acceptodds
Under review as a conference paper at ICLR 2027

Beyond Accuracy: Robustness, Interpretability and Expressiveness of EEG Foundation Models

Abstract

EEG foundation models (EEG-FMs) have been evaluated predominantly on clean, in-distribution accuracy, demonstrating modest gains over supervised baselines and weak frozen representations. This study examines whether these conclusions hold beyond clean accuracy by evaluating six EEG-FMs and a supervised baseline across ten datasets along three layers of analysis: (i) Robustness: we apply test-time perturbations including additive noise, random and region-based channel dropout and region-specific noise injection. Our analyses show that no single model dominates all failure modes. The most noise-robust model is among the most fragile under channel dropout and much of the dropout fragility disappears when channels are removed rather than zero-padded. (ii) Interpretability: using attribution methods in EEG-FMs, we show that models broadly concentrate relevance on task-appropriate brain regions consistent with known neurophysiology. (iii) Expressiveness: we demonstrate that the poor head-only performance previously attributed to low-quality pre-trained representations is largely explained by the pooling strategy and that EEG-FMs possess sufficient representational capacity when their token-level embeddings are preserved. Furthermore, with block-wise probing and attention analysis we show that late blocks are repurposed during fine-tuning, while early blocks already hold task-related information. Our results show that conclusions about EEG-FMs depend on evaluation choices and we recommend that future evaluation of EEG-FMs should report robustness per perturbation type, produce attribution maps and examine multiple pooling strategies.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Electroencephalogram (EEG), Brain-Computer Interfaces (BCIs), Foundation Models, Representation Learning

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_GCboOpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
Read review
Paper summary

The paper evaluates EEG foundation models through corruption robustness, attribution maps, and frozen-feature pooling experiments. Across multiple datasets, it shows that missing-channel handling affects robustness and that preserving token-level features improves frozen-probe performance.

Critical strengths
  1. Practically useful robustness analysis. Comparing perturbation types and channel removal versus zero-padding exposes failure modes that clean accuracy misses.
  2. Substantive pooling findings. Flattening improves average frozen-feature performance for all five tested models across four tasks. Block-wise probes further demonstrate the importance of readout choice.
Critical weaknesses
  1. Robustness rankings require stronger controls. BrainOmni’s noise bandwidth differs from that of other models (Appendices C/D.1), so equal total SNR does not ensure matched corruption in their shared frequency range. Moreover, one dropout mask per dataset/probability is reused across folds (D.2), leaving uncertainty across missing-channel patterns unmeasured.
  2. The pooling explanation exceeds the controls. Mean-tile matches parameter count but not independent feature dimensions or token-specific linear weights. The results establish readout sensitivity, but do not fully separate information preservation from probe capacity and optimization. Appendix G’s end-to-end scratch models also do not isolate pre-training’s contribution to frozen features.
Questions for authors
  1. Does BrainOmni retain its noise advantage under a common physical corruption, with matched spectral content and amplitude before model-specific preprocessing?
  2. Are dropout rankings and removal-versus-padding gains stable across independently sampled masks?
  3. Do flattening gains persist with dimension-controlled readouts and validation-tuned regularization? How do frozen random backbones perform with the same readouts?
4 comments
AuthorsOpenReview ↗

Response to Reviewer GCbo

We thank the reviewer for their constructive comments. We address every point with new evidence and clarifications.

BrainOmni Robustness Analysis. We agree with the reviewer that BrainOmni’s noise bandwidth differs from that of other models, steming from the model's original higher bandpass filtering (0.1-96Hz) compared to the default pipeline (0.5-45Hz) as stated in Appendix C. In the original paper, we demonstrate that under pink noise (1/f), a fairer comparison in the shared frequency range, BrainOmni leads in robustness (we refer the reader to Table 13 of the revised manuscript). During the rebuttal period, we repeated the robustness analysis of BrainOmni under three settings: (i) bandpass at 0.1-96Hz and original white noise (original manuscript result), (ii) bandpass at 0.1-96Hz and restricted white noise 0.5-45Hz (same as all other models) and (iii) fine-tuned on bandpass 0.5-45Hz and noise on the same range (same fine-tuning and testing as the other models but unfair to BrainOmni's original preprocessing setup). We report the drop from the clean performance for all three settings across 6 levels of noise (mean of 8 datasets, excluded the Sleep datasets as mentioned in the original manuscript) and Wilcoxon pairing test between BrainOmni and our deep learning baseline EEGNet (* denotes p<.05). The results of this analysis are reported in the table below:

