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The more, the better? Evaluating the role of EEG preprocessing for deep learning applications

T0 review · 3 major / 3 minor · reviewed 2026-08-12 · deepseek-v4-flash

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Pith's one-line read The paper claims that a minimal, filter-only EEG preprocessing pipeline outperforms both raw data and heavier artifact-removal pipelines on average across six tasks and four deep learning architectures.

desk verdict Useful EEG-DL preprocessing benchmark with open code and carefully chosen subject-level splits, but the shared learning rate across pipelines and weak inter-task significance make the 'minimal preprocessing wins' claim a trend rather than a proven rule. read the letter →

arxiv 2411.18392 v1 pith:QLPFBYJ4 submitted 2024-11-27 eess.SP

Federico Del Pup , Andrea Zanola , Louis Fabrice Tshimanga , Alessandra Bertoldo , Manfredo Atzori This is my paper · ORCID
classification eess.SP
keywords EEGdeeplearningpreprocessingpipelinesartifactremovalbalancedaccuracysubject-levelcross-validationrawminimalfiltering
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 deep learning on EEG benefits from heavy preprocessing and answers with a qualified no. Across six classification tasks (eye state, motor imagery, Parkinson's, Alzheimer's, sleep deprivation, and first-episode psychosis), four common neural architectures, and 4,800 subject-independent trainings, raw data consistently finished last in average ranking, while a minimal pipeline that only filters and normalises the signal finished first on average for every architecture. Richer pipelines that add automatic artifact removal, such as independent-component rejection with and without artifact subspace reconstruction, did not systematically beat the simple filter. The authors read this as evidence that EEG artifacts are not pure noise for deep networks and may carry task-relevant information, and they propose minimal preprocessing as a default guideline while noting that inter-task significance appeared only for the deepest model tested.

What carries the argument

The comparison device is a ranked statistical evaluation of four preprocessing pipelines treated as interventions: Raw (no preprocessing beyond channel removal and resampling), Filt (band-pass filtering, re-referencing, and normalisation), ICA (Filt plus independent-component analysis with automatic component rejection), and ICA+ASR (ICA plus artifact subspace reconstruction and bad-channel correction). Performance is measured with a Nested Leave-N-Subject-Out cross-validation, which splits subjects rather than individual windows and yields an unbiased distribution of balanced-accuracy scores for each pipeline on each task. The central identity is the Friedman average rank across the six tasks: the paper's conclusion rests on the consistency with which the minimal pipeline is ranked first and raw data are ranked last, with Nemenyi's critical difference used to visualise which pipelines are statistically separable.

What would settle it

Take a single task, re-tune the learning rate separately for each of the four pipelines on the validation set, and re-run the Nested Leave-N-Subject-Out comparison; if the filter-only pipeline no longer ranks first on average, the minimal-preprocessing advantage is an artefact of the shared hyperparameter rather than a property of the preprocessing itself.

Watch

Extended reading notes

Core claim

On the paper's own terms, the central discovery is a consistent ordering of EEG preprocessing strategies for deep learning: raw data underperform, a minimal filter-only pipeline performs best on average, and adding artifact-handling steps does not reliably help. Across all four analysed architectures, the minimal pipeline ranked first in average Friedman rank (average ranks between 1.17 and 2.00), and raw data ranked last in every case (average ranks between 2.83 and 3.33). The inter-task Friedman test reached statistical significance only for the largest architecture, DeepConvNet ($\chi^2_F = 9.0$, $p = 0.029$); the other architectures showed the same ranking without reaching significance. The authors interpret this trend as evidence that artifacts may carry discriminative information for deep networks, so aggressively removing them can be counterproductive.

Load-bearing premise

The learning rate for each task-and-model pair is tuned once on the validation set and then used for all four pipelines, so if different preprocessing levels need different learning rates to perform at their best, the pipeline ranking could be an artefact of the shared hyperparameter rather than a true property of the preprocessing.

