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Under review as a conference paper at ICLR 2027

Support Sampling for Montage-Agnostic EEG Source Imaging

Abstract

EEG source imaging (ESI) aims to reconstruct cortical activity from scalp measurements that mix signals generated by multiple sources. This represent a notable ill-posed inverse problem since distinct source configurations can produce similar EEG. Classical methods use a supplied leadfield and explicit assumptions to select a reconstruction, Bayesian methods use a leadfield to infer source uncertainty for each recording, and learned imagers are fast but often return a single estimate for a fixed electrode layout. We introduce a geometry-conditioned imager that estimates parcel waveforms and autoregressively samples sets of active parcels of variable size. By encoding EEG measurements and electrode coordinates in an internal representation, the same model processes different montages without a supplied leadfield, which it predicts directly from geometry. On held-out 256-channel synthetic data, our deterministic estimate improves on the previous state of the art, reducing median localization error by 13.4% to 9.7 mm and increasing AUPRC from 0.749 to 0.787. On real EEG with known intracranial stimulation sites, the full autoregressive model reduces median peak-to-site distance by 15.5% to 22.3 mm relative to the best-performing baseline and achieves a stimulated-parcel AUPRC of 0.090. Trained jointly on four electrode layouts, the imager also generalizes to unseen 21-, 76-, and 256-channel montages, achieving median localization errors of 10.4–16.5 mm compared with 10.6 mm across seen layouts.

Primary area:
applications to neuroscience & cognitive science
Keywords:
EEG source imaging, inverse problems, structured prediction, probabilistic inference, uncertainty quantification, autoregressive models, montage generalisation

Reviews

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1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_keHkOpenReview ↗
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Paper summary

This paper introduces a geometry-conditioned EEG source-imaging model that processes varying electrode layouts without requiring a supplied leadfield at inference. It predicts parcel waveforms and uses an autoregressive decoder to sample variable-size sets of active cortical parcels. Experiments on synthetic data demonstrate improved source localization, support recovery, and transfer to unseen montages. Evaluation on Localize-MI further shows encouraging transfer to real stimulation-evoked EEG.

Critical strengths

Montage-flexible source imaging. The model uses EEG signals and electrode coordinates to handle varying channel counts and unseen layouts with shared parameters, reducing dependence on montage-specific models and externally supplied leadfields.

Structured support uncertainty with strong validation. The autoregressive decoder represents distributions over variable-size active-parcel sets rather than only independent parcel scores. Extensive synthetic experiments, ablations, and real-data evaluation provide encouraging evidence for localization accuracy, montage transfer, and uncertainty quality.

Critical weaknesses

The experiments do not isolate the claimed benefit of autoregressive dependence modeling. OursAR and OursInd learn different marginal inclusion probabilities, and the paper explicitly acknowledges that the comparison therefore establishes only the performance of the complete models. The energy-score difference between them is also small (1.576 versus 1.585). The considerably better excess AURC of OursAR may arise from changed marginals or localization-error distributions rather than learned parcel dependencies. Since autoregressive support sampling is a central contribution, a comparison that controls the marginals—or another direct measure of joint support modeling—is needed to establish that dependencies themselves are consequential.

Questions for authors

Clarification that could affect my assessment: Can the authors provide a baseline that preserves, or is explicitly fitted to, the parcelwise marginals of OursAR while removing dependencies between parcels? Alternatively, can they directly evaluate held-out joint-support likelihood, pairwise co-inclusion quality, cardinality calibration, or another statistic that distinguishes joint modeling from improved marginals?

2 comments

We would like to thank the reviewer for pointing out these aspects. We agree that OursAR and OursInd learn different marginals, so Table 4 only compares complete models (as in Sec. 4.5 and Appendix F). For this reason we followed both of your suggestions, running everything without retraining on the same Table 4 subsets (1k scenarios per simulator, three seeds).

On your first question, we built baselines that keep OursAR's parcelwise marginals exactly and remove the dependencies. For each EEG we start from that EEG's own OursAR draws and either shuffle each parcel's column of the draw matrix independently, which keeps every inclusion frequency and destroys all co-occurrence, or draw each parcel independently with probability π^r\hat\pi_r. We then repeated the excess AURC analysis of Table 4 with these samplers. There, the error is the peak of the point estimate built from the marginals, and EEGs are ranked by the spread of the draw centroids. With the marginals held fixed the errors are identical, so any change comes from the ranking alone:

Excess AURC (mm)
OursAR (fresh draws, 55.18 in Table 4)54.5 ± 1.0
Same marginals, permuted64.0 ± 1.2
Same marginals, Bernoulli64.1 ± 1.6
OursInd (Table 4)83.1 ± 5.1

Removing the dependencies alone costs 9.5 mm (paired bootstrap 95% CI [-11.1, -7.8]), while the mean spread barely moves (10.75 vs 10.69 mm), so the dependencies change which EEGs the model marks as uncertain. Your suspicion is partly right. About two thirds of the gap to OursInd (from 83.1 to 64.0) comes from better marginals, and the remaining third (from 64.0 to 54.5) from the dependencies.

On your second question, we went through the statistics you list, comparing OursAR with the same matched baselines (500 draws per EEG, Brier scores corrected for the finite number of draws, 95% CIs in brackets).