SNREEGNetOriginal ManuscriptNoise Restricted to 0.5-45HzFine-Tuning and Noise to 0.5-45Hz
10dB-0.9-0.6-1.3-1.2
5dB-3.3-1.6-2.5-2.6
0dB-7.2-3.2 (*)-5.2 (*)-4.8 (*)
-3dB-9.8-4.8 (*)-7.4 (*)-6.9 (*)
-5dB-11.9-6.3 (*)-9.1 (*)-8.6 (*)
-15dB-22.7-16.8 (*)-18.8 (*)-17.9 (*)

As seen from the table above as well as Figure 13 in the revised manuscript (we refer the reviewer to Appendix H.1.1 for the complete analysis), BrainOmni keeps its robustness lead under matched spectral content. Therefore, our observations are fair. We thank the reviewer for pointing out this unmatched tested conditions that this new ablation study (in Appendix H.1.1 of the revised manuscript) clearly answers.

AuthorsOpenReview ↗

Response to Reviewer GCbo (2/3)

Sampled Masks We thank the reviewer for their observation of the reused mask (this was the result of the random channel selection process). To answer the question on how robust the ranking across masked selections is, during the rebuttal period we repeated the channel droppout analysis with two more different seeds (leading to two more random masks) under two settings: (i) Zero-padding the missing electrodes and (ii) Removing the missing electrodes. The various masks are described in Appendix D.2 of the revised manuscript.

As shown in the Tables below (reporting performance in bacc mean ± std over three mask seeds), the ranking between the original reported results and under three different seeds remains largely the same in both settings (with the exception of EEGNet and BrainOmni in the zero-padding setting). These results have been updated in the revised manuscript.

Zero-Padding, p = 0.5, Full-fine Tuning

ModelEyesPhysionet MIPhysionet MEKU MIHGPavlovKU ERPSienaAvgRank (seed avg)Rank (original paper)
REVE-2.7 ± 3.3-4.1 ± 0.7-5.0 ± 3.0-5.3 ± 2.9-10.7 ± 3.5-1.0 ± 0.4-18.6 ± 9.8-20.4 ± 7.3-8.5 ± 1.511
LaBraM-3.3 ± 0.2-9.2 ± 4.3-11.0 ± 5.4-9.8 ± 2.5-25.3 ± 4.2-0.1 ± 0.2-19.1 ± 9.8-6.8 ± 0.0-10.6 ± 2.532
EEGNet-6.4 ± 3.6-5.0 ± 0.4-6.0 ± 1.0-13.9 ± 6.7-22.3 ± 3.2-0.3 ± 0.5-17.7 ± 8.0-11.0 ± 5.9-10.3 ± 1.823
CBraMod-3.0 ± 1.8-9.2 ± 2.6-17.2 ± 8.3-15.9 ± 8.6-23.6 ± 7.5-5.8 ± 2.7-16.9 ± 8.5-16.5 ± 8.7-13.5 ± 2.754
NeuroRVQ-7.2 ± 1.3-11.5 ± 1.9-14.7 ± 1.8-14.1 ± 1.6-34.7 ± 0.7-5.9 ± 1.4-15.9 ± 5.5-6.4 ± 3.8-13.8 ± 1.665
BrainOmni-12.2 ± 7.5-12.9 ± 0.4-12.4 ± 2.5-9.2 ± 0.9-18.6 ± 1.8-0.0 ± 0.2-19.7 ± 0.9-13.7 ± 4.1-12.3 ± 0.546

