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Under review as a conference paper at ICLR 2027

Kernelized Task-Sufficiency Regularization for EEG Foundation Model Adaptation

Abstract

Adapting EEG foundation models to new tasks and individuals is essential, especially when task labels are scarce. Yet strong predictive performance does not reveal whether adaptation captures the task-relevant information available from pretraining. A residual-information audit on held-out subjects shows that frozen pretrained features can improve adapted logits in several settings, including after full fine-tuning. Motivated by this finding, we propose ReSuff, which encourages adapted representations to capture label information available in a fixed, compact view of pretrained features. Using label residuals defined by conditional class probabilities, we derive a joint Gaussian-kernel criterion that vanishes exactly at task sufficiency relative to this view at the population level. During training, ReSuff fits a kernel predictor on support subjects and evaluates residual moments on disjoint query subjects, while class-conditioned subject-adversarial learning addresses intersubject variation. Across three limited-label, subject-independent EEG benchmarks and three pretrained backbones, ReSuff improves balanced accuracy over the matched task-focused adaptation baseline in all nine backbone and dataset combinations, with an average gain of 2.3 percentage points. On REVE, it further improves the two-task mean balanced accuracy of four adaptation strategies by 1.5–2.2 points. These results show ReSuff is a practical plug-in to improve EEG foundation model adaptation without increasing inference cost.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
EEG Foundation Models, Parameter-Efficient Fine-Tuning, Predictive Sufficiency, Kernel Conditional Moments

Reviews

Among:
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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_yWvvOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper introduces a kernelized task-sufficiency regularizer (ReSuff) for fine-tuning EEG foundation models to new subjects and tasks. The design of the regularizer is motivated by a residual-information audit, which shows that features from the frozen pre-trained foundation model can improve the predictions of the adapted model. The authors derive a Gaussian-kernel criterion that measures task sufficiency and can be used during training. ReSuff is evaluated with the pre-trained foundation models REVE, LaBraM, and CBraMod on PhysioNet-MI, Mental Arithmetic, and ISRUC.

Critical strengths

The method is well motivated through the residual-information audit and through Propositions 1 and 2, which characterize task sufficiency in terms of the frozen pre-trained model.

Critical weaknesses

Numerical Results

  • The improvements achieved by ReSuff in Tab. 1 over the parameter-efficient fine-tuning baselines are small and come with high standard deviations. When full fine-tuning is included in the comparison, it outperforms ReSuff in 5 out of 9 cases, with one tie.
  • The hyperparameter choice is not consistent: in Fig. 4, the best regularization weight for LaBraM is ~0.02, whereas the weights are set to 0.5 (lines 464ff.). In Fig. 4 and Sec. 4.4, the regularization weights are given per model, while in lines 306ff. they are given per dataset.
Questions for authors
  • Can the authors clarify the hyperparameter sweep for the main experiment and provide some context (e.g., dataset, error bars) for Fig. 4?
  • Can the authors extend Tab. 2 by comparing full fine-tuning vs. full fine-tuning + ReSuff for REVE on ISRUC and for LaBraM and CBraMod on PhysioNet-MI, Mental Arithmetic, and ISRUC?
  • The appendix on page 13 ends mid-sentence. Are some pages missing?
Reviewer_g4wZOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This paper introduces ReSuff, a regularizer for adapting EEG foundation models that encourages the adapted representation to capture label information available in a fixed, compact view of frozen pretrained features. The authors define task sufficiency through conditional independence and derive a population characterization based on label residuals and a joint Gaussian kernel. During training, conditional label means are estimated by weighted kernel ridge regression on support subjects, and residual moments are evaluated on separate query subjects. Experiments on three datasets and three pretrained backbones show higher mean balanced accuracy than the matched TASTEFUL baseline in all nine comparisons, with an average gain of approximately 2.3 percentage points. Further experiments on REVE examine ReSuff alongside four adaptation strategies. The auxiliary components are used only during training, leaving the inference architecture unchanged.

Critical strengths
  1. Assessing whether frozen pretrained features retain label information beyond an adapted representation is relevant to understanding adaptation.

