- Rating
- 3(+1)
- Confidence
- 4
- Informativeness
- 2
- Presentation
- 1
- Soundness
- 3
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Paper summary
The paper looks at the issue that when you take a pre-trained EEG foundation model and apply it to a new EEG headset, such as one with 128 or 256 sensors, the model doesn't know where the new sensors are located on the scalp (as it has never seen this headset during training). Instead of training new sensor-position embeddings from scratch (which LaBraM (which is an EEG Foundation Model) normally does on unseen sensors) or interpolating the raw brainwave signals, the authors took LaBraM’s pre-trained lookup table of 90 standard sensor positions and calculated the embeddings for new sensor locations by taking a distance-weighted average of the 4 closest known sensors. They also plugged this same 90-sensor lookup table into other foundation models (CBraMod, CSBrain, LUNA, REVE). Finally, they bundled this with two standard training tricks, channel dropout + Gaussian noise and reweighting losses of random mini-batch subgroups, and called the whole package RADAR. The paper further presents a first-order analysis contrasting independent embedding tables with shared coordinate encoders, along with stability and approximation bounds for the remapped initialization.
For validation the authors use a cross-subject protocol (5 folds × 3 seeds) on three high-density datasets (HGD, MAMEM1, and CCD for both classification and regression) and five low-density benchmarks. Within each backbone, the authors compare the native positional encoding, a REVE-style coordinate encoding, and SPR. SPR improves average classification on LaBraM (62.5 to 69.6 balanced accuracy), CBraMod, CSBrain, and LUNA, and is roughly neutral on REVE. Ablations cover frozen versus trainable embeddings, random and unaligned pre-trained tables, signal-level and ROI remapping, alternative remapping rules, and a linear probe that decodes electrode coordinates from the remapped embeddings.
Critical strengths
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The method is simple and practical, which makes it interesting and quite useful to consider for other models as well. SPR reuses LaBraM’s pre-trained electrode table to initialize embeddings for unseen electrodes through spherical distance-weighted interpolation. It requires no additional pre-training. Because the remapping acts only on positional parameters, all recorded high-density channels are retained. On LaBraM, SPR outperforms signal-level remapping to LaBraM’s 90 positions (69.6 vs. 66.3 average balanced accuracy for Signal-NN, Table 11 --> average column).
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Informative analysis of positional content is very insightful, and the authors give a clear input into what is happening. The Random PE, Unaligned Pretrained PE, and SPR controls help separate the contributions of pre-trained content and geometric alignment. By comparing SPR against Random PE and Unaligned Pretrained PE controls (Section 4.3), they cleanly separate the benefits of independent vector parameterization, pre-trained content, and geometric alignment. Furthermore, the linear coordinate probing experiment against Random and Shuffled controls (Section 4.5, Table 8) demonstrates that LaBraM’s pre-trained positional table encodes linearly decodable 3D scalp geometry (– error vs. for controls). This is consequential because it validates the paper's core premise: pre-trained electrode tables contain genuine, transferable spatial structure rather than merely serving as arbitrary channel identifiers.
Critical weaknesses
- While Table 1 reports a +7.1 percentage point average gain on LaBraM (62.5% to 69.6%) and +1.6 to +2.2 points on CBraMod, CSBrain, and LUNA, I have found three experimental confounds that weaken the claim that these gains stem from transferring pre-trained spatial knowledge, I present this as one weakness as it all connects to these numbers presented in table 1.
- The LaBraM baseline is artificially low. Appendix E.8 reveals that "Native LaBraM" replaces the entire positional table with random vectors on high-density datasets, even on HGD, whose standard 10-20 electrode names partially overlap with LaBraM's vocabulary. Furthermore, Table 13 shows that simple nearest-neighbor copying (K=1) already recovers nearly the entire gain on HGD (0.664 to 0.723, vs. 0.727 for SPR) and most of the gain on MAMEM1 (0.447 to 0.541, vs. 0.579 for SPR), leaving only ~0.4 and ~3.8 points attributable to the distance-weighted interpolation itself.
- Integrating SPR into non-LaBraM models modifies their architectures (Appendix E.8), removing positional convolutions in CBraMod and CSBrain and bypassing LUNA’s coordinate branch. Table 5 shows that simply applying this architectural change with random independent vectors (Random PE) already accounts for a large fraction of the gain over Native (CBraMod: 0.586 Native --> 0.590 Random PE --> 0.603 SPR; CSBrain: 0.570 --> 0.581 --> 0.586; LUNA: 0.501 --> 0.526 Random PE vs. 0.523 SPR, where pre-trained content provides zero benefit). Meanwhile, on the strongest coordinate-based backbone (REVE), SPR slightly degrades performance (0.659 to 0.656).
