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Under review as a conference paper at ICLR 2027

A Foundation Model for Time-Harmonic Electromagnetic Behavior

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Abstract

3D electromagnetic (EM) systems underpin semiconductor packaging, conformal antennas, and consumer devices such as phones and wearables. Full-wave simulations are necessary to model these systems but remain costly across large design and frequency spaces, while existing surrogates typically specialize in a narrow design family and predict either fields or aggregate responses. We introduce the first EM foundation model for complex 3D systems, predicting both electromagnetic fields and scattering parameters for unseen devices. Our contribution is threefold. First, we generate a corpus of approximately 250k simulations spanning 25 template families of 3D printed-circuit-board and package structures. Second, we train a 340M-parameter model that predicts complex-valued electric and magnetic fields at arbitrary locations and S-parameters across frequencies and port pairs. Finally, we introduce , the first public evaluation suite for EM foundation models covering both data modalities. We find that joint field and S-parameter supervision preserves in-distribution S-parameter accuracy while reducing out-of-distribution error relative to S-parameter-only training, suggesting that field supervision encourages representations that generalize more effectively across geometry families. Also, ablations identify impedance-aware target scaling, a robust field objective, and relative spatial encoding as critical to accurate complex-field prediction. Ultimately, our model's full EM vector-field predictions provide a rich physical description of unseen devices that enables design-critical downstream calculations and visual debugging, opening a path toward general-purpose learned models of EM systems.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
scientific machine learning, neural operators, surrogate modeling, foundation models, computational electromagnetics, electromagnetic field prediction

Reviews

Among:
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1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_C9sMOpenReview ↗
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2
Confidence
2
Informativeness
2
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2
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Paper summary

This paper presents a 340M-parameter neural surrogate for time-harmonic electromagnetic behavior in PCB and package structures. The model combines a sparse volumetric geometry encoder with query-based decoding to predict complex electric and magnetic fields at specified positions, frequencies, and excitations, as well as S-parameters through a separately supervised output head. The authors generate approximately 250,000 simulated designs from 25 template families and introduce EMVal to evaluate field and port-response prediction. Validation includes two held-out geometry families, component ablations, and smaller-scale comparisons with GINO and Transolver. The main empirical finding is that joint field supervision substantially improves S-parameter prediction on the held-out families while leaving in-distribution performance approximately unchanged. The ablations also reveal a tradeoff between global field accuracy and typical-probe relative error.

Critical strengths
  1. Evidence that dense field supervision improves generalization of global responses. The comparison in Table 1 shows that jointly supervising complex E/H fields improves held-out-family S-parameter riRMSE from 0.153 to 0.102 and magnitude weighted MAE from 0.940 to 0.489 dB, while in-distribution performance remains approximately unchanged. This is the paper’s strongest contribution: it suggests that retaining the richer spatial information produced by full-wave simulations can improve prediction of aggregate responses on unseen geometry families. The comparison uses the same nominal architecture and training corpus, making the observed benefit informative for surrogate-model training.

  2. A substantial effort to model local and global EM responses within a common framework. The reported corpus pairs geometry, materials, ports, complex vector fields, and S-parameters across multiple PCB/package families. The common query interface and complementary global and local field metrics provide a useful framework for studying these responses together. In particular, the ablations expose a meaningful tradeoff: the robust objective improves typical-probe relative error, whereas impedance-scaled MSE performs better on global field error. The paired corpus could also become a valuable community resource if released with sufficiently complete generation and evaluation specifications.

Critical weaknesses
  1. The central generalization and benchmark contributions are insufficiently characterized. The OOD evaluation uses only two held-out geometry families within a common board-size, material, frequency, and port regime. However, the manuscript does not identify these families, provide a complete inventory and parameter ranges for the training families, or report results separately for each held-out family. Consequently, it is difficult to assess the difficulty of the distribution shift or whether the joint-supervision benefit holds across both families. The board-level bootstrap intervals do not resolve this uncertainty about generalization across families. In addition, although EMVal is described as public, the supplied manuscript does not provide access information or sufficiently complete generation and split specifications. These gaps matter because cross-family reuse and the evaluation resource are central to the paper’s claimed contribution.