Editorial extensions

If this is right

  • Researchers can expect raw EEG to underperform even modest filtering when training deep networks on new subjects, since the raw pipeline ranked last on average for every architecture in this design.
  • For the six tasks studied, automatic artifact-handling pipelines do not systematically improve balanced accuracy over simple filtering, so the extra computation, expert supervision, and risk of discarding signal may not be worthwhile unless a specific task shows a gain.
  • The paper's guidance is that minimal preprocessing, roughly a 1–45 Hz band-pass filter plus channel-wise z-score normalisation, is a reasonable default for EEG deep learning, with artifact removal reserved for cases where task-specific evaluation justifies it.
  • The authors expect that increasing the number of tasks beyond six would shrink the critical difference and make the 'minimal filter first' ordering statistically significant for the other architectures as well.

Reading between the lines

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

  • The learning rate for each task-and-model pair was selected once and shared across all four pipelines; if the optimal learning rate differs by pipeline, the ranking could reflect a hyperparameter mismatch rather than a genuine preprocessing advantage, so a per-pipeline learning-rate search is the most direct test of the paper's conclusion.
  • If artifacts genuinely help deep networks, the paper's trend implies that artifact-bearing or artifact-injected training data could act as a form of augmentation, a testable extension the authors do not pursue.
  • For clinical tasks such as Parkinson's and Alzheimer's classification, the results make it plausible that models are using artifact-related differences between patient and control groups rather than purely neural signals, which would warrant saliency or out-of-distribution audits before clinical use.
  • The paper's lack of inter-task significance for three of four architectures suggests the main barrier is statistical power; a larger multi-task benchmark with per-pipeline hyperparameter tuning would settle whether the ordering is universal.
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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 / 3 minor

Summary. The paper presents an empirical benchmark of four EEG preprocessing pipelines (Raw, Filt, ICA, ICA+ASR) across six classification tasks and four deep learning architectures, totaling 4800 training runs. Using a nested leave-N-subject-out cross-validation scheme, the authors measure balanced accuracy and analyze pipeline differences with pairwise Wilcoxon tests and Friedman/Nemenyi tests. The central claim is that minimal filtering without artifact handling ranks first on average, while raw data ranks last, and that richer artifact-removal pipelines do not consistently help deep learning models.

Significance. If the central claim holds, the paper would provide useful practical guidance for the EEG deep learning community, where preprocessing choices are often made by habit rather than evidence. The study has notable strengths: subject-level splitting, multiple architectures and tasks, balanced accuracy, Holm-corrected pairwise comparisons, a public code repository, and a reproducible seeding procedure. The authors also transparently report that inter-task significance is reached only for DeepConvNet, and they discuss low statistical power. However, the comparison is compromised by a shared learning rate across pipelines and by a repeated-measures Wilcoxon analysis that treats nested CV folds as independent; these issues affect the strength of the central comparative claim.

major comments (3)
  1. [II-C3, Table III] The learning rate is chosen once per (task, model) pair and kept equal across all four pipelines. Because preprocessing changes the spectral content, artifact composition, and effective input distribution of the data, the optimal Adam step size is not expected to be invariant across Raw, Filt, ICA, and ICA+ASR, even after per-channel z-score normalization. If the shared learning rate happens to align best with Filt, the observed ranking may reflect learning-rate compatibility rather than preprocessing superiority. The paper does not report per-pipeline learning rate tuning or any sensitivity analysis. This is the main threat to the conclusion that minimal preprocessing is intrinsically better, and it should be addressed either by tuning learning rates per pipeline or by demonstrating that the ranking is stable under plausible per-pipeline learning rates.
  2. [II-D, Figure 2 Panels A-D (I)] The Wilcoxon signed-rank tests compare 50 models per task, but these observations are not independent: for each outer fold, the same test subjects are reused across the five inner folds, creating clustering by outer fold. Treating the 50 models as independent repeats likely inflates significance levels, undermining the intra-task significance claims that appear in the abstract and in Section III. The manuscript cites Dietterich's warning about k-fold t-tests but does not apply the same logic to the Wilcoxon tests. A more appropriate analysis would average the five inner-fold results within each outer fold (giving 10 paired observations per task) or use a cluster-robust / mixed-effects approach that accounts for the nested structure.
  3. [IV, V] The central conclusion that 'a minimal preprocessing without artifact handling is superior' is based on average ranks over only six tasks, and the Friedman/Nemenyi inter-task analysis is significant only for DeepConvNet (chi2_F = 9.0, p = 0.029). The authors acknowledge the low power of the Friedman test, but the general statement in the conclusion goes beyond what the statistical evidence supports. I recommend either softening the conclusion to a descriptive trend, or providing additional evidence such as task-level effect sizes, confidence intervals for average ranks, or a sensitivity analysis that increases the number of task-level replicates (e.g., split tasks into multiple dataset blocks) to make the inter-task claim statistically testable.
minor comments (3)
  1. [II-C3] The text states that learning rates were searched on a discrete grid of 13 values, but only 9 values are listed, and the listed order is not monotonic (1.0e-5 appears between 2.5e-4 and 7.5e-5). Please correct the grid and the count.
  2. [II-C3] The learning rate selection criterion ('evaluating the performance of a subset of models on the validation set in terms of consistency') is vague. Please specify which subset of models was used and how median and rank consistency were combined into a final choice.
  3. [II-D and throughout] There are several typos in the statistical terminology, including 'Friedmann' for Friedman and 'Mann-Whiteny' for Mann-Whitney. Please correct these for consistency.