True Removal, p = 0.5, Full-fine Tuning

ModelEyesPhysionet MIPhysionet MEKU MIHGPavlovKU ERPSienaAvgRank (seed avg)Rank (original paper)
LaBraM-0.9 ± 0.2-1.8 ± 0.5-1.5 ± 0.7-3.3 ± 1.9-10.6 ± 5.40.1 ± 0.2-6.7 ± 5.30.9 ± 0.3-3.0 ± 0.911
BrainOmni-0.9 ± 1.1-4.5 ± 1.5-4.6 ± 2.0-2.2 ± 1.8-6.0 ± 1.9-0.3 ± 0.6-2.6 ± 2.0-3.2 ± 1.6-3.0 ± 1.022
REVE-4.0 ± 4.1-2.6 ± 1.0-3.3 ± 1.6-2.6 ± 1.1-8.3 ± 2.8-0.6 ± 0.5-5.5 ± 5.7-2.9 ± 4.5-3.7 ± 0.533
NeuroRVQ-1.7 ± 0.3-4.5 ± 1.2-4.7 ± 0.9-4.0 ± 1.3-16.5 ± 2.1-0.9 ± 0.7-9.0 ± 5.2-4.2 ± 2.9-5.7 ± 1.144
AuthorsOpenReview ↗

Response to Reviewer GCbo (3/3)

Flattening Gains

In the original manuscript, we demonstrate that flatten pooling head-only performance is significantly better than mean pooling performance on the same pre-trained model, demonstrating that mean pooling can discard useful task-related information. Because flattened tokens lead to an increase in the classification head, in our original manuscript we conducted an ablation study (Appendix J) with a parameter-matched control ablation, showing that token information not head size is the leading factor of this increase. Furthermore, our ablation study (frozen backbone and random from scratch analysis) in Appendix G of the revised manuscript demonstrates that pre-training improves performance on average for most models.

To examine the effect of flattening gains with dimension-controlled readouts (as suggested by the reviewer), during the rebuttal period we conducted a readout dimensionality ablation (Appendix J.1 in the revised manuscript). We compare flatten and mean readouts by performing Principal Component Analysis (PCA) to the flattened token representations, projecting them into progressively lower-dimensional spaces. We retain the top k*D (k scale factor and D the dimensionality of mean pool readout) principal components, with PCA fit on the training trials only and train an L2-regularised logistic regression on each projection. The regularisation strength is selected on a 15% validation split and we report test balanced accuracy over 10 subject-wise folds. As shown in Figure 29 in the revised manuscript (we refer the reader to Appendex J.1), performance generally improves with increasing readout dimensionality. More importantly at k=1 corresponding to the dimensionality of the mean pooling readout, all models on all tasks (with the exception of CBraMod on ERP) outperform their respective mean pooling counterparts. This finding further supports our hypothesis that mean pooling discards potentially useful task-related information, limiting head-only performance. Furthermore, we also added a new pooling strategy, namely Time-mean that averages the tokens across the time dimension for each channel individually and retains the spatial dimension. As shown in Table 23 (missing columns are currently running and will be added in the camera-ready version of the paper), time-mean consistently leads to better performance compared to mean-pooling. Our original matched-size comparison, the new dimension-controlled PCA analysis as well as the time-mean pooling result support our hypothesis that mean-pooling limits head-only performance.

We hope that these clarification, extra results and ablation studies satisfy the reviewer's concerns.

AuthorsOpenReview ↗

Follow-Up to Reviewer GCbo

As the discussion period is ending soon, we wanted to kindly follow up on our responses and the revised manuscript, which address the weaknesses and questions raised in your review. We would greatly appreciate it if you could let us know whether these address your concerns.

Reviewer_AET1OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper evaluates six EEG foundation models and EEGNet across ten EEG datasets, extending standard clean-data accuracy benchmarks to robustness, interpretability, and representation expressiveness. It tests robustness to synthetic noise and channel dropout, uses attribution maps to examine whether model relevance aligns with task-appropriate brain regions, and studies frozen representations through different pooling strategies.

Critical strengths
  1. The paper complements existing EEG foundation-model benchmarks by evaluating models beyond clean-data accuracy, across robustness, interpretability, and representational expressiveness. This broader evaluation reveals important limitations of accuracy-only comparisons and provides a useful view of how these models behave under different evaluation settings.  

  2. The expressiveness analysis shows that linear-probe performance can be limited by mean pooling, and that token flattening can mitigate this limitation. This offers practical guidance for using  EEG-FMs.

Critical weaknesses
  1. The robustness analysis relies on synthetic perturbations, including additive noise and channel dropout, without evaluating common real-world disturbances such as muscle artifacts or electrode displacement. Although the results provide useful insights into the tested failure modes, it remains unclear whether the observed robustness patterns generalize to practical EEG recording conditions.

