use long, decaying kernels with few parameters, applied by FFT (Li et al., 2022). Vetter et al. (2024) used them to model neural recordings with diffusion.

These are design motivations, not demonstated advantages.

W2: what the objective comparison adds. We compare diffusion with masked reconstruction on the same backbone. This tests the pretraining objective, without testing patching or attention.

The masked model reconstructs half of each window's samples, zeroed on all channels in five temporal segments, with squared error loss. The data, backbone, initial weights and budget are shared. Both models use CoSMO without XLAP, so neither is full LUCID. In the clean comparison, both are frozen and read on clean input with the same probe over five paired seeds. A contrastive pretext remains untested.

Reading the results in both parts. Balanced accuracy is pooled over windows. We compute 95% percentile intervals from 10,000 resamples of test subjects with replacement, within class groups on COMA, Mumtaz, TUAB and TUEV. Models and settings stay fixed, and seed scores are averaged. Separated means p < .05 after Holm correction within its family. This p value is a bootstrap tail area whose calibration has not been measured. Intervals are unadjusted. Not separated does not mean equal. MAT, BCIC-IV-2a and Siena have only 4, 2 and 2 test subjects, so receive no interval or p value. We withdraw the "five ties", which rested on seed spread.

The table lists datasets where diffusion scores higher. Scores are balanced accuracy in % (mean ± SD over five training seeds per model). Differences are diffusion minus masking in percentage points, computed before rounding, with 95% intervals over test subjects.

Dataset (test subjects)DiffusionMasked reconstructionDiffusion − masked [95% interval]Reading
SEED-V (16)39.8 ± 0.236.0 ± 0.4+3.8 [+1.3, +6.4]separated
BCIC2020-3 (15)32.8 ± 0.826.7 ± 1.0+6.2 [+3.4, +9.0]separated
MAT (4)69.9 ± 6.156.7 ± 3.5+13.3above in all five seed pairs, too few test subjects for an interval
BCIC-IV-2a (2)40.5 ± 2.833.4 ± 1.4+7.0above in all five seed pairs, too few test subjects for an interval
TUEV (63)55.2 ± 1.652.7 ± 1.7+2.6 [−3.6, +7.8]mild advantage, not separated

On PhysioNet-MI and COMA, diffusion shows no advantage over masked reconstruction. For PhysioNet-MI (20 test subjects), with the diffusion model read at its noise level chosen on validation, the difference is +0.2 [−2.4, +2.5], not separated. For COMA (41 test subjects) the difference is −4.1 [−11.1, +2.3], not separated. The same clean comparison has been launched on SLEEP, Mumtaz, TUAB and FACED. We will post each result as it finishes.

The matched comparison shows gains from diffusion on SEED-V and BCIC2020-3 under our stated comparison procedure. Diffusion also scores higher in all five seed pairs on MAT and BCIC-IV-2a, although their small test cohorts limit the conclusions. These gains provide evidence about the pretraining objective beyond the frozen versus fine tuned benchmark. The gains depend on the dataset and comparison protocol. We draw no conclusion from TUEV.

References (both parts)

  • El Ouahidi et al. (2025). REVE. NeurIPS 2025.
  • Gu et al. (2022). Efficiently Modeling Long Sequences with Structured State Spaces. ICLR 2022.
  • Hwang et al. (2026). B[FM]². arXiv:2606.20812.
  • Li et al. (2022). What Makes Convolutional Models Great on Long Sequence Modeling? ICLR 2023.
  • Vetter et al. (2024). Generating Realistic Neurophysiological Time Series with Denoising Diffusion Probabilistic Models. Patterns.
  • Zhou et al. (2025). CSBrain. NeurIPS 2025.
AuthorsOpenReview ↗

Response (2/2): CoSMO ablations, fine tuning gains and whole subject label budgets

Q2: CoSMO versus spatial attention. CoSMO uses each window's channel covariance to guide spatial mixing. Attention also adapts to its input, so adaptability alone establishes no advantage. We have not compared them. The ablation tests CoSMO within our backbone.

Base has neither component, XLAP only omits CoSMO, and Full has both. Scores are balanced accuracy as proportions (mean ± SD over five seeds). Differences are percentage points.