Circularity Check

0 steps flagged · score 0.0 of 10

No significant circularity: the paper's central comparison is an empirical benchmark whose conclusions are measured outcomes, not constructions from fitted inputs or self-cited premises.

full rationale

The paper's central claim is that the Filt pipeline has the best average rank across tasks and models. This claim is obtained from balanced accuracies measured on test sets under a nested leave-N-subject-out protocol, not from any equation that defines the Filt outcome in terms of its inputs. The learning rate is selected per (task, model) pair and shared across pipelines, which is a possible confound for the comparison, but it is not a case of fitted-input-called-prediction: the paper does not fit a parameter to the pipeline-ranking outcome and then report that outcome as a prediction. No such reduction is exhibited. The self-citations (BIDSAlign, SelfEEG) are tooling and library references used for preprocessing and model training; they are not invoked as proof of the empirical result, and no uniqueness theorem or ansatz is imported from them. The manuscript also transparently reports that the inter-task Friedman test is significant only for DeepConvNet, which is a statistical-power limitation rather than a circularity. Therefore, no circular step can be identified, and the appropriate finding is no significant circularity with score 0.

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

The paper introduces no new physical or theoretical entities. Its free parameters are standard hyperparameters and preprocessing choices, not fitted to force the conclusion. The key assumptions are the representativeness of the six tasks, the validity of ICLabel and ASR as artifact handling methods, and the suitability of a shared learning rate across pipelines.

free parameters (5)
  • learning rate per (task, model) = Table III (e.g., EEGNet Eye: 5.0e-4; DeepConvNet Parkinson: 2.5e-4)
    Selected by grid search on the validation set for each task-model pair, then fixed across pipelines. This is a fitted hyperparameter that affects absolute performance and could interact with pipeline ranking.
  • filter band for Filt/ICA/ICA+ASR = 1-45 Hz
    Chosen by hand as a common EEG preprocessing choice; not fitted to the target result but defines the 'minimal filtering' pipeline.
  • ICLabel rejection thresholds = brain class 0-0.1, artifact classes 0.9-1
    Chosen by hand as a trade-off; affects how many components are removed in ICA and ICA+ASR pipelines.
  • ASR default parameters = defaults in EEGLAB clean_rawdata
    Used without tuning; determines the behavior of the ICA+ASR pipeline.
  • resampling rate = 250 Hz (160 Hz for MMI)
    Chosen to standardize inputs; affects the temporal resolution available to models.
assumptions (5)
  • domain assumption The six selected tasks are representative of the broader space of EEG-DL applications.
    The paper relies on these six tasks to draw general conclusions about preprocessing effects across EEG domains. Results could differ for other tasks not covered.
  • domain assumption The ICLabel classifier correctly identifies artifact independent components.
    Automatic component rejection in the ICA pipeline depends on the accuracy of ICLabel, a pre-trained classifier. If ICLabel misclassifies brain components as artifacts, the ICA pipelines could discard informative signal.
  • domain assumption The Nested Leave-N-Subject-Out cross-validation provides an unbiased estimate of model performance on unseen subjects.
    The authors propose N-LNSO as an unbiased scheme; the claim that the measured performance distribution reflects true generalization relies on this method being valid. They provide a comparison against sample-level splitting, but no formal proof.
  • domain assumption The same learning rate is suitable for all four pipelines for a given task and model.
    The learning rate is tuned once per task-model pair and applied to all pipelines. If pipelines have different optimal learning rates, the comparison may be biased.
  • domain assumption Balanced accuracy is the appropriate metric for comparing classification performance across imbalanced medical datasets.
    The central comparisons are based on balanced accuracy. Other metrics (F1, precision, recall, kappa) are reported in the supplement and mostly agree, but the main conclusions are anchored to this metric.