  2. The evaluation does not sufficiently establish the advertised design-relevant accuracy and utility of the predicted fields. Both S-parameter metrics de-emphasize low-magnitude responses: complex RMSE measures absolute amplitude error, while Eq. (7) assigns a weight of approximately 4.5 × 10⁻⁵ to a true response of −40 dB. Errors in deep stopbands or isolation can therefore contribute very little to the reported scores, although these regions may determine whether a design meets its specifications. Figure 4 illustrates visible stopband discrepancies despite a favorable aggregate error. Furthermore, the S-parameters are predicted by a separately supervised head, so their accuracy does not validate quantities derived from the predicted fields. The qualitative Poynting visualization is encouraging, but no quantitative evaluation of a field-derived quantity establishes the claimed downstream utility. This limits how strongly the reported benchmark improvements support the broader application claims.

Questions for authors
  1. Clarification of the OOD protocol. What are the 25 training families and the two held-out families, including their parameter ranges and sample counts? Please report the joint-versus-S-only results separately for each held-out family and clarify whether these families were used for model or hyperparameter selection. This would help establish whether the reported gain is consistent across distinct geometry families.

  2. Clarification of resource availability. Where can reviewers access EMVal, its split definitions, and the metric implementation? Please specify which artifacts are available or planned for release, particularly the template generators, simulation configurations, training data, and pretrained weights.

  3. Clarification of the learned Student-t objective. Equation (3) omits the normalization term C(ν)=log⁡Γ(ν/2)−log⁡Γ((ν+d)/2)+d2log⁡(νπ),C(\nu)=\log\Gamma(\nu/2)-\log\Gamma((\nu+d)/2)+\frac{d}{2}\log(\nu\pi), although ν\nu is learned. Is this term included in the implementation, or is the displayed unnormalized robust objective intentional? Please explain the rationale for learning ν\nu under the implemented objective and report its initialization and learned value. Omitting this term is inconsequential for fixed ν\nu, but changes its gradient when ν\nu is optimized.

  4. Targeted analysis of existing predictions. Could you report S-parameter magnitude errors stratified by the true magnitude, particularly below −30 dB, on the existing test set? Does the joint-supervision benefit persist in these regimes, and what do the errors imply for stopband attenuation or isolation in the relevant device families? This analysis would help determine whether the reported improvements extend to design-relevant behavior that the weighted metric largely excludes.

  5. Clarification on the title: Why do you believe the task of design on PCB is a "Foundation Model for Time-Harmonic Electromagnetic Behavior"? Is it bit overclaiming?

2 comments

Thank you for the specific questions. We appreciate that you called the held-out S-parameter gain from field supervision the paper's strongest contribution, and that you found the common framework for local and global responses useful. Your question on the Student-tt objective led to new runs that we believe strengthen the paper.

Q1 / W1. Held-out families

The held-out OOD families are two planar copper-strip geometries: crossed strips (two perpendicular strips that overlap in a plus, T, or L shape; 1k designs) and fishbones (one spine crossed by several parallel bars; 1k designs), each with either 1 or 2 ports. No hyperparameters or checkpoints were selected on these families. Both families benefit from field supervision:

Held-out familyModelriRMSE [95% CI]mag-wMAE (dB) [95% CI]
Crossed stripsfield + S0.046 [0.044, 0.048]0.197 [0.187, 0.207]
S only0.082 [0.079, 0.085]0.389 [0.367, 0.409]
Fishbonesfield + S0.157 [0.153, 0.162]0.781 [0.749, 0.816]
S only0.223 [0.218, 0.229]1.490 [1.432, 1.554]

Joint supervision reduces riRMSE by 44% on crossed strips and 30% on fishbones, and mag-wMAE by about half on both.

The revision reports these per-family results in Appendix B (Table 4) and lists every design family in Appendix C (Table 6).

Q2. Resource availability

A 500-board 43.6 GB subset of EMVal, with the metric code and evaluation protocol, is publicly available. To preserve anonymity, the camera-ready version will give the link and the full split definitions. The full training corpus, model weights, template generators, and simulation configurations are proprietary and are not released.

Q3. Student-tt objective clarification

You are right that Eq. (3) omits the normalizing term of the Student-tt log-density, C(ν)=log⁡Γ(ν2)−log⁡Γ(ν+d2)+d2log⁡(νπ)C(\nu)=\log\Gamma(\tfrac{\nu}{2})-\log\Gamma(\tfrac{\nu+d}{2})+\tfrac{d}{2}\log(\nu\pi). Eq. (3) is therefore a heteroscedastic loss of Student-tt form rather than an exact likelihood, and it learns the tail parameter ν\nu. We ran a new experiment (Appendix E of the revision) to test what including C(ν)C(\nu) does, and whether the gain over MSE in Table 2 comes from the Student-tt tail shape or from the learned per-probe scale. Starting from the 52M default configuration of Table 2, we include C(ν)C(\nu), fix ν\nu at 12, or replace the Student-tt with a Gaussian negative log-likelihood that keeps the learned per-probe scale.