Dataset (test subjects)Base modelXLAP onlyFullFull − XLAP only [95% interval]
COMA (41)0.3728 ± 0.01220.4170 ± 0.00790.4038 ± 0.0092−1.3 [−2.8, +0.2]
SLEEP (14)0.6900 ± 0.01900.6951 ± 0.02030.7071 ± 0.0077+1.2 [−2.4, +5.3]
Mumtaz (11)0.8972 ± 0.00850.9002 ± 0.00260.8995 ± 0.0068−0.1 [−1.0, +0.9]
TUEV (63)0.5099 ± 0.03400.5327 ± 0.02190.5744 ± 0.0104+4.2 [−1.1, +7.1]

The last column compares Full with XLAP only at the same readout settings. All four intervals include zero. Base scores provide context.

On TUEV, XLAP only exceeds Base by +2.3 [+0.7, +3.6] points, separated under the stated procedure after Holm correction over the original four TUEV component contrasts. This supports XLAP on TUEV at this readout.

Full's TUEV gain of +4.2 points is positive in all five seed pairs. This is descriptive support, since its patient interval includes zero. The difference is negative on COMA, near zero on Mumtaz and positive with a wide interval on SLEEP. CoSMO's benefit within this backbone remains uncertain.

In the original ablations (MAT, BCIC-IV-2a, SEED-V, PhysioNet-MI), Full has the highest five seed mean, above Base and XLAP only on each. This descriptively supports Full. CoSMO only's AUC-PR and AUROC gains on MAT are also descriptive. MAT and BCIC-IV-2a have 4 and 2 test subjects, so receive no interval. The ablation analyses for TUAB (253 test subjects), FACED and BCIC2020-3 are pending.

Q3: fine tuning ordering. For each dataset, mean gain is mean fine tuned minus mean frozen score across models. LUCID's deficit to the best fine tuned model equals that gain plus two gaps: mean frozen score minus LUCID's score, and best fine tuned score minus mean fine tuned score. In a post hoc check, shuffling the gaps together across datasets with gain fixed gave a median correlation of 0.86 versus 0.91. The quantities share a term, so we retain the ordering as descriptive and withdraw "reveals a pattern".

We have not tested the ordering under controlled recipe changes across datasets. REVE illustrates protocol sensitivity (El Ouahidi et al., 2025). On PhysioNet-MI, LUCID trails fine tuned REVE by 9.5 to 16.4 points at every label budget (point estimates). On TUAB, our untuned rerun scores 80.61%, below the published 83.15% and native frozen REVE's 82.43%. The gain changes sign, but montage and split also differ, so we cannot isolate wich change matters.

W3 and Q4: withholding whole subjects' labels. On all twelve datasets, budgets withhold selected subjects' labels for all their training recordings and trials. Training stays fixed. Five class stratified subsets per budget use proportionally reduced validation sets to retune the probe, with at least one subject per class. Intervals also resample the five label subsets.

Two comparisons with local fine tuned REVE (balanced accuracy, %). We can provide LUCID's curves for all twelve datasets. REVE uses one recipe per dataset, with checkpoints chosen on each budget's validation subset.

Dataset (test subjects, labelled training subjects at 10/25/50/100%)Model10%25%50%100%
TUAB (253, 151/378/755/1510)LUCID78.7180.5082.0782.83
REVE FT78.5180.0580.8580.61
TUEV (63, 19/46/93/185)LUCID36.7447.5250.6057.44
REVE FT30.7939.7143.0247.58

Under these local recipes, LUCID's mean balanced accuracy is higher than fine tuned REVE's at every budget on TUAB and TUEV. These examples show that its frozen features support useful decoding with labels from fewer whole subjects, without supervised backbone adaptation.

Across available comparisons, LUCID is separated above REVE or CSBrain in 12 of 102 contrasts and below in 16 (Zhou et al., 2025), after Holm correction within the declared families. These results do not establish general superiority or annotation savings.

Changes to the paper. We add the objective test, component results and subject budget curves, and distinguish architectural motivations from tested advantages. We clarify label efficiency using whole subject budgets and distinguish fewer labels from measured annotation savings.

We would welcome your perspective on what the objective, component and subject budget results establish about LUCID's value as an EEG representation learner.