  2. The matched comparisons and subject-disjoint residual estimation are worthwhile.

Critical weaknesses
  1. The practical regularizer does not isolate task insufficiency. The paper needs stronger evidence that reducing the empirical objective reflects greater use of reference information rather than improved prediction under the auxiliary KRR model.
  2. The ablation does not establish the contribution of reference-dependent moments. The query-MSE comparison in Table 3 is useful, but it covers only Mental Arithmetic and does not separate contributions from dependence on the frozen reference.
  3. The training objective is incompletely specified, leaving attribution unclear. The abstract, introduction, and method describe class-conditioned subject-adversarial training, yet Eq. 16 includes only cross-entropy and the kernel penalty. The discriminator loss, its coefficient, and its optimization procedure are not defined. It is also unclear whether this component is included in the matched baselines and the query-MSE control.
  4. The experimental protocol and uncertainty reporting are insufficient to assess reliability. The supplied PDF does not quantify the limited-label budget, subject counts per split, effective support/query sizes, or the precise checkpoint-selection procedure.
  5. The mechanistic evidence remains inconclusive. A reduction in the training-related kernel statistic is difficult to interpret because both the residual predictor and the task-representation kernel change during optimization.
  6. The practical advantage and methodological contribution need clearer support. The nine positive comparisons against TASTEFUL are encouraging, but ReSuff does not consistently outperform stronger task-specific alternatives.
Questions for authors
  1. Was class-conditioned subject-adversarial training actually used? Please specify its loss, coefficient, optimization procedure, and inclusion in each baseline and control.

  2. What are the label budgets, subjects and trials in each split, batch composition, effective support/query sizes, selected reference layers, and reference dimensions?

  3. What does ReSuff add beyond established kernel conditional-moment methods, conditional-independence representation regularizers, and a simpler frozen-feature preservation or distillation objective?

Reviewer_62PjOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper asks whether downstream adaptation of EEG foundation models (REVE, LaBraM, CBraMod) fully exploits label information present in the frozen pretrained features. A prediction-level "residual-information audit" (Sec. 2.2, Fig. 1) suggests that frozen features can still reduce held-out NLL of adapted logits in some settings. The authors formalize "task sufficiency" of the adapted representation T relative to a fixed compact view U = ρ(H0) (layer-wise mean/std pooling of frozen hidden states, Eq. 7) as I(Y;U|T)=0 (Def. 1). Using label residuals r = Y − E[Y|T], they note (Prop. 1) that sufficiency is equivalent to E[r|U,T]=0, and (Prop. 2) that this is equivalent to the vanishing of the RKHS norm of the residual-weighted mean embedding under a product Gaussian kernel on (U,T) (Eq. 10). In training, each mini-batch is split by subject into support/query sets; a subject-weighted kernel ridge regression on T estimates E[Y|T] on support, and the V-statistic D̂ = tr(E_Q^T W_Q (K_U ⊙ K_T) W_Q E_Q) on query residuals is added to cross-entropy (Eq. 16). Experiments on PhysioNet-MI, Mental Arithmetic, and ISRUC with three seeds report that ReSuff on top of TASTEFUL improves balanced accuracy in all 9 backbone–dataset pairs (avg +2.3 pts, Table 1) and improves FT/Adapter/LoRA/TASTEFUL on REVE (Table 2). A query-MSE control (Table 3) and several diagnostic plots (Figs. 3–5) are offered as mechanistic evidence.

