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REVIEW 3 major objections 7 minor 40 references

Data Normalization Strategies for EEG Deep Learning

T0 review · 3 major / 7 minor · reviewed 2026-08-07 · deepseek-v4-flash

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Pith's one-line read Normalization for EEG deep learning should be matched to the learning objective: per-window, per-channel scaling for supervised tasks, and minimal or cross-channel window-level scaling for self-supervised contrastive learning.

desk verdict Useful, honest empirical comparison of EEG normalization, but the headline claim that supervised and self-supervised learning need different normalization is confounded by window size: the decisive SSL result uses 20-s windows while supervised tasks use 2-s. read the letter →

arxiv 2506.22455 v1 pith:EZRDHGWT submitted 2025-06-15 eess.SP cs.LG

Dung Truong , Arnaud Delorme This is my paper · ORCID
classification eess.SPcs.LG
keywords EEGdeeplearningdatanormalizationself-supervisedcontrastivepredictivecodingageregressiongenderclassificationpreprocessingresting-state
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 one normalization recipe can serve all EEG deep learning pipelines, and answers no. Across two supervised tasks (age regression and gender classification) on resting-state EEG from 2,836 participants, the best results come from robust normalization applied per window and per channel: age mean absolute error of $2.48 \pm 0.36$ years and gender balanced accuracy of $0.85 \pm 0.03$. For a self-supervised Contrastive Predictive Coding pretext task, the same recipe hurts, and leaving normalization minimal or cross-channel at the window level gives the lowest loss. The authors conclude that normalization must be matched to the learning objective, which matters as EEG research moves toward large pretrained models.

What carries the argument

The carrying mechanism is the factorial normalization taxonomy itself: two levels (recording vs window) crossed with three scopes (none, cross-channel, within-channel), applied with robust scaling based on the median and interquartile range. Cross-channel normalization preserves the relative voltage scale between channels, while within-channel normalization keeps only the temporal structure inside each channel. The taxonomy isolates where normalization statistics are computed, and the same encoder architecture (Deep4Net, a temporal-and-spatial convolutional net) is then probed on age regression, gender classification, and Contrastive Predictive Coding with same- or different-recording distractors, making the comparisons attributable to normalization rather than to model choice.

What would settle it

Fine-tune or linearly probe each of the pretrained encoders on a downstream EEG task such as sleep-stage or emotion classification and compare normalization rankings; if the minimal or cross-channel window-level strategy no longer yields the best downstream accuracy, the paper's self-supervised recommendation is overturned.

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Extended reading notes

Core claim

The paper's central claim is that optimal EEG normalization depends on the training paradigm, not just the data. The authors define a 3-by-3 grid of strategies: normalization statistics computed over the full recording or over each short window, and either across all channels jointly, per channel independently, or not at all. Within this grid, window-level within-channel normalization is the clear winner for supervised subject-attribute prediction, while Contrastive Predictive Coding with same-recording distractors performs best with no recording-level normalization and cross-channel normalization at the window level. A systematic failure also appears: recording-level cross-channel normalization combined with window-level within-channel normalization produces NaN losses across tasks, consistent with incompatible feature scaling. The paper therefore challenges the common one-size-fits-all practice of recording-level, per-channel scaling in EEG preprocessing.

Load-bearing premise

The load-bearing premise is that Contrastive Predictive Coding pretraining loss is a valid measure of how good the self-supervised representation is, yet the paper evaluates only that loss and explicitly notes it does not fully capture downstream utility.

Editorial extensions

If this is right

  • Supervised EEG pipelines should move to window-level within-channel normalization; recording-level normalization alone underperforms for age and gender prediction.
  • Self-supervised EEG pretraining with same-recording contrastive objectives should avoid within-channel window-level normalization and prefer no normalization or cross-channel window-level scaling.
  • Recording-level cross-channel combined with window-level within-channel normalization is a configuration to avoid because it reliably collapses training to NaN losses.
  • Optimal normalization choices for cross-recording contrastive learning resemble those for supervised tasks, suggesting a shared sensitivity to cross-subject consistency.
  • As EEG foundation-model training grows, normalization choices should be reported and treated as a hyperparameter tied to the learning objective.

Reading between the lines

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

  • Inference beyond the paper: because the self-supervised comparison is scored only by the Contrastive Predictive Coding pretext loss, the recommended minimal or cross-channel strategy may not survive downstream fine-tuning; a linear probe or transfer evaluation could reverse the ranking.
  • Inference beyond the paper: the NaN failure mode suggests the model's internal scale consistency is broken by mixing normalization scopes; checking gradient norms or activation statistics in the early layers would test this mechanism directly.
  • Inference beyond the paper: the same taxonomy could be applied to other self-supervised objectives such as SimCLR or masked autoencoding, where within-channel window-level scaling might behave differently than in Contrastive Predictive Coding.
  • Inference beyond the paper: the 20-second versus 2-second window difference between same-recording contrastive learning and the other tasks is a confound; varying window length within a single task would clarify whether normalization sensitivity is driven by task structure or by window length.
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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

3 major / 7 minor

Summary. This paper reports a systematic empirical comparison of normalization strategies for EEG deep learning, varying granularity (recording vs. window level) and scope (cross-channel vs. within-channel), applied to two supervised tasks (age regression and gender classification) and two self-supervised Contrastive Predictive Coding (CPC) variants, all on the Healthy Brain Network dataset. The authors find that window-level within-channel normalization yields the best supervised performance, whereas window-level cross-channel or no normalization is best for same-recording CPC, and they conclude that optimal normalization is task-specific and that no universal strategy generalizes across supervised and self-supervised settings.