Thank you for the additional experiments. The comparison experiments partly addresses my concerns. However, the benefits of the main architecural design (non-patch processing and replacing attention into SLV conv) and the insight from the FT-gain ordering are still unclear. And narrowing the claims does not resolve my concern about the contribution of the paper. Therefore, I maintain my rating.

Thank you for clarifying your concern. We chose to preserve sample timing and use SLConv to combine information over long intervals. Our experiments leave open whether processing EEG at its original temporal resolution improves decoding over patching, and whether SLConv offers an advantage over temporal attention.

The clearest finding concerns the complete learner. Using the same preprocessed EEG and logistic regression procedure, we compared frozen LUCID features with two standard EEG summaries. Across the nine datasets with enough test subjects for our statistical comparison, LUCID’s advantage in balanced accuracy met our stated criterion on four datasets against tangent space features and on five against log bandpower features. This gives a concrete benefit on some tasks: a denoiser trained on the dataset’s own unlabelled recordings can yield features from which a linear probe decodes more accurately. Which design choices produce that benefit remains open.

We also agree that the fine tuning gain ordering has limited explanatory value. The mean fine tuning gain enters the expression for the gap between LUCID and the best fine tuned model, so a high correlation can arise from that shared term. We therefore treat the ordering as descriptive. It does not explain why particular tasks benefit more from fine tuning.

Reviewer_7NH8OpenReview ↗
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Paper summary

LUCID investigates how much EEG decoding information is linearly accessible before supervised backbone adaptation. It trains an unconditional DDPM from scratch on the unlabelled training recordings of each dataset, freezes its denoiser, and fits a logistic-regression probe to pooled activations from all residual blocks. The denoiser preserves temporal resolution with structured long convolutions. CoSMO conditions electrode gains and low-rank spatial mixing on each input window's covariance; XLAP adds a training-only masked-channel covariance/log-variance prediction objective with cross-layer pooling. The evaluation covers ten tasks across twelve datasets, six foundation models with frozen and fine-tuned read-outs, seven supervised networks, EEGDM, and an untrained identity-map control. LUCID improves over its untrained control on all datasets, and the authors describe five matches to the best fine-tuned foundation model using their seed-standard-deviation tie rule. Performance is substantially weaker on several tasks. The paper also reports component and feature-width ablations, label-subset experiments, and synthetic-signal statistics. This is in-domain unsupervised representation learning, not cross-dataset foundation-model transfer.

Critical strengths

A useful evaluation question with broad empirical coverage. Separating frozen representations from supervised backbone adaptation is important for interpreting EEG pretraining. Evaluating twelve datasets and six foundation models in both modes provides a broader view than a single-task demonstration. LUCID's gains over its untrained copy on every dataset and the training-only PCA control support the existence of learned, linearly readable information, even though they do not isolate the diffusion objective.

An EEG-motivated architecture with informative negative results. CoSMO provides an explicit mechanism for conditioning spatial mixing on window-specific second-order statistics, while XLAP makes intermediate blocks participate in a shared auxiliary task. The 2×2 ablation, width reduction, and disclosure of large deficits on FACED and imagined speech make the evidence more informative than reporting only favorable datasets. The authors also clearly acknowledge the absence of cross-dataset transfer and matched-objective controls.

Critical weaknesses

The comparative conclusions lack adequate statistical support. The paper reports means and standard deviations over five training seeds, but does not provide formal statistical tests or confidence intervals for the key performance differences supporting claims of superiority and matching, including the comparison with the identity-map control. Section 3.2 instead declares a tie whenever the mean gap is within either method's one-seed-standard-deviation band. This heuristic neither establishes equivalence nor accounts for uncertainty across test subjects, and can reward instability: MAT's 0.7000 +/- 0.0731 is described as matching 0.7660 +/- 0.0355 despite a 6.6-percentage-point mean deficit. Seed variability alone is insufficient to substantiate population-level performance comparisons. The central claims require appropriate difference estimates and statistical assessment respecting the subject/trial structure; matching claims additionally require a justified practical-equivalence or non-inferiority margin, since failure to reject a difference is not evidence of equivalence. Without such analysis, the reported mean differences remain descriptive, and the five-dataset matching conclusion is not adequately established.