Critical strengths
  1. Clear, well-posed question. Asking whether adaptation leaves usable label information in the frozen backbone is a reasonable and practically relevant framing for EEG foundation model adaptation, where linear probing and PEFT are often unreliable (Table 1 shows dramatic backbone-dependent variation, e.g., LaBraM LP at chance on MA).
  2. Sound population-level formulation. Prop. 1 (residual characterization) and Prop. 2 (characteristic product Gaussian kernel ⇒ zero residual embedding iff conditional mean zero) are correct as stated, given bounded residuals and the cited results (Sriperumbudur et al., 2011; Muandet et al., 2020). Using a joint kernel on (U,T) rather than on U alone correctly avoids cancellation across values of T.
  3. Sensible estimator design choice. Subject-disjoint support/query splitting to avoid trivially small in-sample KRR residuals (Sec. 3.3) and subject-balanced weights (Eq. 12) are thoughtful details that match the subject-independent evaluation protocol.
  4. Plug-in, no inference cost. The regularizer is training-only and is applied to four adaptation strategies (Table 2), with matched architectures/seeds within each pair.
  5. Attempted mechanistic controls. The query-MSE control (Table 3) is the right kind of ablation to separate "fit labels better on held-out subjects" from "absorb information conditional on U", and the authors are commendably candid that diagnostics do not establish exact sufficiency (Sec. 5).
Critical weaknesses
  1. A claimed component of the method is missing from the objective and never evaluated. The abstract, Sec. 1 (l. 58–59), and Sec. 3 (l. 149–150) state that ReSuff includes a "class-conditioned subject-adversarial objective". However Eq. 16 contains only L_CE + λ D̂; the discriminator, its architecture, gradient reversal/weighting, and its loss weight are never defined, yet l. 268–269 refers to "the discriminator" and "the subject loss". It is therefore unclear what was actually trained, and — crucially — whether the reported gains come from the kernel sufficiency regularizer or from subject-adversarial training (which is a well-known source of cross-subject gains in EEG; cf. DANN, Ganin et al., 2016; CDAN, Long et al., 2018). There is no ablation separating the two. This alone makes the paper's central attribution unverifiable.

  2. The empirical estimator does not cleanly target conditional dependence; the query-MSE control is confounded. D̂ in Eq. 15 is a V-statistic: since k_U(u,u)=k_T(t,t)=1, its diagonal contributes Σ_i w_i² ||e_i||², i.e., a subject-weighted query-MSE term. With a minibatch split 67/33 by subject (batch size never reported), the query set is small and this diagonal term may dominate D̂. Hence the distinction drawn in Sec. 4.3 between ReSuff and "query-MSE" may be largely a difference in weighting rather than in conditioning on U. An unbiased (U-statistic, diagonal-removed) estimator, or reporting the diagonal/off-diagonal decomposition, is needed. Furthermore, D̂ also penalizes dependence of residuals on T alone (since the joint kernel includes K_T), which is nonzero whenever the support-fit KRR is misspecified or does not transfer across subjects; minimizing this reshapes T to be "KRR-friendly across subjects", which is essentially an episodic, closed-form meta-learning loss (Bertinetto et al., 2019, R2D2) rather than sufficiency with respect to U. The decisive controls are missing: (a) K_U ≡ 1 (T-only kernel), (b) U replaced by a permuted/random/noise view, (c) U from a randomly initialized backbone. If (a)–(c) yield similar gains, the "task sufficiency" story is not what explains the results. Table 3 covers only one dataset (MA).

  3. Statistical evidence is weak relative to the claims. Only three seeds are used, and standard deviations are frequently comparable to or larger than the gains (Table 1: REVE PhysioNet .641±.009 vs .630±.015; LaBraM PhysioNet .559±.027 vs .548±.025; LaBraM ISRUC .770±.004 vs .765±.004; REVE MA .764±.035 vs .731±.054; Table 2: FT+ReSuff PhysioNet .635±.055 vs .623±.007; LoRA+ReSuff MA .669±.114 vs .633±.022). No paired tests, CIs, or per-subject analysis are reported, yet the abstract states improvement "in all nine" combinations as the headline. With subject-level test sets of modest size, per-subject paired tests (e.g., Wilcoxon over test subjects, or across seeds × folds) are the minimum. Also, ReSuff does not beat the strongest baseline in several cells (e.g., CBraMod PhysioNet: Adapter .577 vs ReSuff .536; CBraMod avg .659 vs PEARL .658 — a tie), so the headline "ranking first among frozen-backbone methods" is fragile.

