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Paper summary
This paper proposes EMAG, representing the spatial super-resolution of EEG as the anisotropic 4D Gaussian mixture on the brain grid. The model is driven by low-density EEG to the temporal amplitudes of each Gaussian component and rendered from the potential source field to the scalp electrode through differentiable Gaussian kernels. The author contends that this representation possesses both reconstruction performance and potential source space interpretability.
Critical strengths
Interpreting EEGSR as a differentiable mapping from a latent source field to electrode signals provides a more structured inductive bias compared to pure electrode-space networks.
The 4×4 SPD precision matrix, the spherical brain mesh, and the low-density (LD) signal modulation collectively form a complete and computationally feasible architecture.
Critical weaknesses
The methodological novelty is significantly overstated. The original 4D Gaussian Splatting already introduced spatiotemporal Gaussian representations, and 4D-Rotor Gaussian Splatting has also utilized native 4D covariance. The primary modification in EMAG is adapting the existing 4D Gaussian representation to EEG using a Cholesky formulation, a brain mesh, and LD-conditioned amplitudes. While these are reasonable domain-specific engineering efforts, they are insufficient to constitute strong methodological innovation.
The so-called "differentiable splatting/forward model" is essentially evaluating and computing a weighted sum of Gaussian/RBF kernels at electrode coordinates. It does not involve the camera projection, ray integration, occlusion, or alpha compositing typically found in computer graphics. More importantly, this kernel does not incorporate the true EEG leadfield, dipole orientations, tissue conductivity, head geometry, or reference schemes. Therefore, it should be accurately positioned as an empirical geometric prior, rather than an authentic EEG forward model or a reliable source imaging technique.
The current experiments fail to rule out the interpretation that the Gaussian representation is merely a more complex basis function for interpolation. Specifically, the full HD montage is supervised during training, and the primary metrics are calculated including observed channels. This neither validates generalization to unseen locations nor prevents the overall error metrics from being heavily skewed by the easily replicated input channels.
The comparisons with strong baselines lack auditability. Baselines need to be rerun under the exact same trial splits, input masks, normalization schemes, training budgets, and random seeds, rather than mixing in previously reported results from other papers.
Questions for authors
Compared to the original 4D-GS and 4D-Rotor GS, which core mechanism is mathematically novel, rather than merely migrating existing 4D covariance or Gaussian rendering techniques to EEG?
If this method indeed learns a meaningful source field, can it be rigorously compared against quantitative localization baselines (e.g., true leadfield/BEM forward models, MNE/sLORETA, or known stimulation sites), instead of solely relying on qualitative visualizations showing Gaussians near stimulated regions?
Please report evaluation metrics computed only on unobserved electrodes, and conduct tests with permanent electrode position holdouts or cross-montage evaluations.
Please rerun all strong baselines under a unified protocol and report the variance and statistical significance.
3 comments
Response (2/2)
W3 / Q3 — Is EMAG just an interpolation basis? Metrics on unobserved electrodes.
A: Several controlled experiments test the interpolation hypothesis directly:
- Adding explicit interpolation does not help. Feeding the model a spherical-spline-interpolated HD input instead of the raw LD input gives no improvement (Table 2, App. F.4).
- A pure interpolator is much worse. Non-learned spherical-spline interpolation of the LD montage performs far worse than EMAG (App. D.1, Table 4).
- A black-box mapping is worse. A capacity-matched electrode-space MLP, which can represent any interpolation scheme, doubles NMSE on Localize-MI (Table 2).
- When EMAG is allowed to interpolate, it gets worse. With free-floating centers, components migrate to the scalp next to the LD electrodes and act as local interpolators, and performance drops (App. F.3). The brain-anchored grid is what prevents this.
Reporting over all HD channels follows the convention of SRGDiff and its baselines (App. B), keeping our numbers directly comparable; these baselines do not publish unobserved-electrode metrics, so no like-for-like comparison exists in the literature. As requested, we computed NMSE on the unobserved electrodes only (mean over five split seeds):
| Dataset (2× / 4× / 8× / 16×) | All channels | Unobserved only |
|---|---|---|
| Localize-MI | 0.087 / 0.105 / 0.140 / 0.214 | 0.105 / 0.123 / 0.157 / 0.227 |
| SEED | 0.156 / 0.280 / 0.424 | 0.305 / 0.369 / 0.478 |
| SEED-IV | 0.119 / 0.208 / 0.340 | 0.229 / 0.274 / 0.382 |
On the dense 256-channel montage the cost of excluding observed electrodes is small, and EMAG's unobserved-only NMSE on Localize-MI remains below SRGDiff's published all-channel NMSE at every factor (0.145 / 0.238 / 0.296 / 0.346). On the 62-channel caps the difference between the two metrics is larger, because a larger fraction of the electrodes is observed (half of them at 2×). This applies to any method under the all-channel convention, including the baselines.
W4 / Q4 — Baseline protocol, variance and statistical significance.