The distinct value of LUCID is not sufficiently motivated or demonstrated. If the research goal is to distinguish pretrained representation quality from supervised adaptation, comparing existing foundation models frozen and fine-tuned addresses that question more directly; the paper does not clearly explain why a new dataset-specific diffusion model is necessary. If the goal is a better EEG representation learner, LUCID does not consistently outperform frozen foundation models despite training its backbone on each target dataset's unlabelled recordings. Where a foundation model's pretraining corpus excludes the target dataset, its frozen evaluation also demonstrates cross-dataset transfer, which LUCID does not test; this conditional distinction requires corpus-overlap verification. More importantly, the proposed advantage of diffusion in learning continuous, multiscale structure from full multichannel signals is not specifically validated. The identity-map comparison establishes a benefit of training, component ablations compare variants within the diffusion framework, and generated-signal statistics do not establish a comparative representation advantage or connect structure preservation to decoding gains. The paper neither isolates diffusion against alternative pretexts on matched data and backbones nor identifies a distinct scientific finding that requires diffusion rather than the existing foundation-model analysis. Consequently, the motivation does not yet establish a clear link between the proposed method and a demonstrated practical or scientific benefit.

Questions for authors
  1. What distinct research or practical contribution does LUCID establish beyond evaluating existing frozen foundation models? Comparing the same foundation model frozen and fine-tuned more directly addresses what its pretrained representation provides and what supervised backbone adaptation adds. Why is a new, dataset-specific diffusion model necessary to answer this question? From a performance perspective, LUCID does not consistently outperform the frozen foundation models. If a foundation model's pretraining corpus excludes the downstream dataset, its frozen evaluation additionally tests cross-dataset transfer, whereas LUCID trains its denoiser on each target dataset's unlabelled training recordings. Please clarify corpus overlap and explain what benefit justifies this additional target-domain training. Separately, the introduction motivates diffusion as learning continuous, multiscale structure by reconstructing noise-corrupted, full multichannel signals. Where do the results specifically demonstrate this proposed advantage? The mixed downstream results, untrained control, and component ablations do not isolate it. If the intended advantage is scientific insight rather than decoding performance, what specific, valuable finding or conclusion does diffusion enable that the existing foundation-model analysis cannot provide, and which experiment establishes it? Please distinguish this contribution from the general recommendation to report both frozen and fine-tuned results.

  2. Why are ties defined using seed standard deviations rather than a formal statistical assessment? Section 3.2 treats a mean difference within either method's one-seed-standard-deviation band as a tie. This can classify a less stable method as matching a stronger baseline: on MAT, LUCID obtains 0.7000 +/- 0.0731 versus 0.7660 +/- 0.0355 for the best fine-tuned foundation model. What statistical justification supports this rule and the resulting five-dataset matching claim? Please report uncertainty for the relevant performance differences, including trained LUCID versus the identity-map control, using an analysis appropriate to the dataset's subject/trial structure and training variability. For claims of matching performance, a nonsignificant superiority test alone would not establish equivalence; would the conclusions hold under an equivalence or non-inferiority analysis with a justified, prespecified practical margin?

  3. What further finding, hypothesis, or explanation follows from the association between fine-tuning gain and LUCID's relative deficit? Section 3.3 reports a Spearman correlation of 0.91 and discusses exceptions, but the current analysis appears to identify a preliminary pattern among performance metrics. What substantive hypothesis about EEG representations or task requirements does this pattern support, and what evidence tests that hypothesis beyond the correlation itself? Please explain whether the association remains informative after accounting for the shared fine-tuned performance terms in the gain and deficit, differences in result provenance/training recipes, and task characteristics. In particular, what does this analysis establish beyond the descriptive observation that LUCID tends to trail more on datasets where supervised adaptation helps foundation models more?

2 comments
AuthorsOpenReview ↗

Response (1/2): contribution, statistics, former ties, fine tuning gain

Thank you for the careful review. LUCID learns EEG representations from each dataset's own recordings without labels, freezes the diffusion model, and reads its features with one linear probe. Your description ("in-domain unsupervised representation learning, not cross-dataset foundation-model transfer") captures this scope. Our new analyses address W1 and W2 by clarifying what these frozen features provide and how the pretraining objective affects decoding. We address the matching claims below.