  4. Hyperparameter selection is internally inconsistent and possibly test-informed. Sec. 4.1 (l. 306–307) sets λ = 0.5 / 0.02 / 0.01 for PhysioNet-MI / MA / ISRUC. Sec. 4.4 (l. 464–468) says REVE and LaBraM peak near λ=0.02 and that "increasing the weight to 0.50 generally lowers BA", yet then states "using 0.50 for PhysioNet-MI". Fig. 4a appears to be on MA only (y-range 0.60–0.76), so the PhysioNet choice is unexplained. λ is per-dataset, not per-backbone, despite Fig. 4a showing backbone-dependent optima. The baseline budget sweeps in Sec. 4.2 (LoRA rank 1–32, Adapter 4–126: "reaches at most 0.506") read like maxima over test BA; please clarify that all selection (baseline budgets, λ, warm-up, epoch/checkpoint) used validation only and that the baselines received an equivalent tuning budget to ReSuff (which has λ, warm-up, support fraction, ridge, and bandwidth as extra knobs).

  5. Missing obvious baselines. (a) Late fusion with U: the simplest way to make the predictor "sufficient relative to U" is to concatenate U (a cheap pooled frozen feature) to T before the head, or ensemble a probe on U — at negligible inference cost for frozen-backbone methods since H0 is already computed. Without this, it is unclear why one should regularize rather than fuse. (b) Fine-tuning regularizers that preserve pretrained information: L2-SP (Li et al., 2018), DELTA (Li et al., 2019, feature-map regularization toward the frozen network), LP-FT (Kumar et al., 2022 — cited, but only for a different point), WiSE-FT (Wortsman et al., 2022), and feature distillation from the frozen backbone. (c) Subject-adversarial alone (see W1). (d) Other kernel dependence regularizers: an HSIC penalty in the style of the HSIC bottleneck (Ma et al., 2020), or a conditional-independence regularizer such as CIRCE (Pogodin et al., ICLR 2023) / HSCIC (Park & Muandet, 2020), which are the natural methodological comparators. Also tPoE-EIB appears in Table 1 without citation or description.

  6. Novelty is limited. Props. 1–2 are direct restatements of the kernel conditional moment / maximum moment restriction framework (Muandet et al., 2020) applied to Y − E[Y|T]; the estimator is a weighted KRR plus a kernel V-statistic, with differentiable closed-form KRR as in Bertinetto et al. (2019). Kernel conditional-independence regularization of learned representations (CIRCE, HSCIC-based counterfactual invariance; Quinzan et al., 2022) and information-bottleneck/sufficiency regularization (e.g., Alemi et al., 2017 VIB; Federici et al., 2020 multi-view sufficiency) are closely related and not discussed. The EEG-specific contribution is the application and the subject-disjoint split; this is a reasonable engineering contribution but would need much stronger empirical evidence to clear the ICLR bar.

  7. Gap between theory and practice is large and not analyzed. The population equivalence requires the true E[Y|T]; in practice T changes every step and the KRR is fitted on a handful of support subjects in one minibatch, with median-heuristic bandwidths that also move with T. No analysis is given of the bias of D̂ due to KRR plug-in error (which can be positive even under exact sufficiency, so the regularizer pushes toward something other than sufficiency), of the effect of the T-dependent bandwidth on gradients (the representation can change D̂ by rescaling its geometry), or of the variance with small query sets. Also, sufficiency relative to U is trivially attainable for frozen-backbone methods (T could contain U), so the constraint in Eq. 3 is weak; the paper should discuss why the regularized optimum is not just "copy U into T".

  8. Motivational audit is under-specified. "SPLINCE" (Sec. 2.2) is neither defined nor cited; the correction construction, permutation control, and statistics behind Fig. 1 are not given. Fig. 1 also uses CSBrain and FACED, which are not in the main experiments; and the authors acknowledge it doesn't test sufficiency. The case studies in Fig. 5 / Sec. 4.3 are qualitative and on cached checkpoints different from the selected ones.

  9. Reproducibility and completeness. The Reproducibility Statement promises supplementary "data preprocessing and splits, implementation settings, hyperparameters, random seeds, and diagnostic procedures", but the appendix contains only Fig. 5 and a Related Work section that ends mid-sentence ("encouraging the adapted representation to account"). Missing: number of subjects per split, what "limited-label" means (label fraction? per-subject trial budget?), batch size, epochs, optimizer, learning rates, which layers form U, dimensionality of U, how the support/query split handles batches with few subjects, number of query subjects, compute/memory overhead (FT requires a second frozen copy of the backbone plus an O(n³) solve per step), and code availability. Training overhead is never reported despite the "practical plug-in" claim.