  2. The block-wise probing and attention analyses focus only on REVE and NeuroRVQ, the two best-performing models. Given the architectural and pre-training differences among EEG foundation models, it is unclear whether the conclusions about early representations and the repurposing of later blocks during fine-tuning hold more broadly.

  3. The paper concludes that weak head-only performance is substantially explained by pooling rather than poor pretrained representations. While the parameter-matched control supports the effectiveness of token flattening, flattening also preserves position-specific information and depends on the input token layout. Moreover, the pooling experiments cover only four of the ten tasks. Therefore, the results demonstrate that mean pooling can discard useful information, but do not fully establish that pooling is the primary explanation for weak frozen representations across EEG-FMs more generally. I understand that the scope for additional experiments during rebuttal may be limited, but given that token flattening could increase the risk of overfitting, any additional results the authors can provide would help assess how well this finding generalizes.

Questions for authors
  1. What concrete implications do the robustness and representation analyses suggest for the architecture or pre-training objectives of future EEG foundation models?

  2. Given the related evaluation in OmniEEG-Bench, could the authors clarify how the robustness analyses in this work differ from existing channel-masking evaluations and refine the novelty claim accordingly?

3 comments
AuthorsOpenReview ↗

Response to Reviewer AET1

We thank the reviewer for their constructive comments. We address every point with new evidence and clarifications.

Weaknesses

Regarding the tested robustness conditions, we agree with the reviewer (as also mentioned in the "Limitations section" of our work) that other types of distrubances (such as eye-movement and muscle artefacts or electrode shift and rotation) are not currently captured by this analysis. Nevertheless, the synthetic perturbations done in this work (such as channel dropout or region noise) provide some real-world insights about how these models handle missing electrodes or disturbances in task-related and non-task-related regions, two conditions that can be met in real-life deployments scenarios, for example when models are deployed across EEG headsets with various electrodes or when electrodes are not fitted properly. Although the robustness analysis is not complete (meaning to capture every possible artifact scenario), our goal with this work is to raise awareness to the research community to examine EEG-FMs not only through accuracy metrics but also through different lenses (such as robustness).

In the original manuscript, we included only block-wise probing for REVE and NeuroRVQ as the two best performing models based on our analysis in Section 4.1. As suggested by the reviewer, during the rebuttal period we extended the analysis of block-wise probing to more models namely BrainOmni, LaBraM and CBraMod (we refer the reviewer to Section 4.4 and Appendix of I.5.1 of the revised manuscript). As seen from Figure 4 and Appendix I.5.1 in the revised manuscript, our original assumptions for REVE and NeuroRVQ hold also for all other tested EEG foundation models.

Regarding the head-only analysis, in our work we demonstrate that flatten pooling head-only performance is significantly better than mean pooling performance on the same pre-trained model, demonstrating that mean pooling can discard useful task-related information. Because flattened tokens lead to an increase in the classification head, in our original manuscript we conducted an ablation study (Appendix J) with a parameter-matched control ablation, showing that token information not head size is the leading factor of this increase. In the revised manuscript, we have now conducted a readout dimensionality ablation. We compare flatten and mean readouts by performing Principal Component Analysis (PCA) to the flattened pre-trained token representations, projecting them into progressively lower-dimensional spaces. We retain the top k*D (k scale factor and D the dimensionality of mean pool readout) principal components, with PCA fit on the training trials only and train an L2-regularised logistic regression on each projection. The regularisation strength is selected on a 15% validation split and we report test balanced accuracy over 10 subject-wise folds. As shown in Figure 29 in the revised manuscript (we refer the reader to Appendex J.1), performance generally improves with increasing readout dimensionality. More importantly, at k=1, corresponding to the dimensionality of the mean pooling readout, all models on all tasks (with the exception of CBraMod on ERP) outperform their respective mean pooling counterparts. This finding further supports our hypothesis that mean pooling discards potentially useful task-related information, limiting head-only performance. We hope that the reviewer appreciates these additional experiments during the limited rebuttal period. Furthermore, we also added a new pooling strategy (Appendix J in the revised manuscript), namely Time-mean that averages the tokens across the time dimension for each channel individually and retains the spatial dimension. As shown in Table 23 (missing columns are currently running and will be added in the camera-ready version of the paper), time-mean consistently leads to better performance compared to mean-pooling. Our original matched-size comparison, the new dimension-controlled PCA analysis as well as the time-mean pooling result support our hypothesis that mean-pooling limits head-only performance.