Reading the comparisons in both parts. Differences are in percentage points of balanced accuracy, pooled over windows. We compute 95% percentile intervals from 10,000 resamples of test subjects, with replacement and within class groups on COMA, Mumtaz, TUAB and TUEV. Models and settings stay fixed. Balanced accuracy is averaged over each model's training seeds (five for LUCID).

We call a difference separated when p < .05 after Holm correction within its comparison family. This p value is a bootstrap tail area whose calibration we have not measured. Bracketed intervals are unadjusted for multiple comparisons. Not separated does not mean equal. MAT, BCIC-IV-2a and Siena have only 4, 2 and 2 test subjects, so receive no interval or p value.

W2 and Q1: what LUCID contributes. Two comparisons, using the same bootstrap, assess the linearly readable information:

  • Untrained copy: with the submitted identity map control, LUCID's mean is higher on all twelve datasets, by 4 to 34 points. It is separated on 8 of the 9 datasets with intervals, from +7.0 [3.2, 10.7] on PhysioNet-MI to +34.1 [30.1, 37.9] on TUAB. Among the separated comparisons, the largest adjusted p values are for SLEEP (+12.8 [2.3, 23.6], adjusted p = .035) and COMA (+15.4 [4.2, 27.9], adjusted p = .016). Mumtaz is not separated (+4.1 [−13.4, +21.3]).
  • Frozen foundation models: all six use the same linear probing procedure as LUCID. Among the 54 dataset and model pairs with intervals, LUCID is separated above in 19, below in 6 (PhysioNet-MI, FACED), and not separated in 29.

Unsupervised diffusion features can give better linear decoding than some frozen foundation models. These gains are dataset dependent. LUCID needs a model per dataset and tests no transfer, but needs no external corpus, including for private COMA data.

Our contribution is this learning procedure and its evaluation, not the general recomendation to compare frozen and fine tuned models.

W1 and your question on ties. The one seed SD rule has no statistical justification. On MAT, it favoured LUCID through its larger seed spread, despite a score of 0.7000 against 0.7660 (a 6.6 point deficit). We withdraw it.

The five former ties. The paper claimed ties with the best fine tuned foundation model on five datasets. Below, positive differences favour LUCID and negative differences favour the comparator. Our reruns provide predictions for the same test subjects, enabling paired intervals. Published means allow only point differences.

All rows use LUCID's submitted settings. For SLEEP, we use our strongest local REVE rerun.

Dataset (test subjects)Fine tuned comparatorLUCID − comparator [95% interval]
COMA (41)BIOT, our rerun+0.1 [−9.1, +10.5]
SLEEP (14)REVE, our strongest rerun+1.5 [−2.7, +5.7]
TUAB (253)REVE, published mean−0.3
MAT (4)REVE, published mean−6.6
Siena (2)CSBrain, published mean+4.4

The paired intervals now quantify uncertainty over test subjects. Neither difference is separated, which does not establish equality. With no equivalence or noninferiority margin set in advance, we withdraw the matching claims.

Your question on the fine tuning gain. The correlation is descriptive, not an explanation. For the paper's reported scores, mean fine tuning gain is mean fine tuned score minus mean frozen score.

For each dataset, LUCID's deficit to the best fine tuned model equals the mean fine tuning gain plus two gaps: the mean frozen score minus LUCID's score, and the best fine tuned score minus the mean fine tuned score. All means use the same foundation models. The two quantities being correlated therefore share the gain term.

To examine this dependence, we held each dataset's gain fixed, shuffled the two gaps together accross datasets, and recalculated the deficits using the identity above. The median correlation was still 0.86, and 29% of shuffles reached the observed 0.91.

Replacing reported fine tuning scores with available local reruns, while retaining the other printed values, gives a correlation of 0.93. This limited provenance check does not isolate training recipe effects or remove the shared score term. The original comparison includes 13 published fine tuning scores from splits different from ours. We have not tested task characteristics as an explanation, so the association remains descriptive. We withdraw "reveals a pattern".

AuthorsOpenReview ↗

Response (2/2): representation learning benefit, corpus overlap and diffusion versus masked reconstruction

Corpus overlap (W2 and Q1). We agree: a frozen foundation model tests transfer when its pretraining excluded the target dataset. LUCID learns from each target dataset's training recordings and does not test transfer. We checked published corpus descriptions and available recordings.