Significance. If the central claim holds, the paper would provide practical guidance for the rapidly growing area of EEG deep learning and foundation-model pretraining, where normalization choices are often made by default. The study has notable strengths: it uses a large dataset (over 2,500 training recordings), evaluates a systematic 3-by-3 factorial design, runs five seeds per condition, and makes the code publicly available. The results are, however, not yet convincing as stated because the main self-supervised result is confounded with window size and the evaluation protocol appears to select the best test-set value, which can bias the comparisons. The work is therefore valuable as a starting point, but the central claim requires additional controlled experiments and a more rigorous evaluation procedure.

major comments (3)
  1. [Section II, 'Self-supervised task' and Section IV, 'Window size'] The central claim that supervised and self-supervised tasks favor different normalization strategies relies primarily on the same-recording CPC experiment in Table 1, but that experiment uses 20-second windows, whereas the supervised tasks and the different-recording CPC experiment use 2-second windows. Window size is thus varied together with the learning paradigm, so the observed difference cannot be attributed to self-supervision per se. The paper acknowledges this confound in Section IV but does not control for it. Since Table 2 (different-recording CPC, 2-s windows) shows no significant normalization effect and point estimates that favor window-level within-channel normalization, the claimed paradigm dependence is not established. Please add a controlled comparison, such as a same-recording CPC variant with 2-second windows or a supervised task with 20-second windows, or explicitly reframe the conclusion in terms of window size and task structure rather than supervised versus self-supervised learning.
  2. [Section II, 'Evaluation metrics' and 'Experiment design'] The paper states that 'we report the best error/accuracy/loss value assessed on the test set' while also stating that 'we reported the means and standard deviations of the appropriate evaluation metrics across seeds.' If the best value is selected by evaluating multiple seeds or multiple epochs on the test set, the reported numbers are optimistically biased and the comparisons are invalid. No validation set was sampled, and the rationale given is that no hyperparameter search was performed, but selecting the best test-set value constitutes a form of model selection. Please clarify the exact selection procedure: whether the reported mean is over seeds of the best test value, the best seed, or the best epoch, and use a validation set or a pre-specified rule (e.g., selecting the epoch by training loss) before evaluating on the test set.
  3. [Results, Tables 1-4 and Abstract] The abstract claims that optimal normalization strategies 'differ significantly between training paradigms,' but no statistical significance testing is reported. Several key comparisons show overlapping standard deviations; for example, in Table 2 the None-Channel condition (2.91 ± 0.19) and the Channel-Channel condition (2.98 ± 0.11) are within one standard deviation, and in Table 1 the None-All condition (0.65 ± 0.183) has a large spread. To support the strength of the claims, please provide paired significance tests (e.g., permutation or bootstrap tests over subjects or seeds) or confidence intervals, and soften the language if the differences are not statistically significant.
minor comments (7)
  1. [Section II, 'Data splitting'] The paper reports 2,836 participants in the dataset, but the training and test sets sum to 2,567 + 134 = 2,701 recordings; please clarify whether 135 recordings were excluded and why, or correct the participant count.
  2. [Section II, 'Preprocessing'] After removing the 0-value Cz reference channel, the input dimension should be 127 × 500 rather than 128 × 500; please correct this inconsistency.
  3. [Table 3] The value '1e+9' in the None-All cell is unexplained; if it indicates a diverged run, please state this in the caption or replace it with a notation such as 'NaN' or 'diverged.'
  4. [Section II, 'Supervised tasks'] For gender classification, the text says 'we produced a subset of the dataset to contain a balanced male/female distribution' but does not specify the number of subjects or the balancing procedure; please provide these details.
  5. [Tables 1-4, captions] The captions do not state whether the reported values are the mean across seeds of the best test value or the best seed; please make the evaluation metric and error-bar definition explicit in each caption.
  6. [References] Reference [30] is cited for Adamax but appears to be the original Adam paper; please cite the specific source for the Adamax optimizer or update the reference.
  7. [Section IV, 'Window size'] The speculation that 'larger windows might lead to higher chances of containing extremely noisy EEG signals' is not tested and is presented without supporting evidence; please label it as speculation or provide supporting analysis.

