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Under review as a conference paper at ICLR 2027

Discern, Then Combine: Probe-Guided Multi-Dataset Fine-Tuning for EEG Foundation Models

Abstract

Electroencephalography (EEG) foundation models pretrained on large-scale heterogeneous corpora provide general-purpose representations, yet the standard practice of fine-tuning them on a single target dataset, while direct and widely used, has proven suboptimal in many settings. While incorporating auxiliary datasets can provide effective multi-domain regularization, indiscriminate data mixing frequently induces negative transfer due to incompatible characteristics. Crucially, dataset compatibility in EEG is highly counter-intuitive and cannot be reliably predicted from surface-level task labels or metadata. We propose POSE, a data-centric, target-conditioned framework for multi-dataset EEG fine-tuning. POSE uses early target-only adaptation as a dynamic probe, combining endpoint discrepancies and temporal trends to select and weight auxiliary datasets. A phased training schedule then regulates auxiliary participation to balance joint learning with target-focused refinement. Comprehensive experiments show that POSE achieves higher average performance than all evaluated baselines and improves over target-only fine-tuning on most targets, while maintaining stable and robust performance across heterogeneous settings. Beyond performance improvements, our selection analyses and case studies provide empirical guidance for deciding when and how to incorporate auxiliary data for a given target and backbone. More broadly, this work advances a compatibility-aware perspective on EEG foundation-model adaptation, encouraging further exploration of how heterogeneous datasets can complement one another in target-specific learning.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG foundation model, multi-dataset fine-tuning, dataset selection

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_vKqSOpenReview ↗
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3(+1)
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3
Informativeness
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2
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Paper summary

This paper proposes POSE, a target-conditioned framework for multi-dataset fine-tuning of EEG foundation models. To mitigate negative transfer from heterogeneous auxiliary datasets, POSE first performs early target-only adaptation and measures the evolving feature-distribution discrepancies between the target and candidate datasets. Experiments across 12 EEG datasets and two foundation models (LaBraM and CBraMod), with supplementary evaluations on REVE, demonstrate improvements over target-only fine-tuning and several multi-dataset training baselines.

Critical strengths
  • The observed backbone-dependent and cross-paradigm selection patterns could motivate further research on data-centric adaptation of EEG foundation models.

  • POSE provides a practical data-selection strategy without modifying the pretrained backbone or inference architecture.

Critical weaknesses
  • A central novelty of POSE is combining endpoint discrepancies with their temporal slopes. However, the main ablation compares the full framework against selection from the pretrained checkpoint (No Probe), rather than an endpoint-only selection strategy using the same target-adapted checkpoint.

  • POSE assumes that smaller feature-distribution discrepancies and favorable discrepancy trends indicate more useful auxiliary supervision. However, feature similarity does not necessarily imply compatible learning objectives, particularly across heterogeneous EEG tasks with different label spaces. It would be better to directly quantify how well its compatibility scores predict actual downstream transfer gains.

  • The primary ablation study focuses on eight classification datasets where POSE already outperforms target-only fine-tuning on both backbones. The remaining four datasets are evaluated separately under a fixed exploratory configuration. This ablation protocol may overestimate the benefits of individual components.

  • Although POSE is conceptually backbone-agnostic, all evaluated EEG foundation models are Transformer-based.

Questions for authors

1.Coule the authors evaluate POSE on non-Transformer backbones, such as the structured state-space modeling approach in CodeBrain (ICLR 2026), and alternative pretraining paradigms, such as JEPA-style predictive learning in PATCHCODE (ICML 2026)?

2.Could the authors report downstream performance for endpoint-only selection (β = 1) after the same target-only probing stage, while keeping the auxiliary weighting and training schedule identical?

3.Have the authors investigated the correlation between the proposed compatibility scores and the actual performance gains obtained by adding individual auxiliary datasets?

5 comments
AuthorsOpenReview ↗

Response to Reviewer vKqS (Part 1/3): Endpoint-Only vs. Trajectory-Based Selection [W1, Q2]

We sincerely thank you for the thoughtful review and for recognizing our practical design. Below, we address each of your comments and questions point by point.

W1 & Q2: Downstream Effect of Endpoint-Only Selection (β=1\beta = 1) After Target-Only Probing

A central novelty of POSE is combining endpoint discrepancies with their temporal slopes. However, the main ablation compares the full framework against selection from the pretrained checkpoint (No Probe), rather than an endpoint-only selection strategy using the same target-adapted checkpoint. ... Could the authors report downstream performance for endpoint-only selection (β=1\beta = 1) after the same target-only probing stage, while keeping the auxiliary weighting and training schedule identical?

Combining endpoint discrepancy with its temporal slope (β=0.7\beta = 0.7) consistently improves downstream performance over endpoint-only selection (β=1\beta = 1) in the exact same target-adapted space. For this experiment and the new evaluations in W2 and W4 below, we adopt a subject-level balanced 5-fold cross-validation protocol across six representative benchmarks spanning motor imagery, emotion recognition, and SSVEP (HGD, MAMEM1, SEED-V, BCIC-IV-2a, SEED, and SEED-IV). Target subjects are shuffled into 5 balanced test groups so every subject is tested once across the 5 folds, with the next 2 subjects in circular order used for validation and the remaining subjects for training (strictly disjoint subjects across splits, 3 random seeds 42 to 44 averaged per fold, reporting 5-fold mean ±\pm sample standard deviation in % across identical splits). Evaluating β∈{0,0.7,1}\beta \in \{0, 0.7, 1\} after the identical 4-epoch target-only probe while keeping the inverse-score weighting, phased training schedule, and hyperparameters fixed yields the following results (best per backbone and column in bold):

ModelVariantHGDMAMEM1SEED-VBCIC-IV-2aSEEDSEED-IVAverage
LaBraMTrend-only (β=0\beta = 0)71.21 ±\pm 6.1447.08 ±\pm 9.3122.90 ±\pm 2.3942.08 ±\pm 5.0753.29 ±\pm 5.8534.66 ±\pm 3.0245.20
LaBraMEndpoint-only (β=1\beta = 1)73.17 ±\pm 3.8649.04 ±\pm 12.3224.20 ±\pm 1.7642.95 ±\pm 4.3153.51 ±\pm 5.5235.81 ±\pm 2.0746.45
LaBraMPOSE (β=0.7\beta = 0.7)73.92 ±\pm 4.0752.43 ±\pm 11.5624.29 ±\pm 2.2243.78 ±\pm 6.3656.34 ±\pm 5.0835.79 ±\pm 2.2547.76
CBraModTrend-only (β=0\beta = 0)68.89 ±\pm 5.4941.85 ±\pm 7.1521.98 ±\pm 1.2348.16 ±\pm 3.9253.26 ±\pm 2.6533.04 ±\pm 3.8644.53
CBraModEndpoint-only (β=1\beta = 1)69.21 ±\pm 5.0041.73 ±\pm 8.4523.56 ±\pm 1.6948.44 ±\pm 3.7653.79 ±\pm 1.9333.01 ±\pm 3.6144.96
CBraModPOSE (β=0.7\beta = 0.7)69.95 ±\pm 4.8546.72 ±\pm 9.7123.48 ±\pm 3.2150.83 ±\pm 1.3655.99 ±\pm 3.8434.15 ±\pm 3.4346.86

Across the evaluated backbones and tasks, POSE consistently outperforms both endpoint-only and trend-only selection. Relative to endpoint-only selection (β=1\beta = 1), incorporating the temporal slope raises average balanced accuracy by +1.31% on LaBraM and +1.90% on CBraMod, achieving clear gains on nearly all datasets (most notably on MAMEM1, SEED, and BCIC-IV-2a) while remaining virtually tied on the remaining two pairs. Conversely, relying on slope alone without an endpoint proximity anchor (β=0\beta = 0) degrades accuracy across every dataset on both backbones, confirming that post-probe proximity and adaptation trend provide complementary signals. We will include this controlled ablation in the revised manuscript.

AuthorsOpenReview ↗

Response to Reviewer vKqS (Part 2/3): Single-Source Gain Analysis & Ablation Protocol [W2, W3, Q3]

W2 & Q3: Compatibility Scores Versus Single-Source Transfer Gains

... feature similarity does not necessarily imply compatible learning objectives, particularly across heterogeneous EEG tasks with different label spaces. ... Have the authors investigated the correlation between the proposed compatibility scores and the actual performance gains obtained by adding individual auxiliary datasets?