Our datasetListed in the pretraining data ofStated as removed by
TUAB, TUEVBIOT, CBraMod, CSBrain, CodeBrainREVE, LaBraM
SLEEPREVEnone stated
PhysioNet-MILaBraMREVE
SienaREVE, LaBraMnone stated
Mumtaz, BCIC-IV-2a, BCIC2020-3, FACED, MATnone listedREVE
SEED-Vnone listedLaBraM
COMA (private)none listednone stated

TUAB, TUEV, SLEEP, PhysioNet-MI and Siena appear in at least one model's pretraining list. The other seven are unlisted. Transfer must be assessed for each model and dataset pair. An absent listing or stated removal does not verify exclusion from a checkpoint's training data.

Recording checks:

  • REVE's open training subset contains signals matching 101 of PhysioNet-MI's 109 subjects, despite its stated removal of downstream recordings (El Ouahidi et al., 2025).
  • LaBraM lists four other TUH subsets. Our local releases of those subsets contain exact copies of 130 of our 276 TUAB test recordings and matching signals for 29 of our 159 TUEV test files.

These checks establish overlap between data collections. Wether the released checkpoints used those recordings remains unknown. Transfer claims for the frozen models therefore remain conditional on their actual pretraining exposure.

W2 and Q1: why train a diffusion model? Our goal is better EEG representations learned from each dataset without labels or an external corpus. Comparing existing models frozen and fine tuned measures adaptation, but does not test whether diffusion improves frozen features. We therefore compare diffusion with masked reconstruction on the same backbone.

The masked model reconstructs half of each window's samples, zeroed on all channels in five temporal segments, with squared error loss. The data, backbone, initial weights and budget are shared. Both models use CoSMO without XLAP, so neither is full LUCID. In the clean comparison, both are frozen and read on clean input with the same probe over five paired seeds. A contrastive pretext remains untested.

The table lists datasets where diffusion scores higher. Scores are balanced accuracy in % (mean ± SD over five training seeds per model). Differences are diffusion minus masking in percentage points, computed before rounding, with 95% intervals over test subjects.

Dataset (test subjects)DiffusionMasked reconstructionDiffusion − masked [95% interval]Reading
SEED-V (16)39.8 ± 0.236.0 ± 0.4+3.8 [+1.3, +6.4]separated
BCIC2020-3 (15)32.8 ± 0.826.7 ± 1.0+6.2 [+3.4, +9.0]separated
MAT (4)69.9 ± 6.156.7 ± 3.5+13.3above in all five seed pairs, too few test subjects for an interval
BCIC-IV-2a (2)40.5 ± 2.833.4 ± 1.4+7.0above in all five seed pairs, too few test subjects for an interval
TUEV (63)55.2 ± 1.652.7 ± 1.7+2.6 [−3.6, +7.8]mild advantage, not separated

On PhysioNet-MI and COMA, diffusion shows no advantage over masked reconstruction. For PhysioNet-MI (20 test subjects), with the diffusion model read at its noise level chosen on validation, the difference is +0.2 [−2.4, +2.5], not separated. For COMA (41 test subjects) the difference is −4.1 [−11.1, +2.3], not separated. The same clean comparison has been launched on SLEEP, Mumtaz, TUAB and FACED. We will post each result as it finishes.

Unlike comparisons between released foundation models, this experiment links the objective to decoding quality with the backbone and budget fixed. We draw no conclusion from TUEV.

Changes to the paper. Foundation models become context, and the full masked comparison is added. We have not linked the decoding gains to multiscale structure, so we remove that explanation from the introduction. The concern that masking can disrupt fine temporal variation remains a motivation from prior work. Generation statistics remain a byproduct.

The matched comparison shows gains from diffusion on SEED-V and BCIC2020-3 under our stated comparison procedure. Diffusion also scores higher in all five seed pairs on MAT and BCIC-IV-2a, although their small test cohorts limit the conclusions. Together with the gains over some frozen models in part 1, this supports diffusion as a useful option for learning linearly readable EEG features without an external corpus. The gains depend on the dataset and comparison protocol. We would welcome your perspective on what this evidence adds to the representation learning question raised in W2.

Reference

El Ouahidi et al. (2025). REVE: A Foundation Model for EEG Adapting to Any Setup with Large-Scale Pretraining on 25,000 Subjects. NeurIPS 2025.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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