Circularity Check

0 steps flagged · score 0.0 of 10

No circularity: the conclusions rest on held-out empirical comparisons, and self-citations appear only as implementation and prior-benchmark scaffolding.

full rationale

The paper's central claim—that supervised and self-supervised EEG tasks favor different normalization strategies—is an empirical finding, not a derivation. Normalization strategies are defined independently of the outcome metrics (CPC loss, age MAE, gender balanced accuracy), and none of the reported numbers are produced by fitting a parameter and then renaming the fit as a prediction. The evaluation uses held-out test releases (release 6 for test, rest for training), so the comparisons are not forced by construction. Self-citations to the authors' EEG-SSL framework [27], prior EEG predictability work [2], and the 'EEG is better left alone' preprocessing argument [22] are used as implementation scaffolding or motivation, but they do not carry the conclusion: the ranking of normalization strategies is determined by the reported tables, not by any cited theorem or prior claim. The paper itself flags the two main limitations: same-recording CPC used 20-s windows while other tasks used 2-s windows (Section IV, 'Window size'), and CPC loss 'does not fully capture the downstream utility of the learned representations' (Section IV, 'Self-supervised learning choice'). These are threats to generalizability and construct validity, not circular reasoning. There is no equation, definition, or self-citation chain that makes the result equivalent to its inputs. Accordingly, the appropriate circularity score is 0.

Assumptions & free parameters 5 free parameters · 4 assumptions · 0 invented entities

The paper introduces no invented entities and fits no constants. It relies on fixed hyperparameters and four domain assumptions: that artifact removal is unnecessary for the comparison, that CPC loss measures SSL quality, that the chosen architectures represent EEG deep learning, and that the release-based split is a valid generalization test.

free parameters (5)
  • Normalization statistic choice: robust median and IQR = median and interquartile range
    Chosen to handle outliers; the comparison only tests granularity and scope under this scaling function, so conclusions may be specific to robust scaling.
  • CPC mask rate, mask span, and number of distractors = 0.1, 1, 20
    Copied from prior work [17] without tuning; these control the difficulty of the pretext task and could interact with normalization schemes.
  • Training epochs = 5 for supervised, 10 for SSL
    Set by visual inspection of training loss, not by validation; convergence rates may differ across normalization conditions.
  • Window sizes = 2 s for supervised and different-recording CPC, 20 s for same-recording CPC
    The 20 s versus 2 s difference is a confound acknowledged in the Discussion, making same-recording CPC not directly comparable to the other tasks.
  • Learning rate and batch size = 0.002, 64 (supervised) / 128 (CPC)
    Fixed without tuning; different normalizations can shift optimal hyperparameters, which may affect the ranking.
assumptions (4)
  • domain assumption Advanced artifact removal is unnecessary for a valid comparison of normalization strategies.
    The authors exclude ICA and clean_rawdata, citing prior work that cleaning has limited effect on deep learning outcomes; if artifact cleaning interacts with normalization, the ranking may not transfer.
  • domain assumption CPC pre-training loss measures self-supervised representation quality.
    The SSL comparison uses only CPC loss; the authors acknowledge in Section IV that downstream utility is not measured.
  • domain assumption Deep4Net with an LSTM contextualizer is representative of EEG deep learning architectures.
    The Discussion notes Transformers differ in normalization sensitivity, so conclusions may be architecture-dependent.
  • domain assumption The release-based train/test split provides a valid generalization test.
    Subjects do not overlap across releases, but the test split is a single release with 134 recordings and is not random; no validation set is used.

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Pith. "Pith review of Data Normalization Strategies for EEG Deep Learning." pith.science (2026). https://pith.science/paper/EZRDHGWT

@misc{pith2026250622455,
  author       = {Pith},
  title        = {Pith review of: Data Normalization Strategies for EEG Deep Learning},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/EZRDHGWT}},
  note         = {Machine review of arXiv:2506.22455}
}
read the original abstract

Normalization is a critical yet often overlooked component in the preprocessing pipeline for EEG deep learning applications. The rise of large-scale pretraining paradigms such as self-supervised learning (SSL) introduces a new set of tasks whose nature is substantially different from supervised training common in EEG deep learning applications. This raises new questions about optimal normalization strategies for the applicable task. In this study, we systematically evaluate the impact of normalization granularity (recording vs. window level) and scope (cross-channel vs. within-channel) on both supervised (age and gender prediction) and self-supervised (Contrastive Predictive Coding) tasks. Using high-density resting-state EEG from 2,836 subjects in the Healthy Brain Network dataset, we show that optimal normalization strategies differ significantly between training paradigms. Window-level within-channel normalization yields the best performance in supervised tasks, while minimal or cross-channel normalization at the window level is more effective for SSL. These results underscore the necessity of task-specific normalization choices and challenge the assumption that a universal normalization strategy can generalize across learning settings. Our findings provide practical insights for developing robust EEG deep learning pipelines as the field shifts toward large-scale, foundation model training.

Figures

Figures reproduced from arXiv: 2506.22455 by the authors.

Figure 1
Figure 1. Illustration of normalization strategy taxonomies evaluated in the study. (A) Recording-level vs. window-level normalization: normalization statistics are computed either across the full EEG recording (global temporal context) or within each temporal window (local context). (B) All-channel vs. channel-level normalization: normalization statistics are computed across all channels jointly (preserving spatial scale rel… view at source ↗

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