We did not compute held-out joint-support likelihood, because it would not compare the two models fairly. The probability OursAR assigns to a set is a sum over all the orderings that produce it (Eq. 3), which is intractable, and the teacher-forced likelihood of a single ordering is only a lower bound, whereas the likelihood of the independent sampler is exact.

For pairwise co-inclusion, we scored the 45 pairs among the ten most probable parcels of each EEG. Here the dependencies do not help: OursAR minus the matched sampler is +0.0004 [+0.0003, +0.0005] on the pair Brier score. Cardinality calibration is where they matter. On the Brier score of the number of active parcels the difference is -0.0064 [-0.0101, -0.0025] in favour of OursAR, which is consistent with the STOP token learning the count directly, while an independent sampler is tied to a Poisson-binomial count. The energy score, by contrast, differs by only 0.1% (+0.0019 [+0.0008, +0.0030]), because it mostly reflects the marginals, and this is why OursAR and OursInd looked so close in Table 4.

As a further statistic we looked at the calibration of support sets. For each EEG we take the smallest set of top-ranked parcels whose predicted probability of containing the whole true support reaches p, and check how often it actually does. At p = 0.5 OursAR covers at the stated rate (0.53) with a median of 39 parcels, whereas the independent sampler over-covers (0.68) and needs 205 parcels, and this holds in both simulators (TVB 0.53 vs 0.71, SEREEGA 0.52 vs 0.65). At p = 0.8 and 0.9 both under-cover (0.75 and 0.80 for OursAR, 0.78 and 0.82 for the independent sampler), because the event requires every weak peripheral parcel, and we will report this as a limitation.

Overall, the dependencies improve error ranking, cardinality calibration and set calibration at moderate p, but not pairwise co-inclusion or the energy score. We propose to add this control as Appendix D.5, add the matched rows to Table 4, and describe the contribution of the dependencies in these terms.

Thank you again for your positive review and for the precise question on the role of the dependencies. Following your suggestions, we ran baselines that keep the parcelwise marginals of OursAR while removing the dependencies, together with cardinality and set-level calibration analyses. We hope these results clarify the contribution of the autoregressive decoder and would be happy to discuss any remaining points. If they address your concern, we would be grateful if you considered raising your score.

Reviewer_FkTwOpenReview ↗
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Paper summary

This paper introduces a montage-agnostic EEG source imaging (ESI) framework. It takes an unordered set of EEG channels with their 3D coordinates, predicts an approximate leadfield from the sensor geometry (so no forward model must be supplied at inference), and maps scalp activity to a 994-parcel cortical space using 64 temporal DCT coefficients per parcel. On top of this deterministic parcel encoder (Ours^Det), the authors train an autoregressive decoder (Ours^AR) that samples sets of active parcels of varying size, to express uncertainty about which parcels are active. The model is trained entirely on synthetic EEG-source pairs from two simulators (SEREEGA and TVB) on the fsaverage template anatomy. The authors evaluate fixed 256-channel reconstruction against classical, Bayesian, and learned baselines (Table 2), cross-montage transfer from 32/64/90/128 channels to unseen 21-, 76-, and 256-channel layouts (Table 3), uncertainty over which parcels are active (Table 4), and real-EEG localization across 61 intracranial stimulation runs from 7 patients in the Localize-MI dataset.

Critical strengths

Representing sensors as permutation-invariant tokens with continuous 3D coordinates, and using no layers whose size depends on the number of channels, is a natural way to handle variable EEG caps. Table 3 shows that a single model trained on 32, 64, 90, and 128 channels transfers smoothly to an unseen 76-channel subset of familiar electrode positions (10.4 mm localization error (LE) vs. 10.6 mm on seen layouts). Table 9 shows why performance drops on the unseen 256-channel layout: with the true leadfield instead of the predicted one, LE falls from 13.0 to 9.9 mm. The leadfield predictor, not the encoder, struggles with new electrode positions.

Critical weaknesses

The central real-data claim, a 15.5% reduction in median localization error on Localize-MI to 22.3 mm, rests on a comparison that is incomplete and asymmetric in several ways. First, the classical baselines are incomplete, and their source is unclear. Table 2 attributes the classical Localize-MI values (MNE 34.8 mm, sLORETA 34.6 mm, dSPM 28.4 mm) to the benchmark’s subject-specific head-model results. However, Mikulan et al. (2020) evaluated only MNE, dSPM and eLORETA (no sLORETA) and do not report a median error per method. They report best-configuration errors with individual BEM head models of 5.39 mm mean (range 2.3 to 12.2 mm), most often achieved by eLORETA, which Table 2 omits. A subsequent ten-method comparison on the same dataset (Pascarella et al., NeuroImage 2023) reports roughly 1.2 cm average error for the best methods, with dipolar and sparsity-promoting methods such as SESAME performing best; this paper evaluates SESAME only on synthetic data. The 22.3 mm headline therefore does not beat the best classical performance on Localize-MI, and the source of the reported classical numbers needs to be stated. Second, the real EEG is heavily transformed before it reaches the model. Per Appendix C.7, the model is fed only the final 60 ms of the stimulation-locked average, resampled to fill the 1-second input window. This appears to be a 16.7x time stretch, which shifts all temporal frequencies far from those of the 1-second training simulations. Localize-MI provides digitized per-subject electrode coordinates, which is exactly the input a montage-agnostic model should take. Instead, recordings are interpolated onto the fixed 256-channel training layout with spherical splines. The stimulation site is mapped to the fsaverage template by an affine transform, while the classical baselines use each subject’s own head model.