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Cite this review

Pith. "Pith review of The more, the better? Evaluating the role of EEG preprocessing for deep learning applications." pith.science (2026). https://pith.science/paper/QLPFBYJ4

@misc{pith2026241118392,
  author       = {Pith},
  title        = {Pith review of: The more, the better? Evaluating the role of EEG preprocessing for deep learning applications},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/QLPFBYJ4}},
  note         = {Machine review of arXiv:2411.18392}
}
read the original abstract

The last decade has witnessed a notable surge in deep learning applications for the analysis of electroencephalography (EEG) data, thanks to its demonstrated superiority over conventional statistical techniques. However, even deep learning models can underperform if trained with bad processed data. While preprocessing is essential to the analysis of EEG data, there is a need of research examining its precise impact on model performance. This causes uncertainty about whether and to what extent EEG data should be preprocessed in a deep learning scenario. This study aims at investigating the role of EEG preprocessing in deep learning applications, drafting guidelines for future research. It evaluates the impact of different levels of preprocessing, from raw and minimally filtered data to complex pipelines with automated artifact removal algorithms. Six classification tasks (eye blinking, motor imagery, Parkinson's and Alzheimer's disease, sleep deprivation, and first episode psychosis) and four different architectures commonly used in the EEG domain were considered for the evaluation. The analysis of 4800 different trainings revealed statistical differences between the preprocessing pipelines at the intra-task level, for each of the investigated models, and at the inter-task level, for the largest one. Raw data generally leads to underperforming models, always ranking last in averaged score. In addition, models seem to benefit more from minimal pipelines without artifact handling methods, suggesting that EEG artifacts may contribute to the performance of deep neural networks.

Figures

Figures reproduced from arXiv: 2411.18392 by the authors.

Figure 1
Figure 1. Schematization of the Nested Leave-N-Subject-Out Cross Validation. Each outer fold is used to determine the subjects to use as test set. Then, the remaining subjects are partitioned multiple times in training and validation sets based on the decided number of inner folds. A model is trained for each of the inner folds and its performance is evaluated on the test set of the corresponding outer fold. The procedure is … view at source ↗
Figure 2
Figure 2. Results are reported in four panels, one for each deep [PITH_FULL_IMAGE:figures/full_fig_p006_2.png] view at source ↗
Figure 2
Figure 2. Panels A to D (I) shows the balanced accuracies for the 6 tasks and for the 4 pipelines investigated. Results are marginalized by deep learning models which are: in Panel A EEGNet, in Panel B ShallowNet, in Panel C DeepConvNet and in Panel D FBCnet. Asterisks indicate significant results from Wilcoxon’s signed rank tests, performed within the same task: (∗∗∗∗) p < 0.0001; (∗∗∗) p < 0.001; (∗∗) p < 0.01 and (∗) p < 0… view at source ↗
Figures from the paper (3 more)
Figure 3
Figure 3. Figure 3: Best performing pipeline; results are marginalized by model. The pie-charts report the number of times (in %) a pipeline is better than the others, over 300 results (6 tasks × 50 folds). C. DeepConvNet [PITH_FULL_IMAGE:figures/full_fig_p008_3.png]
Figure 4
Figure 4. Figure 4: Comparison of results between a subject level splitting strategy and a sample level one. Subject split results refer to those achieved with the best configuration (model + pipeline) when using the Nested Leave￾N-Subject-Out method. Sample split results refer to those a…
Figure 5
Figure 5. Figure 5: Panels A to F shows the balanced accuracies for the 4 models and for the 4 pipelines investigated. Results are marginalized by tasks, which are: in Panel A, Eye, in Panel B MMI, in Panel C Parkinson, in Panel D Alzheimer, in Panel E Sleep and in Panel F FEP. Asterisks …

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Pith tools

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