- For HGD (14 subjects) and MAMEM1 (11 subjects), each of the 5 folds holds out only a single test subject (Appendix E.1). Thus, only 5 subjects per dataset are ever evaluated (repeating 3 seeds adds no independent test data), and the cross-backbone gains (~1-2 points) are an order of magnitude smaller than the fold standard deviations, with no statistical significance tests reported.
- The paper packages a straightforward engineering heuristic (spherical 4-NN average of lookup-table embeddings) in heavy abstraction and pairs it with unrelated training tricks that do not consistently help. One thing that stood out to me was that the paper writing is quite dense and the prose can be heavily simplified to improve readability. Throughout the paper, simple operations are obscured behind inflated terminology (e.g., "functionally leveraged," "better unleashing the decoding potential," "preserving high-fidelity spatial semantics") rather than stating the concrete mathematical operations upfront. An example of this is the fact that elementary derivations are framed as a "theoretical basis". Equations 1, 4, and 6 are standard textbook properties, a first-order chain-rule step under Euclidean SGD (whereas all experiments use AdamW, which preconditions coordinates), the non-expansiveness of a row-stochastic matrix, and the triangle inequality under Lipschitz continuity with unobservable reference discrepancy . Moreover, Appendix B.1 explicitly concedes that Eq. 1 imposes no performance ordering between tables and coordinate generators, contradicting Section 3.1's use of Eq. 1 to motivate choosing independent tables.
Questions for authors
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Appendix E.8 states that Native LaBraM replaces the entire positional table with random vectors on high-density datasets, yet Appendix E.6 notes that HGD uses standard electrode names that partially overlap with standard montages. Why does the Native LaBraM baseline not retain name-matched pre-trained embeddings for the overlapping standard 10-20 channels on HGD? What is LaBraM's performance on HGD when overlapping channels retain their pre-trained vectors and only unseen channels are randomly initialized?
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Please confirm whether Random PE in Table 5 uses the exact same modified integration interface as SPR (i.e., with positional convolutions removed in CBraMod/CSBrain and the coordinate branch bypassed in LUNA, Appendix E.8). Given that Random PE already accounts for most of the gain on CSBrain (0.570 to 0.581 vs. 0.586 for SPR) and outperforms SPR on LUNA (0.526 vs. 0.523), and given that only 5 test subjects are evaluated across the 5 folds on HGD and MAMEM1, can the authors provide paired statistical significance tests (e.g., across all subjects via leave-one-subject-out, or across the existing folds) comparing SPR directly against Random PE?
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Table 6 shows that adding STR+DRO to SPR degrades average classification performance on LUNA (0.523 for SPR vs. 0.509 for RADAR) and that full RADAR underperforms Native + STR + DRO on REVE (0.654 vs. 0.691). Furthermore, Appendix E.3 states that DRO hyperparameters are tuned per task on validation data, giving RADAR a larger hyperparameter search budget than SPR or Native baselines. Finally, Appendix C.3 acknowledges that randomly partitioning a shuffled mini-batch does not target meaningful subpopulations and relates the objective to tilted ERM. Can the authors please clarify (a) whether SPR/Native baselines received an equivalent hyperparameter tuning budget, and (b) why random-batch tilted ERM is framed as "Distributionally Robust Optimization" rather than evaluated as true Group DRO over the known training subject identities?
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This is more of a future work request here, but Signal-NN and Signal-KNN4 (Table 11) compress 128/256 channels down to 90 channels, confounding interpolation quality with channel reduction. Comparing against classic spherical spline interpolation (Perrin et al., 1989) and evaluating whether SPR's gains persist on Large/Huge foundation model checkpoints would be valuable extensions for future work.
11 comments
Response to Reviewer 6Xc9 (Part 2/7): HGD Baseline & PE Interface [W1, Q1, Q2]
2. Addressing the Three Confounds in Table 1 [W1, Q1, Q2]
2.1 Revised HGD Baseline and K=4 vs. K=1 Remapping [W1, Q1]
"Why does the Native LaBraM baseline not retain name-matched pre-trained embeddings for the overlapping standard 10-20 channels on HGD? What is LaBraM's performance on HGD when overlapping channels retain their pre-trained vectors and only unseen channels are randomly initialized? ... Furthermore, Table 13 shows that simple nearest-neighbor copying (K=1) already recovers nearly the entire gain on HGD ... and most of the gain on MAMEM1..."