Minor Issues

  • Template residue: l. 506 "things that can be referenced in the reproducibility statement."; Author Contributions and Acknowledgments sections contain the ICLR template placeholder text.
  • Related Work (Appendix A) is truncated mid-sentence; key related work (HSIC bottleneck, conditional-independence regularizers, fine-tuning regularizers, BIOT, EEGPT) is absent.
  • Fig. 4c legend reads "KST" rather than "ReSuff" (apparent leftover name).
  • Sec. 4.3 "As shown in Fig. 3c, NLL decreases markedly", but Fig. 3c plots normalized residual dependence, not NLL, and shows only two time points (epoch 0 and 10) with a very wide band.
  • l. 268 "The subject loss is" — presumably "The overall loss".
  • Spacing typos: "ReSuffacross", "itsReSuff -augmented", "ReSuffon", "ReSuffis is used" (l. 283–309).
  • Sec. 4.2 reports relative improvements (2.2%, 2.1%, 6.3%) while abstract reports absolute points; be consistent.
  • ISRUC is omitted from Table 2 without explanation; Table 3 covers MA only.
  • Fig. 3b is hard to read (dual axes, small font) and its message ("overall change was not so significant", l. 425) undercuts the claim.
  • Kumar et al. (2022) is cited for "learning task-specific predictions while generalizing across subjects", which is not what that paper is about.

Justification of Rating

The population-level idea is correct and cleanly motivated, but it is a direct application of known kernel conditional-moment machinery, so the paper's value rests on demonstrating that the specific sufficiency-relative-to-U mechanism yields reliable gains. The current evidence does not do that: a described component (subject-adversarial training) is missing from the objective and unablated, the V-statistic estimator contains a query-MSE term that confounds the key control, the essential U-ablations and a simple U-fusion baseline are absent, the gains are mostly within one standard deviation over three seeds with no significance testing, hyperparameter choices contradict the sensitivity study, and the promised appendix details are missing (with truncated related work and template residue). I would reconsider the paper, potentially moving toward weak acceptance, if the authors clarify and ablate the adversarial component, show that gains vanish when U is permuted/randomized (and persist with a U-statistic estimator), beat a U-concatenation baseline and standard fine-tuning regularizers, and provide paired significance across more seeds/subject folds with full implementation details and overhead. If the adversarial term or a T-only kernel accounts for most of the gain, this would further strengthen my concerns.

Questions for authors
  1. Exactly what objective was optimized in the reported experiments? Is the class-conditioned subject-adversarial loss used, with what weight and architecture? Please provide results for (i) CE + D̂ only, (ii) CE + adversarial only, (iii) both, on all three datasets.
  2. Please report results with the diagonal-removed (U-statistic) estimator and the diagonal/off-diagonal decomposition of D̂ during training. How large is the query set per batch?
  3. Please report ablations with K_U ≡ 1, permuted U, and U from a randomly initialized backbone. If the gains persist, how do you reconcile this with the sufficiency interpretation?
  4. How does ReSuff compare to simply concatenating U to T before the head (and to L2-SP/DELTA/LP-FT/WiSE-FT for full FT)?
  5. How was λ = 0.5 for PhysioNet-MI chosen given that Sec. 4.4 reports 0.5 lowering BA? Was every hyperparameter and checkpoint chosen on validation subjects only? What tuning budget did baselines receive?
  6. Can you provide per-subject paired significance tests and more seeds (≥5) or multiple subject-split folds?
  7. What is the wall-clock and memory overhead per epoch relative to each baseline, especially for full fine-tuning?
  8. What is SPLINCE, and how exactly is the Fig. 1 audit computed? What is tPoE-EIB?
  9. What is the label budget defining "limited-label", and how do the results change as the label budget grows (does the benefit vanish with more labels, as the motivation would predict)?

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