We agree that feature proximity does not guarantee identical task objectives across different label spaces, which is why POSE uses trajectory scores for top-end selection and tail-risk filtering in multi-source adaptation rather than as an exact linear predictor of every isolated source. When label spaces differ, mid-scoring datasets can still contribute generic backbone regularization and sources interact during joint training, so global rank correlation across all 11 single-auxiliary runs is naturally moderate. Evaluating all 11 single-source additions individually under the balanced 5-fold protocol on LaBraM (MAMEM1 and SEED against a matched Target-only control) shows a positive overall rank trend (mean-score vs. mean-gain Spearman ρ=0.10\rho = 0.10 to 0.210.21, and fold-averaged ρˉ=0.27\bar{\rho} = 0.27 on MAMEM1) while confirming the properties POSE actually relies on. Top-ranked candidates provide reliable positive supervision (e.g., rank-1 SEED-IV on SEED and rank-2 PhysioNet-MI with the highest single-source gain of +3.90% on MAMEM1), whereas bottom-ranked candidates capture negative transfer (e.g., worst-scored SHU-MI at -0.39% on MAMEM1 and rank-10 MAMEM1 at -0.86% on SEED). Combined with the consistent drops observed when replacing POSE's score with No Probe, Uniform Weight, or alternative selectors across our ablations and baselines, these results confirm that the compatibility score provides an effective signal for reliable multi-source adaptation.

W3: Ablation Protocol and Potential Overestimation of Component Benefits

The primary ablation study focuses on eight classification datasets where POSE already outperforms target-only fine-tuning on both backbones. The remaining four datasets are evaluated separately under a fixed exploratory configuration. This ablation protocol may overestimate the benefits of individual components.

Separating the two dataset groups was intended to make individual component contributions observable where multi-dataset adaptation is active. Because the primary purpose of an ablation study is to isolate the effect of each component, on targets where auxiliary training as a whole leaves little room for gain over Target-only (e.g., already saturated performance on TUAB), all variants cluster tightly and component-level differences cannot be meaningfully distinguished.

The remaining four datasets are not simply failure cases of POSE, and the fixed configuration in Table 9 ensures a fair comparison with active auxiliary participation. Specifically, CCD is reported separately because it is a regression task evaluated by NRMSE rather than balanced accuracy (where POSE improves over Target-only on both backbones), while targets such as HGD and TUEV also show gains on LaBraM or in the 3-fold evaluation (Table 7). On less responsive targets, strict validation thresholding can select an empty auxiliary set (S=∅\mathcal{S} = \emptyset), causing weighting and scheduling variants to collapse into identical target-only runs. Using a fixed setting (τ=0.3,λmax⁡=1.0\tau = 0.3, \lambda_{\max} = 1.0) in Table 9 keeps auxiliary participation active for convenient observation, and POSE uses the exact same untuned configuration so the comparison is strictly fair.

Existing results in Tables 8 and 9 confirm that component benefits and their relative ordering hold across the full benchmark. On the four separated datasets in Table 9 alone, POSE still outperforms No Probe on 7 of 8 backbone and dataset pairs, outperforms or ties No Ramp on 7 of 8 pairs, and outperforms or ties Uniform Weight on 6 of 8 pairs, while matching or beating every variant on CCD. Furthermore, when combining Tables 8 and 9 across all 11 classification targets, the average gains of POSE decrease by at most 0.5% compared with the 8-dataset subset, remaining clear and consistent across both LaBraM and CBraMod (+2.32% and +1.95% over No Probe, +1.64% and +1.32% over Uniform Weight, and +1.81% to +2.09% over schedule ablations).

AuthorsOpenReview ↗

Response to Reviewer vKqS (Part 3/3): Non-Transformer Backbone (CodeBrain) & Pretraining Paradigms [W4, Q1]

W4 & Q1: Generalization Beyond Transformers on CodeBrain (SSM) and Diverse Pretraining Paradigms

Although POSE is conceptually backbone-agnostic, all evaluated EEG foundation models are Transformer-based. ... Could the authors evaluate POSE on non-Transformer backbones, such as the structured state-space modeling approach in CodeBrain (ICLR 2026), and alternative pretraining paradigms, such as JEPA-style predictive learning in PATCHCODE (ICML 2026)?

Evaluating POSE on the official non-Transformer CodeBrain backbone (ICLR 2026) under the balanced 5-fold protocol confirms that its benefits extend to structured state-space architectures. CodeBrain replaces self-attention with an 8-layer bidirectional S4 / spectral-convolution state-space encoder pretrained via dual temporal-frequency discrete codebook prediction. Using a common 20-epoch configuration across all six benchmarks (LR=1×10−4\text{LR} = 1 \times 10^{-4}, λmax⁡=1.0\lambda_{\max} = 1.0, τ=0.3\tau = 0.3), we compared Target-only, Meta-select equipped with the identical POSE phased schedule, and POSE (balanced accuracy in %, ±\pm 5-fold standard deviation, with best per column in bold):

ModelVariantHGDMAMEM1SEED-VBCIC-IV-2aSEEDSEED-IVAverage
CodeBrainTarget-only68.85 ±\pm 3.5024.83 ±\pm 2.1323.63 ±\pm 3.0034.27 ±\pm 2.3953.63 ±\pm 5.8032.77 ±\pm 2.0239.66
CodeBrainMeta + POSE schedule67.10 ±\pm 3.4625.39 ±\pm 4.3522.99 ±\pm 1.5733.85 ±\pm 2.2653.15 ±\pm 4.0832.30 ±\pm 2.7239.13
CodeBrainPOSE69.03 ±\pm 4.2027.47 ±\pm 5.8322.90 ±\pm 1.7334.93 ±\pm 3.3454.24 ±\pm 3.9133.18 ±\pm 1.9040.29

Heuristic metadata grouping still induces negative transfer on a state-space backbone, whereas POSE consistently improves target adaptation. Even when given the exact POSE phased schedule, Meta-select falls below Target-only on almost every dataset, whereas POSE achieves the highest overall average (+0.63% over Target-only and +1.16% over Meta + POSE schedule) and improves performance on nearly all evaluated tasks, most notably on MAMEM1. Regarding PATCHCODE, its pretrained model weights are not publicly released, preventing a direct empirical evaluation. Nevertheless, because POSE operates solely on pooled penultimate backbone features during target-only probing without relying on attention maps or specific pretraining heads, it already generalizes across diverse pretraining objectives (neural-tokenizer masked prediction in LaBraM, continuous patch reconstruction in CBraMod, spatial-positional pretraining in REVE, and dual-domain codebook modeling in CodeBrain) and can be directly applied to JEPA-style predictive encoders once weights become available. We will include the CodeBrain evaluation in the revised manuscript.

Thank you again for your valuable suggestions, which have helped us significantly improve our empirical evaluation and manuscript clarity.

Reviewer_tYrdOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes POSE, a probe-guided framework for auxiliary dataset selection in EEG foundation model fine-tuning. It uses early target-only adaptation to measure distribution discrepancies and temporal trends between the target and candidate datasets, followed by compatibility-based weighting and phased auxiliary training. Experiments across 12 EEG datasets and multiple foundation models show improved average performance over the evaluated baselines.

Critical strengths

S1. Important research problem

The paper addresses auxiliary dataset selection for EEG foundation model fine-tuning. Effectively leveraging heterogeneous EEG datasets while mitigating negative transfer is a meaningful research problem.

S2. Extensive experimental evaluation

The evaluation covers diverse EEG datasets, multiple foundation models, and several auxiliary data selection strategies. The paper also includes component ablations and supplementary analyses.

S3. Practical and computationally efficient design

POSE evaluates multiple candidate datasets through a shared target-only probe, without separately training source-specific models or searching over dataset combinations. The framework can be applied to different EEG foundation models without modifying their inference architectures.

Critical weaknesses

W1. Modest and inconsistent performance gains

Although POSE achieves favorable average performance, its improvements are relatively modest. It obtains the best results on 7/12 tasks with LaBraM and 8/12 with CBraMod, while several other tasks show limited gains.

W2. Insufficient connection between distribution similarity and transfer benefits

The probe uses MMD and Fréchet Distance to estimate dataset compatibility, but representation-level distribution similarity does not necessarily indicate beneficial auxiliary supervision. The relationship between the proposed scores and actual downstream transfer gains remains insufficiently established.

W3. Limited validation of short-term probe dynamics

The probe uses only four epochs, all within the five-epoch learning-rate warm-up period. It is unclear whether these early dynamics reliably reflect longer-term trends. Sensitivity to probe duration and checkpoint selection also deserves further investigation.

W4. Insufficient justification of the dataset scoring design

Although the scoring formula and hyperparameter values are provided, the choices of weighting coefficients, Top-K selection, and score aggregation and normalization are not sufficiently justified. More targeted sensitivity analyses would help establish their influence on dataset ranking and downstream performance.

W5. Limited evidence for the contribution of temporal trends

The temporal trend analysis mainly demonstrates changes in auxiliary dataset selection when the slope term is included (Appendix D.9). It does not directly establish whether the slope provides useful information that improves downstream performance over endpoint-only scoring.

W6. Potentially unmatched auxiliary training exposure

Although the methods tune λmax⁡\lambda_{\max} over the same candidate range, POSE uses phased auxiliary sampling, whereas some baselines employ fixed mixing ratios. This may result in different cumulative auxiliary training exposure, making it difficult to isolate the benefits of the selection strategy.