Questions for authors
  1. Where do the classical Localize-MI values in Table 2 come from? Mikulan et al. (2020) did not evaluate sLORETA and report no per-method medians. Please add eLORETA and SESAME on Localize-MI under both individual and fsaverage head models, and relate your result to the benchmark’s best-configuration errors (5.39 mm mean) and to the ten-method comparison of Pascarella et al. (2023).
  2. What is the rationale for taking the final 60 ms of the Localize-MI evoked response and stretching it by roughly 16.7x to fit the 1-second model window (Appendix C.7)? How do peak-to-site distance and AUPRC change with a native timescale (zero-padding or a wider epoch) rather than resampling?
  3. Localize-MI provides digitized per-subject electrode coordinates and the benchmark itself evaluates 256-, 128-, 64- and 32-channel montages. Why were recordings interpolated onto the fixed 256-channel training template (Appendix C.7)? Please report the multi-montage model on the native, un-interpolated coordinates, ideally across those four montages, since this is the real-data test the method is designed for.
  4. The learned baselines in Table 2 are re-implementations trained on your pooled SEREEGA+TVB simulator mix, yet Table 11 shows that adding TVB causes DeepSIF’s Localize-MI error to nearly double from 28.9 mm (when trained on SEREEGA alone) to 57.6 mm. Was the original authors' released DeepSIF checkpoint evaluated on Localize-MI, and how should the 57.6 mm DeepSIF baseline in Table 2 be interpreted given this simulator sensitivity? Also, please report Localize-MI results per subject (and under cortical geodesic distance, where Table 7 shows your model and ConvDip both sit around 40 mm) along with a paired comparison that accounts for the nesting of 61 runs within 7 subjects.
3 comments

First of all we would like to thank the reviewer for the careful reading. We ran all the analyses you asked for. Some of them change how we present our real-data results, and we will revise the paper accordingly. Below, numbers are median peak-to-site distances in mm over the 61 runs (three seeds for learned models). Paired comparisons resample subjects and then runs within each subject; we report ours minus the baseline with a 95% confidence interval, so a positive value means the baseline is closer.

Q1 answer.

The classical numbers do not come from Mikulan et al. since we computed them with our re-implementation of the benchmark pipeline, ported from the authors' original code. We also added sLORETA ourselves to provide an additional baseline. We will expand the caption and describe the pipeline in App. C.7.

As asked, we report eLORETA and SESAME, and ran every classical method with both the individual and the fsaverage head model:

MethodHead modelPeak-to-siteOurs minus method
Ours ARfsaverage (learned)22.7
dSPM / sLORETA / eLORETA / MNEindividual28.4 / 34.6 / 34.4 / 34.8-3.2 / -8.5 / -7.7 / -11.4 (all CIs include 0)
dSPMfsaverage19.2+4.0 [-0.2, +18.4]
sLORETAfsaverage19.7+4.0 [-1.8, +18.5]
eLORETAfsaverage20.8+3.0 [-4.1, +19.4]
SESAMEindividual21.5+0.5 [-9.1, +18.4]
SESAMEfsaverage26.2+0.6 [-7.3, +9.4]
ConvDip (retrained)fsaverage27.0-0.6 [-5.4, +4.1]
DeepSIF (retrained)fsaverage65.7-25.2 [-47.5, -7.7]

The fsaverage rows receive exactly the input our model receives: the EGI channels mapped by spline onto the 256-channel standard layout, the fsaverage forward model used for our training data, and the stimulation site registered to fsaverage. Their only change from the benchmark pipeline is a Ledoit-Wolf noise covariance. Scoring their peak per parcel, as for our model, changes them by less than 1 mm. SESAME uses the same data, fixed orientation and at most 10 dipoles, and we score its strongest dipole. Our 22.7 mm is the median of seed-averaged errors while the paper's 22.3 is the mean of per-seed medians.

Our model, which needs no subject-specific head model and runs in a single forward pass, performs on par with SESAME using individual head models (21.5 mm) and is the best of the learned methods. With the same template geometry, dSPM and sLORETA reach slightly lower medians (19-20 mm). These median differences are not significant; the mean difference for dSPM is significant (+13.1 [+2.6, +25.1]), mostly because of two subjects. Unlike the classical methods, our model also returns a distribution over active supports. Since the gain over ConvDip is not significant once runs are nested within subjects, we will replace the 15.5% claim with the statement that our model is competitive with the best classical and learned methods on Localize-MI.

For the best-configuration errors, we ran Mikulan et al.'s full grid (4 SNR x 10 loose x 10 depth) for MNE, dSPM and eLORETA on all runs, keeping the best configuration per stimulation as they do. dSPM reaches 21.9 mm and eLORETA 26.6 mm, and the best of the three per run gives 20.2 mm, all with ground-truth tuning. Our re-implementation does not reach 5.39 mm, and we have not yet identified the difference in protocol. For this reason we consider the fsaverage comparison the most reliable, since it shares our input and scoring. Pascarella et al. (2023) report about 12 mm for the best methods with their protocol; with ours SESAME reaches 21.5 mm. We will cite both and state the protocol difference.