Our initial pipeline reinitialized the full table whenever a layout exceeded LaBraM's standard set. We agree that retaining overlapping channels on HGD is a fairer Native baseline and will adopt it in the revision. Under LOSO, retaining the 78 matched channels lifts LaBraM from 70.43% to 73.70%, while interpolating the 50 unseen channels via SPR further raises accuracy to 76.34% (p = 0.002/0.002, improving 13 of 14 subjects). Even against a strong baseline that already preserves every available standard anchor, SPR still extracts consistent gains across nearly every subject from the remaining unseen electrodes, demonstrating that it reliably extends pretrained spatial priors to new sensor locations.
For Table 13 under our original 5-fold evaluation, both K=1 and K=4 retain exact source vectors at matched electrodes, differing only at unseen locations. While K=1 snaps each unseen electrode discontinuously to a single nearest anchor regardless of direction, K=4 triangulates across four surrounding anchors via a parameter-free distance softmax with zero extra trainable parameters. On HGD, 78 of 128 channels match source anchors identically under both rules and the remaining 10-5 sites sit tightly within the 10-20 grid, leaving limited room between K=1 and K=4 even though K=4 still leads. On MAMEM1, however, GSN-256 sensors deviate substantially from the 10-20 montage with zero exact matches, where single-anchor copying suffers spatial quantization error (54.1%) and uniform 4-neighbor averaging blurs local geometry (53.7%). Distance-weighted K=4 raises accuracy to 57.9%, outperforming K=1 by 3.8 percentage points and uniform K=4 by 4.2 points (accounting for nearly 30% of the total 13.2-point improvement over the 44.7% baseline). That K=1 already captures coarse anchor transfer as the simplest case of geometric reuse does not diminish the clear value of distance-weighted K=4, which consistently leads across layouts and delivers a substantial 3.8-point gain on non-standard 256-channel montages at zero extra parameter or training cost.
2.2 Interface Confirmation and Pretrained Spatial Content [W1, Q2]
"Please confirm whether Random PE in Table 5 uses the exact same modified integration interface as SPR ... Table 5 shows that simply applying this architectural change with random independent vectors (Random PE) already accounts for a large fraction of the gain over Native..."
We confirm that Random PE in Table 5, Table 9, and the LOSO table uses the exact same modified interface as SPR (Appendix E.8), removing positional convolutions in CBraMod and CSBrain and bypassing LUNA's coordinate branch under identical parameter counts and training settings.
Under the exact same modified interface and parameter count, full-cohort LOSO confirms that switching to random independent vectors (Random PE) brings no reliable gain over Native, whereas initializing that interface with SPR's remapped priors improves accuracy across all five backbones on both datasets. Specifically, replacing Native modules with Random PE slightly lowers accuracy on CBraMod and CSBrain on HGD, degrades REVE on both datasets, and barely moves MAMEM1 elsewhere, showing that an independent-vector interface alone cannot unlock high-density decoding. Initializing that same interface with SPR overturns the minor 5-subject fluctuations in Table 5 and delivers up to 6 percentage points of gain over Random PE. Consistent with our low-density benchmarks where SPR beats Random PE in 24 of 25 pairs (Table 9), SPR turns mere layout compatibility into effective spatial prior reuse without extra pretraining.
Response to Reviewer 6Xc9 (Part 3/7): Statistical Power & STR/DRO [W1, W2, Q2]
2.3 Cross-Subject Variance vs. Paired Statistical Power [W1, Q2]
"...and the cross-backbone gains (~1-2 points) are an order of magnitude smaller than the fold standard deviations, with no statistical significance tests reported."
Subject-level standard deviations reflect intrinsic inter-subject differences rather than method instability. While HGD subjects are relatively stable (subject-level SD around 5% to 9%), MAMEM1 exhibits extreme subject-to-subject spread (subject-level SD around 10% to 26%), where Subject 9 exceeds 90% accuracy whereas on Subject 8 every model and method barely exceeds 30% and most hover near 20%. Evaluating all variants on the exact same held-out subjects cancels these large subject-specific offsets. Once paired by subject, SPR improves mean performance across all 20 baseline comparisons in the LOSO table, reaching dual parametric and non-parametric significance in 11 of 12 comparisons across the three electrode-level backbones without target-layout pretraining exposure (LaBraM, CBraMod, and CSBrain) and in 8 of 10 comparisons across all five backbones on HGD.