Questions for authors

Q1. Could the authors quantify the relationship between probe scores and observed auxiliary transfer gains, and compare downstream performance with and without the temporal slope term?

Q2. Could the authors report the cumulative auxiliary training exposure for each method under its selected configuration? Would the conclusions remain consistent under matched exposure budgets?

4 comments
AuthorsOpenReview ↗

Response to Reviewer tYrd (Part 1/4): Practical Objective & Probe-Gain Relationship [W1, W2, Q1]

We sincerely thank you for the constructive evaluation and for recognizing the practical importance of our work. Below, we address each of your comments and questions in detail.

W1: Modest and Inconsistent Performance Gains

Although POSE achieves favorable average performance, its improvements are relatively modest. It obtains the best results on 7/12 tasks with LaBraM and 8/12 with CBraMod, while several other tasks show limited gains.

As emphasized in Sections 1 and 4.6, our goal is not to recover a globally optimal auxiliary subset for every task, but to provide a search-free framework that delivers stable and reliable improvements across heterogeneous EEG settings. Cross-dataset EEG transfer interacts closely with task characteristics and backbone inductive biases across an exponentially large combination space, making exhaustive subset search impractical, while already well-constrained benchmarks such as TUAB naturally leave limited room for further gain (Section 4.5). Using only a single target-only probe without combinatorial enumeration, POSE consistently identifies compositions near the 90th percentile of sampled mixtures (Figure 2) and achieves the highest overall performance across backbones.

Empirically, POSE fulfills this objective by improving most targets while avoiding the severe negative transfer seen in competing baselines. In Table 5, competing baselines occasionally peak on isolated tasks only at the cost of sharp drops on incompatible targets (with worst-case single-target drops of 4% to 14% in balanced accuracy below Target-only). In contrast, POSE achieves the best result on 7 of 12 (LaBraM) and 8 of 12 (CBraMod) tasks, delivers substantial gains where auxiliary regularization is needed (e.g., improving MAMEM1 from 0.487 to 0.562 on CBraMod and SEED by ~5% on both backbones), and stays comparable to Target-only elsewhere without ever dropping by more than 0.8% on any dataset. The same reliable pattern holds across the 3-fold evaluation (Table 7) and REVE (Table 6), where POSE improves over Target-only on nearly all evaluated tasks.

W2 & Q1: Relationship Between Probe Scores and Observed Transfer Gains

The probe uses MMD and Fréchet Distance to estimate dataset compatibility, but representation-level distribution similarity does not necessarily indicate beneficial auxiliary supervision. ... Could the authors quantify the relationship between probe scores and observed auxiliary transfer gains ...?

Representation-level trajectory scoring is designed as a coarse compatibility filter and tail-risk guard rather than a strict one-to-one predictor of isolated single-source gains. We fully agree that under mismatched label spaces, representation proximity alone does not establish an exact rank-order equivalence across every individual auxiliary dataset, because mid-ranked sources can still provide generic regularization while auxiliary utility also depends on multi-source interactions. That is precisely why POSE does not rely on static similarity alone, instead measuring how candidates co-adapt during target-specific probing (validated in W5 below) and using thresholded Top-KK weighting to retain compatible anchors while rejecting poorly aligned sources.

Empirical diagnostics at both the single-source and composition levels confirm that this score reliably separates beneficial compositions from harmful ones. In a controlled 5-fold single-source diagnostic on LaBraM (evaluating each of the 11 candidates individually on MAMEM1 and SEED against a matched Target-only control), full-pool rank correlation across all 11 candidates is positive as a coarse trend (mean-score vs. mean-gain Spearman ρ=0.10\rho = 0.10 to 0.210.21, with fold-averaged ρˉ=0.27\bar{\rho} = 0.27 on MAMEM1), while effectively capturing the key operational boundaries: top-scored candidates consistently yield positive transfer (e.g., rank-1 SEED-IV on SEED and rank-2 PhysioNet-MI at +3.90% on MAMEM1), whereas worst-scored outliers induce negative transfer (e.g., bottom-ranked SHU-MI at -0.39% on MAMEM1 and rank-10 MAMEM1 at -0.86% on SEED). Crucially, at the composition level, replacing POSE's score with No Probe, Uniform Weight, Meta-select, or LogME under identical exposure budgets (W6 below) consistently degrades accuracy across all six benchmarks.

AuthorsOpenReview ↗

Response to Reviewer tYrd (Part 2/4): Probe Duration Dynamics & Scoring Design [W3, W4]

W3: Validation of Short-Term Probe Dynamics and Sensitivity to Probe Duration

The probe uses only four epochs, all within the five-epoch learning-rate warm-up period. It is unclear whether these early dynamics reliably reflect longer-term trends. Sensitivity to probe duration and checkpoint selection also deserves further investigation.

Placing the probe within early learning-rate warm-up captures smooth initial target adaptation while leaving most of the training budget for phased joint optimization. Moderate early step sizes steer the backbone smoothly toward target-relevant representations without abrupt parameter shifts (aligning with the local response view in Section 3.2), and Appendix D.9 confirms that candidate rankings already evolve substantially during this window rather than remaining close to the static pretrained space.

Evaluating T1∈{2,4,6}T_1 \in \{2, 4, 6\}, including probing past the warm-up phase, confirms that the default duration achieves the strongest overall performance. Using the original single-fold split protocol from the main paper (Table 4) under a shared controlled configuration and hardware setup across both backbones, we tested one representative dataset from each of three task families: motor imagery (BCIC-IV-2a), emotion recognition (FACED), and SSVEP (MAMEM1):

ModelDatasetT1=2T_1 = 2 (%)T1=4T_1 = 4 (%)T1=6T_1 = 6 (%)
LaBraMBCIC-IV-2a44.4447.2241.67
CBraModBCIC-IV-2a40.6243.0641.32
LaBraMFACED55.1855.4855.32
CBraModFACED54.8955.3955.34
LaBraMMAMEM159.6060.4060.80
CBraModMAMEM150.0049.6049.60
Average50.7951.8650.68

The default T1=4T_1 = 4 achieves the highest average and leads most backbone and dataset pairs, whereas stopping too early (T1=2T_1 = 2) under-adapts the probe and extending probing beyond learning-rate warm-up (T1=6T_1 = 6) shortens subsequent joint refinement without systematic benefit. Across FACED and MAMEM1, performance remains stable across all three probe lengths, showing that POSE does not rely on delicate tuning of the probe duration.

W4: Justification of the Dataset Scoring and Selection Design

Although the scoring formula and hyperparameter values are provided, the choices of weighting coefficients, Top-K selection, and score aggregation and normalization are not sufficiently justified. More targeted sensitivity analyses would help establish their influence on dataset ranking and downstream performance.

Each element of the scoring, filtering, and weighting rule is designed to align heterogeneous discrepancy signals on a common relative scale without introducing metric-specific scaling parameters.

For score normalization and metric aggregation, MMD and Fréchet Distance operate on incompatible numerical scales that vary with feature dimensionality, and raw per-epoch slopes likewise have a different scale from endpoint distances. Applying candidate-wise min-max normalization maps both metrics and both trajectory terms onto a shared [0,1][0, 1] relative interval in a parameter-free manner. Equal averaging combines non-parametric kernel discrepancy (MMD) with first- and second-moment Gaussian discrepancy (FD), and Table 8 confirms that using both metrics jointly outperforms either FD-only or MMD-only on both backbones.

Regarding the Top-KK cap, threshold τ\tau, and inverse-score weighting, restricting ∣S∣≤K=3|S| \le K = 3 prevents target updates from being diluted across too many heterogeneous sources (as observed in Ratio-mixed and Full-mixed), whereas the threshold τ\tau allows POSE to select fewer than KK sources or abstain entirely (S=∅\mathcal{S} = \emptyset) when no candidate is sufficiently compatible. Within S\mathcal{S}, inverse-score weighting prioritizes stronger candidates and consistently outperforms Uniform Weight across Tables 8 and 9. Finally, the controlled β∈{0,0.7,1}\beta \in \{0, 0.7, 1\} evaluation in W5 below directly validates the score-mixing balance between endpoint proximity and temporal trend.

AuthorsOpenReview ↗

Response to Reviewer tYrd (Part 3/4): Downstream Contribution of Temporal Trends [W5, Q1]

W5 & Q1: Contribution of Temporal Trends Over Endpoint-Only Scoring

The temporal trend analysis mainly demonstrates changes in auxiliary dataset selection when the slope term is included (Appendix D.9). It does not directly establish whether the slope provides useful information that improves downstream performance over endpoint-only scoring. ... compare downstream performance with and without the temporal slope term?