AuthorsOpenReview ↗

Response to Reviewer AET1 (2/2)

Questions

  1. We thank the reviewer for this question. The primary goal of our work is to was raise awareness to the research community that the evaluation of EEG-FMs should be extended beyond accuracy. To that front, we have conducted several analyses in this work that led to several observations (as discussed in the Discussion section) that point to several concrete directions for future EEG-FMs.

(i) Channel-dropout Much of the model fragility disappears when channels are removed instead of zero-padded. This shows that models fail on zero-valued inputs rather than on lost task information. Future architectures should condition on channel identity and represent missing channels explicitly, for instance via mask tokens or attention masking, rather than as zero signals.

(ii) Pre-training objectives REVE is the only tested model pre-trained with channel masking and based on our results it is the most robust under zero-padded dropout. This suggests that masking whole channels during pre-training may result in robustness to missing or faulty electrodes.

(iii) Robustness to noise BrainOmni’s noise robustness to noise needs further investigation that could also guide future EEG-FM training. As already discussed in the manuscript, latent compression of channels and multimodal EEG–MEG pre-training need further investigation.

(iv) Pooling Flatten pooling improved head-only performance for all models. A parameter-matched control ablation (present in the original submission) and the readout dimensionality analysis via PCA (in the revised manuscript) rule out head size as the main cause. This indicates that mean pooling (commonly used in head-only EEG-FM analyses) discards information present in token-level embeddings. Future EEG-FMs should therefore be released with token-preserving or learned aggregation heads.

  1. We thank the reviewer for pointing us to OmniEEG-Bench which appeared as a concurrent preprint close to our submission. We have now cited it in the revised manuscript in the Related Work section. There are several differences between our work and OmniEEG-Bench regarding robustness:

(i) OmniEEG-Bench evaluates robustness through random channel masking only, whereas we test additive white and pink noise at multiple SNRs, random channel dropout, region-based dropout and region-specific noise injection (with primary and control regions defined based on neurophysiology).

(ii) in the overlapped channel dropout setup between the two works, we apply perturbations at test time only to fine-tuned models (using per-channel Bernoulli dropout probabilities) whereas OmniEEG-Bench applies a fixed corruption ratio within linear probing. Additionally, we apply one mask per dataset (different across seeds) while OmniEEG-Bench applies one mask per sample.

(iii) OmniEEG-Bench zero-masks channels. In our work, we test both zero-padding and true channel removal for variable-channel models and demonstrate that much of the dropout fragility disappears under removal. This suggests that zero-masked evaluations partly measure how models handle zero-valued inputs rather than loss of task information.

We hope that these clarification, extra results and ablation studies within the rebuttal's period timeframe satisfy the reviewer's concerns.

AuthorsOpenReview ↗

Follow-Up to Reviewer AET1

As the discussion period is ending soon, we wanted to kindly follow up on our responses and the revised manuscript, which address the weaknesses and questions raised in your review. We would greatly appreciate it if you could let us know whether these address your concerns.

Reviewer_brZiOpenReview ↗
Rating
4
Confidence
4
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies EEG foundation models from the perspective of robustness (impact of different noise sources/types), interpretability (using attribution methods and block-wise probing) and expressiveness (performance of different output sequence pooling strategy). To do so, it compares six existing EEG FMs over 10 datasets across varied paradigms (motor imagery, ERP, sleep, etc.). Results suggest that (1) no model is universally robust and that removing (bad) channels rather than zeroing them generally works better, (2) attribution maps on EEG FMs reveal spatially plausible patterns, suggesting physiological sources for decoding performance, and (3) linear probing with a flattening of the output token sequence, rather than its averaging, recovers a lot of the finetuning performance. Overall, these results highlight the importance of probing other capabilities of EEG foundation models when comparing them.