Q2 answer. The derivative epochs only span -250 to +10 ms, so there is no native 1 s window. We tried windows of different length and the native 500 Hz timescale with zero padding:

WindowOursDetOursARMulti-montageConvDipDeepSIF
30 ms, stretched19.620.218.525.129.7
60 ms, stretched (paper)22.922.322.426.457.6
110 ms, stretched25.929.639.527.481.3
260 ms, stretched73.272.977.627.586.1
60 ms, native + zero padding68.170.874.643.769.2

The location information is in the stimulation pulse, within a few milliseconds of t = 0, which is why the classical pipeline uses ±2 ms. At the native rate the pulse covers one or two samples, while our temporal basis (64 DCT components over 1 s, up to 32 Hz) is built for the slower activity of the training simulations. The stretch maps the pulse into that band. Windows centred on the pulse give stable results (19.6-25.9 mm for OursDet from 30 to 110 ms), and the 60 ms window is not the best of them. Windows dominated by pre-stimulus baseline degrade, because the model expects activity throughout its input; ConvDip reads topographies sample by sample and is less sensitive to this. We will add this table, explain the stretch in App. C.7 and discuss the dependence on the window among the limitations.

Q3 answer. We used the benchmark's reduced EGI montages and its bad-channel replacement:

MontageOurs, spline to standard layoutOurs, recorded positionsOurs, recorded positions + true leadfieldBest classical, spline input
25622.431.927.120.1 (dSPM)
12822.132.526.718.2 (sLORETA)
6425.231.627.521.2 (sLORETA)
3227.136.027.022.2 (dSPM)

The model runs directly on the recorded coordinates at every density, and its error stays nearly constant as channels are removed. Using recorded positions costs about 10 mm, and most of it comes from the leadfield predictor, as Table 9 suggests. When we give the model the true fsaverage leadfield at the recorded positions, the error drops to 26.7-27.5 mm at every density, and at 32 channels it matches the spline input. The predictor was fitted only on standard 10-05 positions; refitting it on denser scalp positions needs only forward-model rows, not new simulations. We will report this table and discuss it as the main direction for improvement.

Q4 answer. We have downloaded the released DeepSIF weights (bfinl/DeepSIF), which use the same 994-region parcellation, and will evaluate them on Localize-MI with the same mapping and window in the revision. The pooled 57.6 mm understates DeepSIF, which reaches 28.9 mm when trained on SEREEGA alone (Table 11); Table 2 will show that setting too. With the same training data our imager reaches 22.7 mm (SEREEGA only) and 22.9 mm (pooled).

Per-subject medians (sub 1 to 7) are 18/23/39/64/30/16/16 for Ours AR, 21/31/32/27/29/13/21 for ConvDip and 13/27/22/23/18/18/20 for dSPM on fsaverage. Our median error is at most 30 mm in five of the seven subjects, and two subjects account for most of the remainder. With exact cortical geodesic distance we obtain 39.7 mm (Ours AR), 49.9 mm (ConvDip) and 161.8 mm (DeepSIF); ours minus ConvDip is +1.3 [-12.3, +7.7]. We will add the per-subject and geodesic tables with the nested statistics, and phrase our real-data claims accordingly.

Thank you again for your careful reading. Your comments led us to run eLORETA and SESAME with both individual and template head models, the time-window analysis, the evaluation on the recorded coordinates across the four benchmark montages, and the per-subject and geodesic results with nested statistics, and we will revise how we present our real-data results. We hope these additions clarify the points you raised and would be happy to discuss any remaining concerns. If they address your concerns, we would be grateful if you considered raising your score.

Reviewer_mqeuOpenReview ↗
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Paper summary

The paper proposes an EEG source imager that accepts different electrode layouts using electrode coordinates and measurements. It predicts parcel waveforms and samples sets of active parcels with an autoregressive decoder. Evaluation covers synthetic data, unseen montages, and real stimulation recordings from Localize-MI.

Critical strengths
  1. The experiments use scenario-disjoint splits, shared training conditions for learned methods, and multiple seeds for the main results. The limitations are discussed openly.
  2. The real-data results are promising: the full model reaches 22.3 mm median peak-to-site distance, compared with 26.4 mm for ConvDip and 57.6 mm for DeepSIF under the shared training setup.
  3. Processing different electrode counts with one model has practical value. Transfer to the unseen 76-channel layout is also encouraging.
Critical weaknesses
  1. The role of the physics prior needs clearer positioning. In Table 10, removing it improves most synthetic results, including localization error from 9.7 to 8.9 mm at 256 channels. It helps real-data transfer for the multi-montage model, but its benefit is less consistent for the fixed-montage model. The no-prior experiments also use fewer seeds. These findings deserve more emphasis and a complete comparison with equal seed counts.

  2. Montage generalization on real recorded coordinates remains untested. Localize-MI recordings are interpolated onto a standard layout before inference. This shows transfer to real EEG after preprocessing, but does not directly test the model on the original electrode positions. On synthetic data, replacing the predicted lead-field with the true one improves unseen-256-channel error from 13.0 to 9.9 mm, showing a limitation when positions are new.