Evaluating β∈{0,0.7,1}\beta \in \{0, 0.7, 1\} across a subject-level balanced 5-fold protocol confirms that the temporal trend term provides consistent downstream gains beyond selection changes alone. For this experiment and the matched-exposure study in W6 below, we evaluate six small-cohort benchmarks (HGD, MAMEM1, SEED-V, BCIC-IV-2a, SEED, and SEED-IV) using a subject-level balanced 5-fold cross-validation protocol instead of a single split. Target subjects are shuffled into 5 balanced test groups so every subject is tested once across the 5 folds, with the next 2 subjects in circular order used for validation and the remaining subjects for training (strictly disjoint subjects across splits, 3 seeds 42 to 44 averaged per fold, reporting 5-fold mean ±\pm sample standard deviation in % across identical splits). Holding all post-probe weighting, phased scheduling, and optimization settings identical, POSE (β=0.7\beta = 0.7) consistently outperforms both endpoint-only (β=1\beta = 1) and trend-only (β=0\beta = 0) scoring (best per backbone and column in bold):

ModelVariantHGDMAMEM1SEED-VBCIC-IV-2aSEEDSEED-IVAverage
LaBraMTrend-only (β=0\beta = 0)71.21 ±\pm 6.1447.08 ±\pm 9.3122.90 ±\pm 2.3942.08 ±\pm 5.0753.29 ±\pm 5.8534.66 ±\pm 3.0245.20
LaBraMEndpoint-only (β=1\beta = 1)73.17 ±\pm 3.8649.04 ±\pm 12.3224.20 ±\pm 1.7642.95 ±\pm 4.3153.51 ±\pm 5.5235.81 ±\pm 2.0746.45
LaBraMPOSE (β=0.7\beta = 0.7)73.92 ±\pm 4.0752.43 ±\pm 11.5624.29 ±\pm 2.2243.78 ±\pm 6.3656.34 ±\pm 5.0835.79 ±\pm 2.2547.76
CBraModTrend-only (β=0\beta = 0)68.89 ±\pm 5.4941.85 ±\pm 7.1521.98 ±\pm 1.2348.16 ±\pm 3.9253.26 ±\pm 2.6533.04 ±\pm 3.8644.53
CBraModEndpoint-only (β=1\beta = 1)69.21 ±\pm 5.0041.73 ±\pm 8.4523.56 ±\pm 1.6948.44 ±\pm 3.7653.79 ±\pm 1.9333.01 ±\pm 3.6144.96
CBraModPOSE (β=0.7\beta = 0.7)69.95 ±\pm 4.8546.72 ±\pm 9.7123.48 ±\pm 3.2150.83 ±\pm 1.3655.99 ±\pm 3.8434.15 ±\pm 3.4346.86

Both trajectory components are necessary for reliable auxiliary selection. Endpoint-only scoring (β=1\beta = 1) captures post-probe proximity but ignores whether a candidate is moving toward or away from the target representation during adaptation, falling behind POSE on almost every backbone and dataset pair (with especially clear improvements on MAMEM1 and SEED across both backbones, and essentially tied results on the remaining two pairs). Conversely, trend-only scoring (β=0\beta = 0) favors shrinking relative distances even when a source remains far from the target, underperforming POSE on every evaluated dataset. Combining the two terms therefore anchors selection in compatible regions while prioritizing sources that co-adapt favorably with the target. We will add these downstream ablation results to complement Appendix D.9.

AuthorsOpenReview ↗

Response to Reviewer tYrd (Part 4/4): Cumulative Auxiliary Exposure & Matched-Budget Comparisons [W6, Q2]

W6 & Q2: Cumulative Auxiliary Training Exposure and Matched-Budget Comparisons

POSE uses phased auxiliary sampling, whereas some baselines employ fixed mixing ratios. ... Could the authors report the cumulative auxiliary training exposure for each method ...? Would the conclusions remain consistent under matched exposure budgets?

Under any matched λmax⁡\lambda_{\max}, POSE uses strictly less cumulative auxiliary exposure than fixed-ratio and multi-task baselines, ruling out larger auxiliary training volume as the source of its gains. Over E=20E=20 epochs measured in target-epoch batch equivalents BTB_T (BiB_i batches per epoch for dataset ii), summing λ(e)\lambda(e) in Algorithm 1 across the 4 probe (00), 3 warm-up (2λmax⁡2\lambda_{\max}), 10 joint (10λmax⁡10\lambda_{\max}), and 3 cool-down (1λmax⁡1\lambda_{\max}) epochs gives POSE a cumulative auxiliary budget of 13λmax⁡BT∈{6.5,13,26,65}BT13\lambda_{\max}B_T\in\{6.5,13,26,65\}B_T when S≠∅\mathcal{S}\neq\emptyset (00 when S=∅\mathcal{S}=\emptyset). By comparison, Ratio-mixed, Meta-select, Random-select, and LogME-based apply a constant ratio across all 20 epochs for 20λmax⁡BT∈{10,20,40,100}BT20\lambda_{\max}B_T\in\{10,20,40,100\}B_T (spanning POSE's range, with POSE using only 65% at the same λmax⁡\lambda_{\max}), whereas ConFIG and GradNorm process 220BT220B_T auxiliary batches and Full-mixed processes 20∑j≠TBj20\sum_{j\neq T}B_j. Notably, removing warm-up or cool-down in Tables 8 and 9 raises exposure to 14λmax⁡BT14\lambda_{\max}B_T to 16λmax⁡BT16\lambda_{\max}B_T yet lowers accuracy.

New controlled experiments under both the exact POSE phased schedule and an exposure-matched constant schedule confirm that POSE's advantage comes from selection and weighting rather than exposure volume. Using the balanced 5-fold protocol across the six benchmarks, we evaluated Meta-select and LogME under (i) the identical POSE phased schedule and (ii) a post-epoch-4 constant ratio matching POSE's exact cumulative auxiliary batch budget (13λmax⁡BT13\lambda_{\max}B_T), alongside POSE-uniform (best per backbone and column in bold):

ModelVariantHGDMAMEM1SEED-VBCIC-IV-2aSEEDSEED-IVAverage
LaBraMPOSE-uniform73.33±4.4946.85±13.5822.57±2.3342.26±5.7455.05±5.1435.69±2.5745.96
LaBraMMeta+POSE schedule73.23±6.0047.86±13.4324.33±2.4840.97±8.2754.54±4.6335.16±2.7346.01
LaBraMMeta+matched constant73.50±4.1750.86±13.0523.60±2.7741.88±5.5554.34±4.8235.31±2.5046.58
LaBraMLogME+POSE schedule72.33±4.8646.50±14.5523.69±2.5542.47±4.8555.63±4.3935.02±1.9745.94
LaBraMLogME+matched constant73.37±5.9049.10±14.5223.93±2.4541.77±7.3354.43±6.3935.04±2.7246.27
LaBraMPOSE73.92±4.0752.43±11.5624.29±2.2243.78±6.3656.34±5.0835.79±2.2547.76
CBraModPOSE-uniform69.01±5.4445.11±12.9722.20±2.5148.72±2.5555.14±1.8533.89±3.3745.68
CBraModMeta+POSE schedule68.31±4.2442.95±10.7022.53±1.6650.14±2.2854.85±4.2733.94±1.8345.45
CBraModMeta+matched constant69.55±5.7644.11±7.0922.03±2.8149.06±3.6853.57±1.7634.04±1.8645.39
CBraModLogME+POSE schedule69.22±5.2041.26±10.9823.70±1.6350.52±3.9055.34±3.7033.52±3.4345.60
CBraModLogME+matched constant69.16±5.2345.04±11.3722.97±1.7348.85±4.3254.99±4.4032.58±3.1645.60
CBraModPOSE69.95±4.8546.72±9.7123.48±3.2150.83±1.3655.99±3.8434.15±3.4346.86

Across all matched-budget settings, POSE consistently achieves the strongest overall performance on both backbones. Under the exact same cumulative auxiliary exposure (13λmax⁡BT13\lambda_{\max}B_T), POSE outperforms Meta-select and LogME on all 12 of 12 backbone and dataset pairs under the matched-budget constant schedule (+1.18% to +1.49% average gain) and on 10 of 12 pairs under the identical POSE phased schedule (+1.26% to +1.82% average gain, with especially clear margins on MAMEM1 and SEED). Simply transferring POSE's phased schedule to heuristic or static selectors fails to close the gap and slightly trails their matched-constant counterparts on LaBraM, whereas pairing phased scheduling with POSE's probe-guided selection and inverse-score weighting (beating POSE-uniform on all 12 of 12 pairs) unlocks consistent gains across tasks. We will include this matched-exposure comparison in the revised manuscript.

Thank you again for your insightful feedback and time in reviewing our work, which have helped us substantially strengthen the paper.

Reviewer_KjtMOpenReview ↗
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Confidence
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Informativeness
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Paper summary

The paper studies multi-dataset fine-tuning of EEG foundation models. A shared backbone has dataset-specific heads, and the goal is to improve one target dataset with auxiliary datasets that may have different label spaces and montages. The proposed method, POSE, works in three steps.