Critical strengths
  1. The paper presents interesting and timely results that help better interpret existing EEG foundation models, which are commonly tested in noise-free conditions only, and through the lens of downstream performance uniquely. As such, the results are likely to help design better EEG FM pretraining and evaluation pipelines, e.g. by highlighting the importance of the output aggregation strategy on performance. The paper is overall clearly written, with clean analyses and actionable findings.
Critical weaknesses
  1. The text (line 175) mentions the use of Common Average Referencing across all recordings. This step is not included in the original EEG FMs preprocessing pipelines, meaning that the data they receive during downstream evaluation may be out of distribution, at least to some level. Also, using CAR on datasets with sparse montages (e.g. the sleep datasets) may impact performance negatively as the average reference is computed from few electrodes. This mismatch may have an impact on the comparison across models, but also across output token aggregation strategies, as linear probing experiments may suffer more from this distribution shift than experiments where the entire model is allowed to update its weights. Similarly, I wonder whether this may in part explain the poor performance of BIOT, which despite lower performance in existing benchmarks has performed better than chance. Overall, an ablation would be required to ensure CAR is not a confounding factor in these analyses.
Questions for authors
  1. Do the main results (robustness and head pooling strategy) hold if the exact preprocessing pipeline of the original EEG FMs is used?
3 comments
AuthorsOpenReview ↗

Response to Reviewer brZi

We thank the reviewer for their very positive assessment of our paper.

Common Average Referencing (CAR) was applied to establish a fair common preprocessing pipeline for all models. During the rebuttal period, we ran the following ablation study: we repeated the clean performance analysis without CAR, to examine whether that decision interfered with our reported results (favoured any particular model), as suggested by the reviewer (same as "exact preprocessing of the original FMs"). We examined two settings: (i) full-fine tuning and (ii) head-only (head as reported by the original authors) and measured the difference between CAR and no-CAR performance. The results on three tasks (selected for their fast training times during the rebuttal period) are presented below:

Full-Fine Tuning Results

ModelEyesKU MIHGAvg CAR / no-CARΔ = CAR − no-CAR (pp)
LaBraM83.3 / 75.177.5 / 71.162.0 / 59.174.3 / 68.45.83
NeuroRVQ86.1 / 84.180.9 / 79.068.9 / 63.178.6 / 75.43.23
REVE79.9 / 75.382.9 / 78.469.4 / 72.077.4 / 75.32.15
BrainOmni85.2 / 84.875.0 / 75.058.5 / 58.772.9 / 72.90.04
CBraMod82.1 / 79.075.2 / 73.559.4 / 58.872.2 / 70.51.79
BIOT75.3 / 73.450.1 / 50.332.2 / 35.752.5 / 53.1-0.61
EEGNet75.8 / 78.778.6 / 76.462.4 / 61.672.3 / 72.20.06

Head Only Results

ModelEyesKU MIHGAvg CAR / no-CARΔ = CAR − no-CAR (pp)
LaBraM71.7 / 54.550.4 / 49.930.0 / 31.350.7 / 45.25.47
NeuroRVQ73.6 / 70.050.1 / 50.127.1 / 29.850.3 / 50.00.28
REVE79.0 / 76.176.1 / 72.554.4 / 56.069.8 / 68.21.65
BrainOmni82.9 / 83.265.8 / 66.148.1 / 47.965.6 / 65.7-0.15
CBraMod80.9 / 78.965.3 / 62.138.1 / 43.461.4 / 61.4-0.02
BIOT67.9 / 66.950.1 / 49.930.9 / 32.049.6 / 49.60.05

As can be seen from the Table above, applying CAR led to increased or same performance for all models. Therefore, we believe our conclusions are valid and fair. This ablation study has been added to the revised manuscript (we refer the reviewer to Appendix F.1 in the revised manuscript).

We agree with the reviewer that on Sleep CAR might have a bigger impact. We are currently running this experiment (not reported due to its longer training time) and we will report it in the camera-ready version of the paper.

Once again, we thank the reviewer for their positive assessment of our work and its timely significance in the field.

Thank you to the authors for the additional result above; interesting to see CAR having a positive or neutral impact, even under linear probing.

AuthorsOpenReview ↗

To Reviewer brZi

Thank you again for your constructive feedback and positive assessment. We sincerely appreciate your time and careful consideration of our work.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.