  3. The benefit of modeling support dependencies is not isolated. The autoregressive decoder improves F1 and uncertainty-related metrics, but worsens localization error and AUPRC. Its energy score is also close to the independent decoder’s. Since their marginal probabilities differ, the comparison does not show how much of the gain comes from dependencies. An independent baseline with matched marginals would address this.

Questions for authors
  1. What justifies using the physics prior in the main model? Table 10 shows that removing it improves most synthetic results, while its real-data benefit depends on the training regime and metric. Could you complete the no-prior comparisons with three seeds for both regimes and report the full reconstruction and support-sampling results?

  2. How does the model perform on the original Localize-MI electrode coordinates? The current evaluation interpolates recordings onto a standard montage. Could you evaluate the multi-montage model directly on the recorded coordinates, without this interpolation? This would more directly test the practical value of montage-agnostic inference.

  3. How much of the decoder’s gain comes from modeling dependencies? Could you compare against an independent Bernoulli sampler using the autoregressive model’s empirical parcel-inclusion probabilities? Matching the marginals would help separate the contribution of dependencies from changes in individual parcel probabilities.

  4. What is gained by predicting the lead-field rather than computing a template lead-field directly? At unseen 256-channel positions, using the true lead-field reduces error from 13.0 to 9.9 mm. Could you compare prediction accuracy, computation time, and downstream performance against directly computed template lead-fields?

  5. How sensitive are the real-data results to the selected time window? What interval relative to stimulation does “the final 60 ms” refer to, and how are stimulation artifacts handled? Could you test alternative windows and explain how resampling this short segment to the model’s input length affects the temporal features?

  6. How robust are the classical baseline results to their settings? Were noise-covariance whitening and regularization tuning used, particularly under spatially correlated noise? Could you report how these choices affect the synthetic comparisons?

  7. How consistent is the improvement over ConvDip across real recordings? Could you provide paired uncertainty estimates for the peak-to-site difference, alongside per-participant results? The analysis should account for multiple stimulation runs coming from the same participant.

  8. Do the uncertainty results hold beyond pooled parcelwise metrics? Since most parcels are inactive, could you report calibration separately for active and inactive parcels, together with support-size accuracy? It would also help to explain when the decoder’s improved support and uncertainty scores outweigh its worse localization error and AUPRC.

3 comments

We thank the reviewer for these precise questions. Given their number, we have kept each answer shorter than we otherwise would, and we are happy to expand on any of them. We ran new experiments for most of them, and a few results lead us to rephrase some claims in the paper. Localize-MI numbers are median peak-to-site distances in mm over the 61 runs, and paired comparisons resample participants and then runs within participant, with 95% CIs in brackets.

Q1 answer. Table 10 shows that the prior hurts in-distribution synthetic accuracy (fixed 256 channels: LE 9.7 vs 8.9 mm) but helps under distribution shift. On the sparse 21-channel layout LE is 16.5 vs 18.8 mm, and on Localize-MI the multi-montage model reaches 22.4 vs 28.9 mm (AUPRC 0.102 vs 0.042), ranking the stimulated parcel higher in 81 of 122 runs. For the fixed 256-channel model the real-data effect is small and rests on a single no-prior seed. We keep the prior because it helps where the model leaves its training distribution, while noting that Localize-MI is also our test set, so this is not an independent model selection. As you point out, the comparison is incomplete. We are completing it with three seeds in both regimes, including the support decoder and the full reconstruction and sampling metrics, and the complete table will go into the main text.

Q2 answer. We ran the multi-montage model directly on the recorded EGI coordinates, registered but not interpolated, on the benchmark's 256/128/64/32-channel montages:

MontageRecorded positionsRecorded positions + true leadfieldSpline to standard layout
25631.9±2.327.1±1.122.4±1.0
12832.5±1.226.7±0.922.1±0.6
6431.6±3.027.5±0.225.2±2.7
3236.0±2.027.0±2.127.1±2.5

On recorded coordinates the error stays nearly constant as channels are removed, about 10 mm above the interpolated input. Giving the model the true fsaverage leadfield at the same positions recovers 4.5-9 mm, so, as you anticipated from Table 9, most of the gap comes from the leadfield predictor, which was fitted only on standard 10-05 positions. Refitting it on denser scalp positions needs only forward-model rows, and we will discuss this as the main direction for improvement.

Q3 answer. We ran this control without retraining on the Table 4 subsets. From each EEG's OursAR draws we built samplers with exactly the same parcel marginals and no dependencies, either by shuffling each parcel's column of the draw matrix or by independent Bernoulli draws. Since the marginals, and therefore the point estimate and its errors, are identical, any difference is due to the dependencies. Excess AURC goes from 54.5 for OursAR to 64.0 without dependencies (-9.5 [-11.1, -7.8]), which is about a third of the gap to OursInd (83.1), the rest coming from better marginals. The count Brier score also improves (-0.0064 [-0.0101, -0.0025]), and at a stated probability of 0.5 OursAR's support sets cover at the stated rate with 39 parcels, against 0.68 coverage and 205 parcels without dependencies. The dependencies do not improve pairwise co-inclusion (+0.0004 [+0.0003, +0.0005]) or the energy score (+0.1%). Our reply to Reviewer keHk gives the details, and we will restate the contribution in these terms.