Overall, 13 of the 20 comparisons are significant under both tests, and the remaining cases on REVE, LUNA, and MAMEM1 reflect clear pretraining, architectural, and sample-size boundaries rather than ineffective transfer. On REVE, SPR achieves a highly significant +5.62-point gain over Random PE on HGD () and a +6.02-point gain on MAMEM1, confirming that SPR effectively injects valid spatial priors into REVE, whereas the narrower margin over Native simply reflects REVE's stronger 25,000-subject pretraining with direct exposure to HGD and HBN GSN-128 layouts (Appendix E.6), which already endows Native REVE with target-layout priors (and SPR still edges it out on both datasets). On LUNA, compressing 128 or 256 sensors into fixed latent queries via early cross-attention (Section 2) alongside weaker baseline capacity (~32% on 5-class MAMEM1) attenuates fine-grained positional differences, although SPR still significantly beats Native on HGD (). Finally, MAMEM1's small cohort (, 1,081 trials total in Table 2) inherently caps paired statistical power even when mean gains are substantial, such as +6.02 points on REVE and +3.27 points on CSBrain.
3. Practical Motivation and Modular Role of STR and DRO [W2]
"The paper packages a straightforward engineering heuristic (spherical 4-NN average of lookup-table embeddings) in heavy abstraction and pairs it with unrelated training tricks that do not consistently help."
Our inclusion of STR and DRO is driven directly by practical downstream adaptation needs rather than bundling unrelated tricks to inflate a headline score. As described in Section 3.3, we introduce them for two concrete practical reasons. First, when adapting EEG foundation models in practice, researchers rarely rely on a single modification in isolation and routinely apply other means of regularization to improve decoding. Evaluating SPR alongside STR and DRO tests whether SPR maintains its spatial advantage when established data- and optimization-level techniques are already active, rather than merely substituting for them, which Table 6 confirms through clear incremental gains over Native + STR + DRO on LaBraM, CBraMod, and CSBrain.
Second, EEG heterogeneity is a fundamental practical bottleneck that spans layout mismatch, signal perturbations, and distribution shifts simultaneously. Combining SPR, STR, and DRO addresses this single root problem from the three orthogonal dimensions of model representation, data regularization, and optimization. Because these three components are strictly orthogonal and decoupled, practitioners are never locked into an all-or-nothing package and can freely enable or disable each module according to their backbone and task. Rather than assuming every auxiliary module helps universally, we report exhaustive ablations across all five backbones to equip researchers with rich empirical priors, clear selection criteria, and direct validation of where each component adds value in practice.
Response to Reviewer 6Xc9 (Part 1/7): Full-Cohort LOSO Evaluation [W1, Q1, Q2]
We are deeply grateful for your time and effort, as your exceptionally thorough and rigorous review has substantially strengthened our work. Below, we first present the full Leave-One-Subject-Out (LOSO) results on HGD and MAMEM1, and then address each specific concern and question in turn.
1. Full-Cohort LOSO Evaluation and Revised HGD Baseline [W1, Q1, Q2]
Following your suggestion, we introduce a new full-cohort Leave-One-Subject-Out (LOSO) protocol with 14-fold evaluation on HGD (N=14) and 11-fold evaluation on MAMEM1 (N=11) across all five backbones under matched settings, so that every subject serves once as the held-out test set. In each LOSO fold, one subject serves as the test set, one subject serves as the validation set, and the remaining N−2 subjects form the training set, yielding an (N−2)/1/1 subject split (12/1/1 on HGD and 9/1/1 on MAMEM1). Each run is repeated across three random seeds (42, 43, and 44) and averaged within each fold before computing cross-subject statistics. Below we report balanced accuracy as mean ± subject-level SD (%) and subject-level two-sided p-values formatted as paired t-test / continuity-corrected Wilcoxon signed-rank test.
*HGD Native LaBraM retains pretrained vectors for all 78 name-matched channels and randomly initializes the 50 unseen channels. †MAMEM1 (GSN-256) has zero name overlap with LaBraM's 10-20 table, so Native equals Random PE.
Notably, once evaluated under the stricter full-cohort LOSO protocol, the minor 5-fold fluctuations disappear and SPR achieves the best mean performance across every single backbone and dataset without exception.