A: We agree that a fully re-run comparison is the ideal, and we took several steps toward it. SRGDiff's code is public, but its exact train/test split and trained weights are not, so its published numbers cannot be reproduced sample for sample. We therefore followed SRGDiff's published protocol as closely as possible: the same datasets, SR factors, random 80/20 split, uniform random LD subsampling and metrics (App. B). The only element we cannot match is their specific random draw of the split. The unavailability of a split file should not prevent comparison with published results; comparing under a matched protocol is standard practice.
To rule out a favorable split, we follow the common practice of using multiple seeds: five independent split seeds per setting (SRGDiff reports a single split). Seed-to-seed variability is very small (std ≤ 0.0024 NMSE in every setting). A one-sample t-test of the five EMAG runs against SRGDiff's published values shows that EMAG's improvement is statistically significant in every setting where it leads, on all three metrics: p < 10⁻⁷ on Localize-MI at every factor, p < 3·10⁻³ on SEED at 2× and 4×, and p < 7·10⁻³ on SEED-IV at 2× and 4×. At 8× on the 62-channel caps, SRGDiff remains ahead, as reported transparently in the paper (Sec. 4.2).
In addition, we evaluated a further strong baseline, the 380M-parameter EEG foundation model ZUNA, entirely under our own protocol (identical splits, LD electrodes, ground truth and metrics). EMAG outperforms it on every dataset and SR factor (e.g. Localize-MI 4×: NMSE 0.105 vs 0.467; SEED 2×: 0.156 vs 2.019).
Q2 — Quantitative comparison of the learned sources.
A: We agree with the reviewer that a rigorous source-localization claim would require such comparisons, and this is why we do not claim that EMAG recovers the true neural sources. EMAG is trained without any source supervision. The paper says only that high-amplitude components "cluster near the known stimulation sites" (Sec. 6). In App. H.1 we explicitly state that this "is not precise localization" and that intracranial stimulation drives network-level propagation, so the scalp signal reflects multiple regions. Our goal there was to check whether the learned representation shows any correspondence with real sources. A rigorous comparison with MNE or sLORETA would require subject-specific head models, beyond the scope of a super-resolution paper.
We are grateful for the reviewer's rigorous feedback, which led to the unobserved-electrode evaluation, the significance tests and the ZUNA baseline. We hope these address the reviewer's main concerns, and would sincerely appreciate it if the reviewer would reconsider the score.
Thank you for the clarifications and additional experiments. I appreciate the unobserved-electrode evaluation and the clarification that EMAG does not recover validated neural sources. However, several concerns remain unresolved. First, evaluating electrodes absent from the test input is different from evaluating positions permanently excluded from training supervision. The added results address the former, but the requested permanent electrode holdout or cross-montage evaluation remains missing. Second, the explanation that the larger metric gap on the 62-channel datasets arises from a larger observed-electrode fraction appears inconsistent with the stated super-resolution factors: at 2×, approximately half the electrodes are observed in both the 62-channel and 256-channel settings. Please clarify this discrepancy. Finally, I still think that what you are doing now is merely applying a mature method to EEG, and you haven't demonstrated where the difficulties lie in its application to EEG, or what difficulty of EEG super-resolution you solve.
Response (1/2)
We thank the reviewer for the detailed and rigorous review, and for recognizing that a source-field-to-electrode mapping "provides a more structured inductive bias compared to pure electrode-space networks" and forms "a complete and computationally feasible architecture". We address each point below.
W1 / Q1 — What is novel relative to 4D-GS and 4D-Rotor?
A: We agree that the 4D Gaussian primitive is not ours, and we do not claim to have invented Gaussian splatting or 4D Gaussians. We credit 4D-GS and 4D-Rotor and describe their 4D covariance explicitly (Sec. 1–2). Our contribution is the first use of the Gaussian-splatting analogy for EEG, together with the adaptations required to make that analogy work in the EEG domain. Transferring an established technique to a new domain, with the adaptations that domain requires, is a well-recognized form of contribution: the Vision Transformer (Dosovitskiy et al., ICLR 2021) brought the NLP Transformer to images with minimal architectural change, and diffusion-based EEG-SR methods, including SRGDiff, adapt diffusion models from vision. Our adaptations are:
Each adaptation is validated by ablation (Table 2, App. F).
W2 — Is the Gaussian rendering a forward model?
A: We agree that EMAG is not a biophysical forward model, and the paper positions it this way. Sec. 1 describes the renderer as "a physics-inspired surrogate that encodes the core volume-conduction inductive bias, a smooth distance-decaying source-to-sensor projection, rather than an exact biophysical head model". We use the term physics-inspired consistently (Sec. 2, 4.4, F.5, 6).
The simplification is deliberate, and its structure matches EEG physics:
We also tested the physically derived alternative directly: replacing the Gaussian kernel with a fixed three-shell spherical leadfield on the same grid performs markedly worse on both datasets (Table 2, App. F.5). Where the paper uses "forward model", it refers to this learned source-to-sensor mapping in the generative sense, not to a biophysical leadfield.
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