Q4 answer. Against the fsaverage BEM, the predictor's mean relative row error is 0.03-1.7% on training layouts, 0.04% at 21 channels, 0.9% at 76 and 20% at 256. The true leadfield only helps where the predictor is wrong: Table 9 shows no change from 21 to 128 channels and 13.0 to 9.9 mm at 256, and the recorded positions of Q2 go from 32 to 27 mm. The predictor runs in 0.17 ms on a GPU, while computing the same leadfield with MNE takes 22-25 s per layout. Speed is not a strong argument, since a template leadfield can be cached. Prediction is convenient because the model needs only the EEG and the coordinates, with no forward-modelling pipeline, and the leadfield is differentiable in the positions. When a template leadfield can be computed it should be used, and the model accepts it unchanged. We will present the predictor in these terms.

Q5 answer. "The final 60 ms" is -50 to +10 ms relative to the pulse, and the derivative epochs span only -250 to +10 ms. We do not remove the stimulation artifact. As in the benchmark, whose classical pipeline uses ±2 ms around the pulse, the signal being localized is the field the stimulation produces around t = 0.

WindowOursDetOursARMulti-montageConvDipDeepSIF
30 ms, stretched19.620.218.525.129.7
60 ms, stretched (paper)22.922.322.426.457.6
110 ms, stretched25.929.639.527.481.3
260 ms, stretched73.272.977.627.586.1
60 ms at 500 Hz, zero-padded68.170.874.643.769.2

At the native rate the pulse covers one or two samples, while our temporal basis (64 DCT components over 1 s, up to 32 Hz) is built for the slower activity of the training simulations. Resampling maps the transient into that band, and the spatial pattern then carries the location information. Windows centred on the pulse give stable results, and 60 ms is not the best of them. Windows dominated by pre-stimulus baseline degrade, since the model expects activity throughout its input, while ConvDip reads topographies sample by sample and is less sensitive. We will add the table and discuss the window dependence among the limitations.

Q6 answer. Table 2 used one setting (λ = 0.05, no depth weighting, no whitening). We now score MNE, dSPM and sLORETA on the same 2,000 scenarios per simulator over λ in {0.005, 0.05, 0.5}, depth in {0, 0.8}, and no whitening, a population noise covariance or each scenario's own (oracle) noise covariance, taking as noise whatever the simulated sources do not explain. LE (mm) / AUPRC:

MethodPaper settingBest settingBest, oracle whitening
MNE60.3 / 0.15739.8 / 0.21032.2 / 0.282
dSPM35.7 / 0.15631.1 / 0.21827.8 / 0.249
sLORETA39.8 / 0.29621.8 / 0.30716.5 / 0.381
OursDet11.4 / 0.787

The paper setting was not the best one for the classical methods, and tuning halves sLORETA's error, although these settings are chosen on the test scenarios and therefore flatter them. OursDet stays clearly ahead, also when scenarios are split by the spatial correlation of their noise (tuned sLORETA 19.8-23.7 mm, oracle-whitened 16.1-17.1, OursDet 10.3-11.9). We will replace the classical rows of Table 2 with the tuned ones.

Q7 answer. Once runs are nested within participants, the difference from ConvDip is not significant (-0.6 mm [-5.4, +4.1]), so we will rephrase this claim. Per-participant medians (sub-01 to sub-07) are 18/23/39/64/30/16/16 for OursAR and 21/31/32/27/29/13/21 for ConvDip, and our error is at most 30 mm in five of the seven participants. Among learned models only the gap to DeepSIF is significant. With the same template input, dSPM and sLORETA reach slightly lower medians (19-20 mm, not significant), while our model needs no subject-specific head model and is on par with SESAME using individual ones (see our reply to Reviewer FkTw). We will describe it as competitive with the best classical and learned methods and add the per-participant and nested statistics.

Q8 answer. On the Table 4 subsets, restricting calibration to candidate parcels (p >= 0.01) removes the inactive bulk that dominates pooled ECE: OursAR then has ECE 0.009, against 0.037 for OursInd and 0.029 for the imager head. Mean p is 0.54 on truly active parcels, 0.037 on inactive parcels within 20 mm of the support and 0.003 further away. For the support size, the expected count is equally accurate for all decoders (mean error 3.8 parcels), but OursAR's 80% interval covers the true count 72% of the time, against 55% for the same marginals sampled independently and 48% for OursInd. It is still somewhat overconfident, and its wider count distribution puts slightly less mass within ±2 of the truth (0.39 vs 0.42). The decoder does not replace the imager's point estimate: OursDet is better for a single map (LE 9.7 vs 11.1 mm, AUPRC 0.787 vs 0.754), while the decoder is the tool for questions about the set, with better F1 and SD, a calibrated support size and a ranking of uncertain cases (excess AURC 55 vs 64 mm). We will add this guidance to Sec. 4.5.

Thank you again for your detailed questions. They led to several new analyses, including the evaluation on the recorded Localize-MI coordinates, the matched-marginal control isolating the contribution of the dependencies, the tuned classical baselines, the time-window analysis, and the nested per-participant statistics, which also led us to rephrase some of our claims. We hope these results clarify the points you raised and would be happy to discuss any remaining concerns. If they address your concerns, we would be grateful if you considered raising your score.