  1. For the first T1 = 4 epochs, it fine-tunes on the target only. At each of these epochs it extracts mean-pooled backbone features for 1,000 fixed samples per dataset and computes MMD (RBF, median heuristic) and Fréchet distance between the target and each of the 11 candidates (Eqs. 2–3).
  2. It min-max normalizes the distances across candidates at each epoch. It then combines the final normalized distance with a min-max normalized OLS slope using β = 0.7, averages the two metrics (Eq. 5), and keeps up to K = 3 candidates whose score is below τ. These are weighted by inverse score (Eq. 6).
  3. It continues training with a linear warm-up, a constant phase, and a cosine cool-down of the auxiliary-to-target batch ratio λ(e).

The experiments cover 12 public datasets with LaBraM and CBraMod (Table 5), plus a 6-dataset REVE study (Table 6), a 3-fold subject-partition study (Table 7), ablations (Tables 2, 8, 9), an affinity matrix (Fig. 3), a comparison against 500 random auxiliary subsets (Fig. 2) and a sensitivity analysis (Fig. 5). POSE has the best average balanced accuracy: 0.560 vs 0.545 for target-only on LaBraM, and 0.550 vs 0.528 on CBraMod. Appendix B gives a first-order Taylor argument and a restatement of the Ben-David et al. (2010) bound as motivation.

Critical strengths
  1. Relevant, practical problem. Data reuse is the obvious lever for small EEG datasets, and the field has few studies of which auxiliary EEG datasets help a given target under a foundation-model backbone. Mixing all datasets (Full-mixed) or grouping them by metadata is shown to be unreliable (Table 5; MAMEM1 under LaBraM vs CBraMod). This is a useful, if expected, empirical message.
  2. Breadth of the evaluation. The study uses 12 heterogeneous datasets (22–256 channels, classification plus one regression task), two main backbones and a third (REVE). It runs five seeds, adds a 3-fold subject-partition extension, and includes gradient-based multi-task baselines (GradNorm, ConFIG, PCGrad) as well as a transferability baseline (LogME).
  3. Cheap, label-free selection. All candidates are scored along a single target-only trajectory, with no per-source models and no auxiliary labels (Sec. 3.2). The cost is reported: 8–16% of POSE runtime (Table 10).
  4. Honest framing of the theory. Appendix B explicitly says that the Taylor expansion and the domain-adaptation bound are motivation only. It states that they neither justify the score mixture nor the inverse weighting, and that the normalized slope is not a directional derivative. I appreciate the candor.
  5. Clear and careful protocol statements. The paper states that tuning and checkpoint selection use target validation data only (App. A.2, C.3.4). It reports per-method tuning grids and discloses pretraining-corpus overlap (App. C.2).
Critical weaknesses
  1. Evaluation units are too small to support the generalization claims. In the main comparison (Table 4), BCIC-IV-2a, HGD, MAMEM1, SEED, SEED-IV and SEED-V each use one validation subject and one test subject, and SHU-MI uses two of each. For half of the benchmark, a "cross-subject" score in Table 1/5 is therefore the accuracy on a single held-out person, and hyperparameters and checkpoints are selected on a single other person. The five seeds (42–46) only capture optimization noise, not subject variability, which is the dominant source of variance in cross-subject EEG.

    • The paired t-tests in Table 1/5 appear to use n = 5 seed-level averages. They do not test generalization to new subjects and should not be read as such.
    • Table 7 (3 folds) helps, but three folds still means three test subjects for these datasets, and the fold standard deviations are large (e.g., MAMEM1 ±0.086–0.131, TUEV ±0.097–0.114). Only four methods are compared there.
    • For datasets with ≤ 16 subjects, leave-one-subject-out (or k-fold over subjects), with significance tests over subjects, is the standard expectation in this literature.
    • As it stands, the headline gain of about 1.5 pp is of the same order as the seed standard deviations (0.01–0.04) and is measured on very few test subjects.
  2. The central claimed novelty — the temporal-trend term — is never validated on downstream performance. The contribution list and Sec. 3.2–3.3 emphasize combining endpoint discrepancy with its trend over the probe trajectory. The supporting evidence is weak:

    • β is fixed at 0.7 throughout (App. C.3.4), and there is no performance ablation for β = 1 (endpoint only, target-adapted space) or β = 0 (trend only).
    • Appendix D.9 reports only that the top-3 set changes in over 80% of cases. The authors themselves note that this "measures changes in selection decisions rather than isolating the effect of the slope term on downstream performance." A change in selection is not evidence of benefit.
    • The "No Probe" ablation conflates two things: using a target-adapted representation, and using a trajectory. Endpoint-only selection after 4 target epochs is the missing control.
    • The slope comes from an OLS fit over only 4 points of min-max-normalized relative distances, and the median-heuristic bandwidth is re-estimated at each checkpoint (acknowledged in B.1). It is therefore plausibly noisy. Without the β sweep, the trajectory idea is unsupported.
  3. The ablation design is biased in POSE's favor.

    • (a) The main ablation (Tables 2/8) is restricted to the 8 datasets "where POSE improves over target-only fine-tuning on both backbones" (Sec. 4.3). Choosing evaluation subsets based on the full method's test outcome inflates the apparent contribution of every component.
    • (b) All variants "retain the remaining hyperparameters of the complete framework" (Sec. 4.3). In other words, λmax and τ were tuned on validation for full POSE and reused for each variant, so the variants are not re-tuned.
    • (c) On the remaining datasets (Table 9), which use a fixed configuration, the differences are tiny and mixed. Uniform Weight beats POSE on LaBraM-HGD and CBraMod-TUAB. No Ramp ties POSE on CBraMod-CCD.
    • (d) The POSE numbers in Table 9 differ from Table 5 (e.g., LaBraM TUEV 0.551 vs 0.532), because the configuration is different. That is fine, but it confirms that differences of 1–2 pp lie within configuration noise.
    • Each ablation should be run on all 12 targets, with each variant re-tuned on the same grid.
  4. Target-only baselines look under-trained, which may inflate the "auxiliary regularization" gains. All methods train for only E = 20 epochs with batch size 32 (App. C.3.4), and TUAB and TUEV are subsampled to 5% and 20% (App. C.1). Several target-only numbers fall well below published fine-tuning results for the same backbones. For example, the CBraMod paper (Wang et al., ICLR 2025) reports substantially higher balanced accuracy on TUEV, SEED-V, BCIC-IV-2a and SHU-MI than the target-only values here (0.507, 0.244, 0.433, 0.556).

    • I accept that the splits differ. But when a baseline is weak, regularization from extra data tends to help, and that effect can disappear against a well-tuned single-dataset run: longer schedules, layer-wise LR decay as in LaBraM/CBraMod, stronger augmentation or dropout, or simply more epochs at matched compute.
    • Compute is not matched. With λmax up to 5, POSE processes up to 6× more batches per epoch than target-only.
    • A compute-matched target-only baseline and target-only results under the backbones' published fine-tuning recipes are needed.
  5. Selection baselines confound the selection criterion with the schedule.

    • Random-select, Meta-select and LogME-based selection use a constant ratio with no warm-up or cool-down (Sec. 4.1; App. C.3.5: "without target-only probing or ratio ramping").
    • POSE's ablations show that removing warm-up or cool-down alone costs 1.5–2 pp (Table 2). So a large part of POSE's margin over these baselines could come from the schedule rather than from probe-guided selection.
    • The fair comparison is each selector (LogME, Meta, Random, endpoint-only, pretrained-space) inside the same phased schedule and weighting.
    • It is also unclear whether λmax was tuned for LogME-based selection ("default ratio of 1" in C.3.5 vs. the λmax search described in C.3.4).
  6. The weighting rule is ad hoc and degenerate. The scores are averages of min-max normalized quantities, and ε = 10⁻⁸ in Eq. 6.

    • A candidate that is best on both components for both metrics gets s ≈ 0 and therefore essentially all the weight. This explains the 1.00 entries in Fig. 3 (CBraMod SEED-IV→SEED; LaBraM BCIC-IV-2a).
    • The weights depend on which other candidates happen to be in the pool, because of the min-max scaling, and they are not calibrated to anything. τ is likewise a threshold on a relative quantity.
    • Appendix B.2 explicitly does not justify inverse-discrepancy weighting. A softmax with temperature, or rank-based weights, would be more principled and should be compared.
    • The "Uniform Weight" ablation gains (about 2 pp) are again measured on the biased 8-dataset subset.
  7. Novelty is moderate relative to existing work on source selection and task affinity.