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Paper summary

This work proposes an EEG source imager that treats the electrodes as an unordered set of tokens carrying DCT signal features and 3D positions. A separately fitted predictor maps the positions to an approximate leadfield that is used to build parcel tokens, a deterministic head outputs parcel waveforms, and a pointer-style autoregressive decoder trained afterwards samples variable-size sets of active parcels. Trained on simulations on a fixed template anatomy, the deterministic imager is reported to improve localization error and AUPRC over DeepSIF on 256-channel synthetic data, the full model to reduce the median peak-to-site distance on Localize-MI by 15.5% relative to ConvDip, and a model trained on four layouts to transfer to unseen 21-, 76-, and 256-channel layouts.

Critical strengths
  1. The problem is relevant, since learned ESI models are usually tied to one electrode layout and return a single estimate, and this work addresses both in one model.
  2. The evaluation is careful, with scenario-disjoint test sets from two simulators, three seeds, real data with known stimulation sites, and geodesic distances. The limitations are discussed in detail.
Critical weaknesses
  1. Most results are on the authors' own simulations, and the authors themselves note that synthetic gains do not always carry over to real data. The only real data come from one dataset, Localize-MI, where the multi-montage model is tested only after interpolation to the 256-channel layout. Transfer to other layouts is therefore shown only on synthetic data. The baselines are also few, with none in Table 3 and no sparse methods or beamformers.
  2. The method is hard to follow because the reasons for its design are not given before the components are introduced. The leadfield predictor, a main feature in the abstract, is described in one sentence, with no architecture or training loss, and the code is not yet available. With a fixed template anatomy, the leadfield can be computed directly for any electrode positions. The predicted one is no better on familiar positions and worse on new ones (Table 9).
  3. The support decoder does not improve localization over the deterministic imager (Table 2), so the synthetic gain over DeepSIF claimed in the abstract is much smaller for the full model. The value of the decoder therefore depends on the probabilistic interpretation of its samples. The energy score and excess AURC improve on synthetic data, but they do not show whether the spread of the samples matches the actual errors. Coverage at given predicted probabilities, reported with the set sizes, would show how the decoder differs from simply widening the candidates.
Questions for authors
  1. How do classical methods, ConvDip, and fixed-montage models applied after interpolation perform on the unseen layouts of Table 3?
  2. How does the multi-montage model perform on Localize-MI subsampled to low-density layouts at the native electrode positions?
  3. What architecture and training loss does the leadfield predictor use, and what does predicting the leadfield offer over computing it on the template anatomy?
  4. How often does the true support fall within sets of a given predicted probability, and how large are these sets?
4 comments

Thank you for the constructive review and for the concrete questions on montage transfer and real recordings. We ran new experiments for Q1-4 and report all the results below.

Q1 answer. We used the same 10k test sets per simulator as Table 3 (simulators pooled, three seeds). For the fixed-montage models we took the 256-channel checkpoints of Table 2 and mapped the unseen layout onto the 256 positions by spherical spline, as we do for Localize-MI. Electrodes shared by both layouts are copied exactly. The classical methods use each layout's true leadfield. They need no training, so for them the layout is not "unseen", but we include them as a reference (2k scenarios per simulator, as in Table 2).

LayoutMethodLE (mm)AUPRCF1
21Ours, multi-montage16.5±0.20.521±0.0060.460±0.008
21OursDet-256, raw 21 channels27.0±0.30.303±0.0060.290±0.003
21OursDet-256 + spline44.9±2.20.123±0.0030.125±0.002
21DeepSIF-256 + spline49.8±0.70.207±0.0050.179±0.005
21ConvDip-256 + spline41.6±0.70.277±0.0090.216±0.001
21sLORETA / dSPM / MNE54.8 / 43.9 / 71.80.168 / 0.111 / 0.0810.156 / 0.128 / 0.085
76Ours, multi-montage10.4±0.10.747±0.0060.648±0.006
76OursDet-256, raw 76 channels11.4±0.10.693±0.0060.606±0.004
76OursDet-256 + spline16.8±0.00.478±0.0070.441±0.003
76DeepSIF-256 + spline16.5±0.50.593±0.0080.501±0.008
76ConvDip-256 + spline26.1±1.00.432±0.0200.316±0.006
76sLORETA / dSPM / MNE45.1 / 39.8 / 63.90.255 / 0.137 / 0.1300.223 / 0.158 / 0.127

The multi-montage model is best on every metric at both layouts. Interpolation costs every learned model 6-16 mm at 76 channels, and at 21 channels it brings them down to the level of the classical methods. The OursDet-256 rows separate architecture from training. Fed the sparse layout directly, a model trained only at 256 channels still does well at 76 channels but not at 21, so sparse layouts need training on several layouts. We will add these rows to Table 3.

Q2 answer. We used the benchmark's own reduced montages (for each GSN-HydroCel-128/64/32 electrode, the nearest recorded channel, with its bad-channel replacement). Numbers are median peak-to-site distances in mm over the 61 runs. The classical column inverts the same spline-mapped data with the fsaverage forward model, so it receives exactly our input and is scored against the same registered target.