    • Using distributional distances between datasets to choose sources has a long history. Examples are domain-similarity (EMD) based source selection (Cui et al., CVPR 2018), dataset distances via optimal transport (OTDD; Alvarez-Melis & Fusi, NeurIPS 2020), and many MMD-based multi-source selection schemes in EEG transfer learning.
    • Choosing auxiliary tasks from training dynamics is also established: task grouping (Standley et al., ICML 2020; Fifty et al., NeurIPS 2021, "TAG"), auxiliary-loss gating by gradient similarity (Du et al., 2018), and auxiliary task reweighting.
    • Ramping auxiliary losses up and down over training is a common heuristic.
    • Multi-dataset/instruction-style joint fine-tuning of EEG FMs is also explored, e.g., NeuroLM (Jiang et al., ICLR 2025). It is not discussed, and neither is BIOT's cross-dataset training beyond a passing citation.
    • The related-work section omits most of the task-affinity/grouping literature, and none of these methods (e.g., TAG-style lookahead affinity, or gradient-cosine gating as a selection baseline) is compared in the main tables. Appendix D.13 gives only an anecdotal gradient-similarity diagnostic on one dataset with a different candidate pool.
    • The specific new ingredient is the slope-over-4-epochs term (see W2), which is incremental.
  8. The random-mixture comparison (Sec. 4.6, App. D.8, Fig. 2) is not apples-to-apples.

    • Each sampled mixture is a single-seed run with a random learning rate and, it seems, no schedule or tuning. POSE, by contrast, is a 5-seed mean with validation-tuned λmax/τ.
    • A 5-seed mean is less noisy than a single run and is pulled toward the center, but tuning advantages work in POSE's favor. The 90th-percentile figure is therefore hard to interpret.
    • Even at face value, about 10% of untuned random mixtures beat POSE.
    • The count is also wrong. Each target has 11 candidates, so there are 2¹¹ − 1 = 2,047 auxiliary subsets, not 2¹² − 1 = 4,095. Was the target included in the sampled "combinations"?
  9. The "robust to hyperparameters" claim (App. D.10) is overstated.

    • The success rate is computed conditionally, excluding targets where no configuration beats target-only. Unconditionally it is 53/96 ≈ 55% (LaBraM) and 54/96 ≈ 56% (CBraMod). So in roughly half of the λmax/τ settings, POSE does not beat target-only.
    • The variance decomposition shows that seed variance (about two thirds of the total) dominates configuration variance. That says the effect sizes are small relative to noise. It does not show that the method is "insensitive."
  10. Potential cross-dataset subject leakage is not addressed. The protocol keeps target subjects disjoint across train, validation and test. But auxiliary datasets may contain the same individuals as the target's test subjects:

    • TUAB and TUEV both derive from the TUH corpus and may share patients. TUAB is in fact the most heavily weighted auxiliary for TUEV in Fig. 3.
    • The SEED-family datasets come from the same lab, and participants may be recurrent.
    • In addition, LaBraM's pretraining includes SEED, SEED-IV and PhysioNet-MI, and CBraMod's includes TUAB and TUEV (acknowledged in App. C.2).
    • If an auxiliary training set contains target test subjects, the gains on those pairs are not cross-subject gains. The authors should verify subject identity across the auxiliary pool and exclude overlaps.
  11. The theory adds little. Eq. 4/B.1 is a first-order Taylor expansion with a Lipschitz remainder. B.2 restates Ben-David et al. (2010) with a convex combination of sources, which is a known result, e.g., the multi-source bounds in Ben-David et al. (2010) itself and Zhao et al. (2018). Neither result connects to the actual score, which the authors admit. This is fine as motivation, but it should not take up a page of main-text/appendix narrative or be presented as a principled justification.

Minor Issues

  • Sec. 3.3 says that Eq. 6 "assigns greater auxiliary participation to candidates with lower compatibility scores". Since lower score means higher compatibility, the sentence reads as the opposite of what is meant. Please rephrase.
  • Fig. 1 writes the normalization as "σ(1/score)", which reads like a sigmoid. It should be a sum.
  • Sec. 1: "fine-tuning ... on a single target dataset ... has proven suboptimal in many settings" needs citations.
  • Sec. 1, l. 72–73: "to support joint learning followed" is garbled.
  • Sec. 4.5 reports CBraMod numbers (MAMEM1 0.487→0.562; TUAB 0.809), but the text does not say which backbone. Fig. 4 clarifies it is CBraMod, which should be stated in the main text.
  • Table 1 duplicates the LaBraM half of Table 5. That space could hold the 3-fold results, which are more informative.
  • Tables 6 and 11 lack standard deviations and seed counts.
  • Table 10: total training time (about 9–19 h per run on a V100) is not compared with target-only wall-clock time, so the "overhead" is relative to POSE itself. Please also report the absolute cost relative to target-only.
  • Specify the feature dimensionality used for FD and the covariance regularization. With 1,000 samples, FD covariance estimates may be ill-conditioned for wide backbones.
  • Appendix D.13 compares rank ranges of gradient similarity vs MMD on a different candidate pool. That says little about selection quality and could be dropped or replaced with a proper baseline.
  • The REVE backbone is used but never cited or described.

Justification of Rating

The problem is worthwhile and the experimental breadth (12 datasets, 3 backbones, several baseline families) is above average for EEG-FM papers. However, the evidence does not yet support the specific claims:

  • The key "trajectory" component has no performance ablation.
  • Ablations are run on a subset chosen because POSE works there, with variants that are not re-tuned.
  • Selection baselines lack the schedule that POSE's own ablation shows to be worth 1.5–2 pp.
  • Target-only baselines are weaker than published numbers and not compute-matched.
  • Most small datasets are tested on a single held-out subject, so a 1.5–2 pp average gain is hard to distinguish from subject-level noise.

I would move toward weak acceptance if the authors show four things: (i) a β = 1 / β = 0 comparison in which the trend term gives a consistent, significant gain; (ii) LOSO or multi-fold subject-level evaluation with significance over subjects; (iii) selector-only comparisons inside the same schedule; and (iv) compute-matched, properly tuned target-only baselines, with POSE retaining a clear margin. I would lower my score if the cross-dataset subject-overlap check reveals leakage, or if the gains disappear against well-tuned target-only fine-tuning.

Questions for authors
  1. Can you report a β sweep, in particular β = 1 (endpoint-only in the target-adapted space) and β = 0, on all 12 targets for both backbones, with each variant re-tuned on the same λmax/τ grid? If endpoint-only matches POSE, the trajectory contribution disappears.
  2. Can you re-run the main comparison with leave-one-subject-out (or ≥ 5-fold subject CV) for the ≤ 16-subject datasets, and report significance across subjects rather than across seeds? Which unit does the paired t-test in Table 1/5 pair over (seeds? datasets×seeds?), and what is n?
  3. How does a compute-matched target-only baseline perform? For example, train for the same number of gradient steps as POSE at the selected λmax, and/or follow the published LaBraM/CBraMod fine-tuning recipes (epochs, layer-wise decay). Why do your target-only numbers differ so much from those reported by the backbone authors on TUEV, SEED-V, BCIC-IV-2a and SHU-MI?
  4. Please evaluate LogME, Meta-select, Random-select and No-Probe selection inside the identical POSE schedule and weighting, so that only the selector differs. Was λmax tuned for LogME-based selection?
  5. Did you check for overlapping individuals between the target's test subjects and any auxiliary training set (TUAB/TUEV patients; SEED/SEED-IV/SEED-V participants)? If there is overlap, how do the results change when it is removed?
  6. Why is the main ablation restricted to targets where POSE beats target-only? Please give the Table 2/8 averages over all 12 targets, with re-tuned variants.
  7. How stable is selection across seeds and folds? For example, what is the Jaccard similarity of selected sets across seeds for a fixed target? Fig. 3's diffuse rows (e.g., CBraMod FACED, MAMEM1) suggest that it is unstable.
  8. How often is the selected set empty (e.g., LaBraM TUAB appears all-zero)? In those cases POSE reduces to target-only with a different random state (App. A.2). How many of the reported "comparable to target-only" results are of this kind?
  9. For Fig. 2, please give results for random mixtures with the same tuning and schedule as POSE, averaged over 5 seeds, and clarify the 4,095 vs 2,047 count.
  10. For REVE (Table 6): how many seeds were run, what are the standard deviations, and what hyperparameter tuning was used? Ratio-mixed is within 0.8 pp of POSE on average and beats it on two of six datasets.
6 comments
AuthorsOpenReview ↗

Response to Reviewer KjtM (Part 1/6): Subject-Level 5-Fold CV & Temporal-Trend Validation [W1, W2, Q1, Q2]

We sincerely thank you for the detailed review. Below, we address each of your comments and questions in detail.

W1 & Q2: Balanced 5-Fold Subject Cross-Validation on Small-Cohort Benchmarks

Evaluation units are too small to support the generalization claims. ... For datasets with ≤16\le16 subjects, leave-one-subject-out (or k-fold over subjects) ... is the standard expectation ... Can you re-run the main comparison with leave-one-subject-out (or ≥5\ge5-fold subject CV) for the ≤16\le16-subject datasets ...? Which unit does the paired t-test in Table 1/5 pair over ... and what is n?

Evaluating all six small-cohort benchmarks (≤16\le16 subjects) under a subject-level balanced 5-fold cross-validation protocol ensures 100% subject test coverage and multi-subject validation, with POSE consistently outperforming both Target-only fine-tuning and competing selectors across folds. For all our new supplementary evaluations across HGD, MAMEM1, SEED-V, BCIC-IV-2a, SEED, and SEED-IV, we shuffle target subjects into 5 balanced test groups so that every subject is evaluated in the test set exactly once across the 5 folds, while the next 2 subjects in circular order form the validation set and the remaining subjects form the training set, keeping train, validation, and test subjects strictly disjoint and leaving auxiliary dataset partitions unchanged. Each fold is averaged over 3 random seeds (42 to 44), and we report the 5-fold equal-weighted mean ± sample standard deviation (ddof=1\text{ddof}=1) of test balanced accuracy (%) across identical splits for all methods. Together with the six larger datasets in Table 5, every dataset in our benchmark is now evaluated across representative multi-subject test partitions. As detailed in the tables for W2, W4, and W5 below, POSE achieves the highest 5-fold average accuracy on both LaBraM and CBraMod, outperforming the Target-only baseline on all 12 of 12 backbone and dataset pairs while also leading all schedule-matched and exposure-matched selector baselines. Regarding Q2's question on Table 1 and Table 5, the paired tt-tests pair the 5-seed dataset means across the n=11n=11 classification tasks rather than across n=5n=5 seeds, summarizing benchmark-wide task consistency with p=0.0072p=0.0072 on LaBraM and p=0.0213p=0.0213 on CBraMod against Target-only.

W2 & Q1: Downstream Validation of the Temporal-Trend Term (β∈{0,0.7,1}\beta\in\{0,0.7,1\})

The central claimed novelty, the temporal-trend term, is never validated on downstream performance. ... Endpoint-only selection after 4 target epochs is the missing control. ... Can you report a β\beta sweep, in particular β=1\beta=1 (endpoint-only in the target-adapted space) and β=0\beta=0 ...?

Evaluating endpoint-only selection in the 4-epoch target-adapted space (β=1\beta=1), trend-only selection (β=0\beta=0), and POSE (β=0.7\beta=0.7) under the balanced 5-fold protocol confirms a clear and consistent downstream gain from the trajectory slope. All three β\beta variants share the exact same 4-epoch probe checkpoints, inverse-score weighting, phased schedule, and training configuration, isolating β\beta without confounding from No Probe, with the best result per backbone and column marked in bold:

ModelVariantHGDMAMEM1SEED-VBCIC-IV-2aSEEDSEED-IVAverage
LaBraMTrend-only (β=0\beta=0)71.21±6.1447.08±9.3122.90±2.3942.08±5.0753.29±5.8534.66±3.0245.20
LaBraMEndpoint-only (β=1\beta=1)73.17±3.8649.04±12.3224.20±1.7642.95±4.3153.51±5.5235.81±2.0746.45
LaBraMPOSE (β=0.7\beta=0.7)73.92±4.0752.43±11.5624.29±2.2243.78±6.3656.34±5.0835.79±2.2547.76
CBraModTrend-only (β=0\beta=0)68.89±5.4941.85±7.1521.98±1.2348.16±3.9253.26±2.6533.04±3.8644.53
CBraModEndpoint-only (β=1\beta=1)69.21±5.0041.73±8.4523.56±1.6948.44±3.7653.79±1.9333.01±3.6144.96
CBraModPOSE (β=0.7\beta=0.7)69.95±4.8546.72±9.7123.48±3.2150.83±1.3655.99±3.8434.15±3.4346.86

Despite being estimated over four probe epochs, the slope signal is informative rather than noisy and consistently outperforms both β=1\beta=1 and β=0\beta=0. Relative to endpoint-only selection (β=1\beta=1), incorporating the temporal trend improves average accuracy by +1.31% on LaBraM and +1.90% on CBraMod, winning on nearly every backbone and dataset pair, especially on MAMEM1, SEED, and BCIC-IV-2a, while remaining virtually tied on the other two pairs. Conversely, relying on the trend alone without an endpoint anchor (β=0\beta=0) lowers performance across every evaluated dataset on both backbones, confirming that endpoint proximity and temporal evolution act as complementary selection signals. We will incorporate this endpoint-versus-trajectory ablation into the revised manuscript.

AuthorsOpenReview ↗

Response to Reviewer KjtM (Part 2/6): Ablation Protocol & Target-Only Baseline [W3, W4, Q3, Q6]

W3 & Q6: Ablation Subset Design and Controlled Hyperparameter Protocol

Why is the main ablation restricted to targets where POSE beats target-only? ... All variants "retain the remaining hyperparameters of the complete framework" ...

Separating the two dataset groups was intended to make component contributions observable where multi-dataset adaptation is active, and the four remaining datasets are not failure cases of POSE. Because an ablation study aims to isolate individual component effects, on already saturated targets such as TUAB where auxiliary training leaves minimal room for gain over Target-only, all variants cluster tightly and component differences cannot be meaningfully distinguished. Meanwhile, CCD is reported separately because it is a regression task evaluated by NRMSE rather than balanced accuracy, on which POSE beats Target-only across both backbones, while targets such as HGD and TUEV also improve on LaBraM or in the 3-fold evaluation (Table 7).

Holding λmax⁡\lambda_{\max} and τ\tau fixed across variants follows a standard single-factor ablation design, and existing results across Tables 8 and 9 confirm consistent component gains over the full benchmark. Re-tuning λmax⁡\lambda_{\max} and τ\tau per variant would simultaneously alter total auxiliary exposure and selected subset size, confounding the direct effect of removing a component with hyperparameter compensation. Moreover, Table 9 evaluates POSE and all ablated variants under the exact same untuned setting of τ=0.3\tau=0.3 and λmax⁡=1.0\lambda_{\max}=1.0, which keeps auxiliary participation active rather than collapsing into S=∅\mathcal{S}=\emptyset target-only runs, and POSE still outperforms No Probe on 7 of 8 backbone and dataset pairs, outperforms or ties No Ramp on 7 of 8 pairs, outperforms or ties Uniform Weight on 6 of 8 pairs, and matches or beats every variant on CCD. Combining Tables 8 and 9 across all 11 classification targets reduces POSE's average margins by at most 0.5% relative to the 8-dataset subset, preserving clear gains across both LaBraM and CBraMod. We will clarify this grouping rationale and present the overall benchmark picture more transparently in Section 4.3 and Appendices D.4 and D.5.

W4 & Q3: Target-Only Recipe and Comparison With Published Numbers

Target-only baselines look under-trained ... How does a compute-matched target-only baseline perform ...? Why do your target-only numbers differ so much from those reported by the backbone authors ...?

Our original 20-epoch Target-only baselines already converged fully, as shown by the training and validation curves in Figure 4 and tuned over a 9-point LR and weight-decay grid in Appendix C.3.4, and further training Target-only under the backbones' original 50-epoch settings on the new 5-fold splits still sees POSE win on all 12 of 12 pairs. Following your suggestion, we trained Target-only under the balanced 5-fold protocol from pretrained weights keeping the same single-layer linear head without auxiliary data. The recipe runs for 50 epochs, exceeding POSE's average total update budget of ~40 target-equivalent epochs across these targets, with batch size 32, weight decay 0.05, label smoothing 0.1, 5-epoch linear warmup followed by cosine decay, and validation selection over LR∈{1×10−4,5×10−4}\text{LR}\in\{1\times10^{-4},5\times10^{-4}\}. Model-specific settings follow the published backbone designs: LaBraM uses 0.9 layer-wise learning-rate decay, parameter-specific weight-decay exclusions, attention dropout 0.0, and drop-path 0.1, while CBraMod searches the backbone LR and sets the head base LR to ≈3.54×10−4\approx3.54\times10^{-4} per the original CBraMod scaling formula under cosine scheduling, with the best result per backbone and column in bold:

ModelVariantHGDMAMEM1SEED-VBCIC-IV-2aSEEDSEED-IVAverage
LaBraMTarget-only73.02±6.8150.90±13.4523.40±1.7243.61±5.8755.25±3.4934.91±1.2246.85
LaBraMPOSE73.92±4.0752.43±11.5624.29±2.2243.78±6.3656.34±5.0835.79±2.2547.76
CBraModTarget-only68.52±4.2644.00±9.7223.29±1.1349.17±4.5054.76±6.0433.17±3.5945.49
CBraModPOSE69.95±4.8546.72±9.7123.48±3.2150.83±1.3655.99±3.8434.15±3.4346.86

Across all six benchmarks, 20-epoch POSE without these backbone-specific single-task regularizers outperforms Target-only on 6 of 6 targets for LaBraM and 6 of 6 targets for CBraMod, confirming that compatible multi-dataset supervision provides complementary benefits beyond longer single-task optimization. Regarding why the original Target-only numbers in Table 5 differ from those in the CBraMod paper, the two setups use different data partitions and preprocessing pipelines: our benchmark enforces strict cross-subject splits, fixed subsampling on TUAB and TUEV to balance multi-dataset scale, and a shared single-layer linear head across all methods for controlled multi-dataset comparison.