ChannelsOurs, recorded positionsOurs, recorded positions + true leadfieldOurs, spline to standard layoutConvDip-256DeepSIF-256Best classical, same input
25631.9±2.327.1±1.122.4±1.026.4±0.357.6±5.020.1 (dSPM)
12832.5±1.226.7±0.922.1±0.626.8±2.258.3±4.318.2 (sLORETA)
6431.6±3.027.5±0.225.2±2.737.6±1.972.1±14.521.2 (sLORETA)
3236.0±2.027.0±2.127.1±2.526.1±2.167.1±8.422.2 (dSPM)

With spline input the model loses only 5 mm from 128 to 32 channels. It is the best learned model at 128 and 64 channels, on par with ConvDip at 32, and has the highest stimulated-parcel AUPRC among them at every density (0.103 / 0.079 / 0.138 vs at most 0.075). Classical inverses given the same input and template head model reach 4-5 mm lower medians. At 256 channels, where we computed paired statistics with runs nested in subjects (see our reply to Reviewer FkTw), these median differences are not significant.

The model also runs directly on the recorded coordinates, and its error stays nearly constant as channels are removed. Using recorded positions costs about 10 mm, mostly because of the leadfield predictor, as Table 9 suggests on synthetic data. When we give the model the true fsaverage leadfield at the same positions, it recovers 4.5-9 mm, and at 32 channels it matches the spline input. The predictor was fitted only on standard 10-05 positions, and refitting it on denser scalp positions needs only forward-model rows, not new simulations. If needed we will report this (or part of this) table and discuss it as the main direction for improvement.

Q3 answer. The predictor is small, each electrode position goes through a Fourier encoding and a three-layer MLP that outputs 64 coefficients, which are multiplied by a learned 994x64 parcel basis to give that electrode's gain row (rank 64 keeps 99.97% of the template leadfield's energy). We fit it to the BEM rows of the 32-128-channel layouts with a relative row-error loss and freeze it before training the imager. On held-out layouts its error is 0.04% at 21 channels, 0.9% at 76, and 20% at 256, where half the positions are new.

We agree with your second point. With a fixed template the leadfield can be computed for any positions, and when it is available it should be used. The imager accepts it unchanged and does better at 256 channels (Table 9). The predictor is a convenience. At inference the model needs only the EEG and the coordinates, with no head model or BEM solve. Its accuracy drops at positions far from the training layouts, as Q2 shows. We will say this in the abstract and Sec. 3.1, move the architecture and loss into the main text, and release the code.

Q4 answer. For each EEG we rank parcels by the decoder's inclusion probability and take the shortest prefix whose predicted probability of containing the whole true support (the fraction of 500 draws inside it) reaches p. We then check whether the true support is inside and record the set size. Table 4 subsets, 6,000 EEG-seed pairs.

Stated pCoverageMedian sizeSame marginals, independent: coverage / sizeImager head, same size: coverage
0.50.528390.678 / 2050.540
0.80.7463540.782 / 3990.812
0.90.8044490.815 / 4580.877
0.950.8284820.831 / 4850.901

At p = 0.5 the stated probability holds (coverage 0.53, median 39 parcels: 21 for TVB, 134 for SEREEGA). At higher p coverage falls below the stated level (0.80 at p = 0.9). Containing the whole support means containing every weak peripheral parcel, and many of these never appear in any draw. Excluding the 1.5% of supports larger than the 32-parcel cap changes little (0.81).

For the comparison you ask about, the imager's parcelwise head, read as independent probabilities, gives sets of 880-983 parcels at every p, so its probabilities cannot be read at the set level. At equal size, though, ranking parcels by the imager's head covers about as well as the decoder at p = 0.5 and better at higher p (0.88 vs 0.80 at p = 0.9). The decoder contributes a calibrated choice of set size at moderate p, while its ranking of parcels is similar to the imager's. We will make this distinction explicit in the paper. Sampling the decoder's own marginals independently over-covers at p = 0.5 (0.68) with sets five times larger, so the tight sets come from the dependencies.

Per parcel, the decoder's probabilities are close to calibrated (for example, predicted 0.449 against an observed 0.457, and 0.948 against 0.946) and slightly underconfident between 0.7 and 0.9 (predicted 0.847, observed 0.904). The marginal-mass sets of Fig. 3 have 8 parcels at 50% mass (recall 0.59) and 93 at 90% (recall 0.93, with the whole support inside in 60% of cases). We will add these results and list the under-coverage at high p as a limitation.

Thank you again for your constructive review. Your questions led us to run the baselines on the unseen layouts of Table 3, the evaluation on Localize-MI at the recorded electrode positions and reduced montages, the full description of the leadfield predictor, and the coverage analysis of the support sets. We hope these results clarify the points you raised and would be happy to discuss any remaining concerns. If they address your concerns, we would be grateful if you considered raising your score.

Thanks for the response and all the new experiments. The rows for the unseen layouts are convincing. But on Localize-MI, dSPM and sLORETA with the same input are at 18-22 mm against 22-27 mm for the model, and the gain over ConvDip is not significant. The coverage of the decoder is also below the stated level at high p (0.80 at 0.9). You say the 15.5% claim will be replaced, but the paper has not been updated, and in its current form the claims are stronger than the results. I keep my score.

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