AuthorsOpenReview ↗

Response to Reviewer KjtM (Part 3/6): Selector Comparison Under Matched Schedule & Exposure [W5, Q4]

W5 & Q4: Controlled Comparison of Selectors Under Matched Schedule and Exposure

Selection baselines confound the selection criterion with the schedule. ... Please evaluate LogME, Meta-select, Random-select and No-Probe selection inside the identical POSE schedule and weighting, so that only the selector differs. Was λmax⁡\lambda_{\max} tuned for LogME-based selection?

When evaluated inside the identical POSE phased schedule or under an exposure-matched constant schedule, POSE consistently outperforms alternative selectors across both backbones. Under the balanced 5-fold protocol, we compared POSE against POSE-uniform, which keeps POSE's selection and schedule with equal weights, Meta-select and LogME-based selection equipped with the exact POSE phased schedule of 4 target-only epochs followed by 3 warmup, 10 joint, and 3 cosine-cooldown epochs, and Meta-select and LogME-based selection under a matched-budget constant ratio after epoch 4 that delivers the exact same cumulative auxiliary batches (13λmax⁡BT13\lambda_{\max} B_T) as POSE:

ModelVariantHGDMAMEM1SEED-VBCIC-IV-2aSEEDSEED-IVAverage
LaBraMPOSE-uniform73.33 ±\pm 4.4946.85 ±\pm 13.5822.57 ±\pm 2.3342.26 ±\pm 5.7455.05 ±\pm 5.1435.69 ±\pm 2.5745.96
LaBraMMeta + POSE schedule73.23 ±\pm 6.0047.86 ±\pm 13.4324.33 ±\pm 2.4840.97 ±\pm 8.2754.54 ±\pm 4.6335.16 ±\pm 2.7346.01
LaBraMMeta + matched constant73.50 ±\pm 4.1750.86 ±\pm 13.0523.60 ±\pm 2.7741.88 ±\pm 5.5554.34 ±\pm 4.8235.31 ±\pm 2.5046.58
LaBraMLogME + POSE schedule72.33 ±\pm 4.8646.50 ±\pm 14.5523.69 ±\pm 2.5542.47 ±\pm 4.8555.63 ±\pm 4.3935.02 ±\pm 1.9745.94
LaBraMLogME + matched constant73.37 ±\pm 5.9049.10 ±\pm 14.5223.93 ±\pm 2.4541.77 ±\pm 7.3354.43 ±\pm 6.3935.04 ±\pm 2.7246.27
LaBraMPOSE73.92 ±\pm 4.0752.43 ±\pm 11.5624.29 ±\pm 2.2243.78 ±\pm 6.3656.34 ±\pm 5.0835.79 ±\pm 2.2547.76
CBraModPOSE-uniform69.01 ±\pm 5.4445.11 ±\pm 12.9722.20 ±\pm 2.5148.72 ±\pm 2.5555.14 ±\pm 1.8533.89 ±\pm 3.3745.68
CBraModMeta + POSE schedule68.31 ±\pm 4.2442.95 ±\pm 10.7022.53 ±\pm 1.6650.14 ±\pm 2.2854.85 ±\pm 4.2733.94 ±\pm 1.8345.45
CBraModMeta + matched constant69.55 ±\pm 5.7644.11 ±\pm 7.0922.03 ±\pm 2.8149.06 ±\pm 3.6853.57 ±\pm 1.7634.04 ±\pm 1.8645.39
CBraModLogME + POSE schedule69.22 ±\pm 5.2041.26 ±\pm 10.9823.70 ±\pm 1.6350.52 ±\pm 3.9055.34 ±\pm 3.7033.52 ±\pm 3.4345.60
CBraModLogME + matched constant69.16 ±\pm 5.2345.04 ±\pm 11.3722.97 ±\pm 1.7348.85 ±\pm 4.3254.99 ±\pm 4.4032.58 ±\pm 3.1645.60
CBraModPOSE69.95 ±\pm 4.8546.72 ±\pm 9.7123.48 ±\pm 3.2150.83 ±\pm 1.3655.99 ±\pm 3.8434.15 ±\pm 3.4346.86

Across both schedule-matched and exposure-matched settings, POSE consistently achieves the strongest overall performance on both backbones. Simply transferring POSE's phased schedule to heuristic or static selectors fails to close the gap, as POSE remains +1.26% to +1.82% higher in average accuracy than Meta + POSE schedule and LogME + POSE schedule, which even slightly trail their matched-constant counterparts on LaBraM, while POSE also outperforms both selectors on every backbone and dataset pair under the matched-budget constant schedule. Likewise, POSE surpasses POSE-uniform on every pair, and No Probe in Tables 2, 8, and 9 already shares the exact POSE phased schedule and inverse-score weighting yet consistently lags behind POSE across the benchmark. Finally, regarding Q4's protocol question, LogME-based selection in Table 5 tuned λmax⁡∈{0.5,1.0,2.0,5.0}\lambda_{\max} \in \{0.5, 1.0, 2.0, 5.0\} on target validation data following Appendix C.3.4, whereas "default ratio of 1" in Appendix C.3.5 referred only to the code default prior to grid search.

Comments on the paper

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Global Response: Consensus Strengths, Core Contributions & Summary of New Evidence

We sincerely thank the reviewers for their time and constructive feedback. Below, we summarize the consensus strengths across reviews, highlight POSE's core scientific value, and briefly outline our response.

1. Consensus Strengths Recognized by All Reviewers

  • Important practical problem and data-centric insight. All three reviewers recognize that reusing heterogeneous EEG datasets while mitigating negative transfer is a timely challenge for EEG foundation models (KjtM, tYrd, vKqS). Reviewers particularly highlight our finding that indiscriminate mixing and surface-level metadata grouping are unreliable, whereas effective auxiliary selection shows clear backbone-dependent and cross-paradigm patterns that motivate data-centric adaptation research (KjtM, vKqS).
  • Lightweight, search-free, and architecture-preserving design. Reviewers note that POSE scores all candidates along a single short target-only probe without source-specific models, aligned auxiliary labels, or subset search, adding modest overhead while keeping the pretrained backbone and inference architecture intact (KjtM, tYrd, vKqS).
  • Comprehensive evaluation breadth and transparent protocols. Reviewers commend our study across 12 heterogeneous public datasets spanning diverse montages and paradigms, multiple foundation models, and broad multi-task and transferability baselines (KjtM, tYrd, vKqS).

2. Core Contributions and Value Proposition of POSE

POSE reframes multi-dataset EEG fine-tuning from brittle data mixing or intractable subset search into a reliable, search-free adaptation framework. Although scarce recordings and cross-subject noise motivate auxiliary data reuse in EEG, indiscriminate mixing and heuristic task grouping often trigger severe negative transfer, while searching across thousands of candidate subsets is computationally infeasible. Rather than chasing an elusive oracle subset, POSE offers a single-pass mechanism that reliably captures multi-domain gains where complementary supervision exists while safeguarding well-constrained or weakly compatible targets against harmful interference.

Beyond accuracy gains, our work establishes a target-conditioned representation-evolution view of dataset compatibility for neural foundation models. Compatibility in EEG cannot be predicted from surface task labels or static pretrained embeddings alone. By coupling adapted endpoint proximity and trajectory slopes during early target-only probing with phased auxiliary scheduling, POSE tracks how candidate distributions co-evolve as the backbone specializes to the target. Across four foundation models with distinct architectures and pretraining objectives, our results further show that auxiliary compatibility is inherently backbone-dependent, providing practical guidance for curating heterogeneous neural corpora.

3. Brief Summary of Response

  • Balanced 5-fold subject CV: Re-evaluated all six small-cohort targets (≤16\le16 subjects) with 100% subject test coverage, confirming consistent POSE gains (KjtM W1/Q2).
  • Temporal-trend and probe duration: β∈{0,0.7,1}\beta\in\{0,0.7,1\} ablations confirm clear gains over β=1\beta=1 and β=0\beta=0, with stable dynamics across T1∈{2,4,6}T_1\in\{2,4,6\} (KjtM W2/Q1, tYrd W3/W5, vKqS W1/Q2).
  • Matched schedule and exposure: Under the exact POSE schedule and matched budgets, POSE beats Meta-select, LogME, and uniform weighting on both backbones (KjtM W5/Q4, tYrd W6/Q2).
  • 50-epoch reference Target-only: Against 50-epoch published backbone fine-tuning recipes, 20-epoch POSE wins on all 12 of 12 pairs (KjtM W4/Q3).
  • Non-Transformer SSM and single-source runs: POSE generalizes to CodeBrain (vKqS W4/Q1), and single-source runs confirm high-gain anchoring and outlier filtering (tYrd W2/Q1, vKqS W2/Q3).

We thank the reviewers again for their time and effort.

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

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