Selected metrics (means; see Table 8 of the revision for the full results):

Variantν\nuID field rel L2L_2 (E\mathbf{E})ID riRMSEOOD field rel L2L_2 (E\mathbf{E})OOD riRMSE
default (no C(ν)C(\nu))12.3–12.60.2740.0650.4010.133
with C(ν)C(\nu)2.00.5910.1820.7170.291
ν\nu fixed at 12120.2810.0610.4090.152
Gaussian NLL∞\infty0.2570.0580.3680.120

With C(ν)C(\nu), ν\nu falls to its floor of 2 and every metric is far worse; a likely cause is that heavier tails let the model discount the residuals it fits worst. With ν\nu fixed at 12, results are close to the default except for higher out-of-distribution S-parameter error. The Gaussian is comparable in distribution and better or tied out of distribution on every metric. The gain over MSE therefore comes from the learned per-probe scale, not from heavy tails. Every model in the paper is trained with Eq. (3). The Gaussian form is a promising choice for future research (we have not yet tested it at 340M parameters).

Q4 / W2. Low-magnitude S-parameters

Here, we report the out-of-distribution mean absolute error of ∣S∣\lvert S\rvert in dB, binned by the true magnitude. Error grows as the magnitude falls, but the gain from joint supervision (compared to S-only supervision) persists in every bin, including below −40 dB:

True ∣S∣\lvert S\rvert (dB)OOD: field + SOOD: S only
> −100.450.90
−10 to −202.133.55
−20 to −304.006.13
−30 to −405.548.04
< −407.8712.88

With errors of several dB below −30 dB, the model can screen designs on stopband attenuation and isolation, but checking a design's margin against such a specification still needs full-wave simulation. The revision adds this breakdown as Table 5 in Appendix B.

Q5. "Foundation model" title

We use "foundation model" in its usual sense: one model trained on a broad set of data that serves as a base for downstream tasks. We view our joint model's superior OOD S-parameter prediction performance compared to S-only pretraining as a clear demonstration of this capability, and do not believe it is overclaiming. However, to further demonstrate our model's ability to transfer to downstream tasks, we formulated and ran a new transfer learning experiment, which we detail in our reply to GeG2 and in Sec. 4.2 and Appendix G of the revision.

Thank you again for your detailed review. As the discussion period closes tomorrow, we wanted to check whether our response addressed your questions. In brief, the revision identifies the two held-out families and reports results for each, with both benefiting from field supervision (Appendix B, Table 4); lists all design families by device type (Appendix C); tests including C(ν)C(\nu), fixing ν\nu, and a Gaussian objective (Appendix E); reports S-parameter error by true magnitude, where the gain from joint supervision persists below −40 dB (Table 5); and adds a fine-tuning experiment on a new target (Sec. 4.2). If these address your concerns, we would be grateful if you would consider updating your score, and we are happy to answer any remaining questions.

Reviewer_GeG2OpenReview ↗
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Paper summary

The authors develop a large-scale dataset of electromagnetic (EM) systems, comprising a 3D voxel-based characterization of system, and corresponding system properties comprising complex S-parameters and complex field distributions. The authors then use this dataset to train and evaluate an EM foundational model.

Critical strengths
  1. Building a foundation model for EM systems is an important problem, and it appears that this is indeed the first attempt to build such a model for EM systems.
  2. The model architecture proposed by the authors seems like a reasonable adaptation of existing approaches to this problem
  3. The publication of the large dataset produced by the authors is a valuable contribution to photonics community.
  4. The paper is relatively well written, which I greatly appreciate.
Critical weaknesses

I appreciate this work, and I think this is a very important general direction of research. I think this work has some potentially great value, however, there is one major flaw that undermines the authors' main conclusion that their proposed model is a "foundation model", and therefore I am compelled to give a "weak reject", instead of a "strong accept".

  1. A unique and IMO necessary property of a foundation model is that it acts as a "foundation" for other data-driven models on the same or similar EM systems. most typically this is demonstrated by showing that a foundation model can reduce (often significantly) the quantity of training data required for related modeling tasks via transfer learning. Specifically, the conventional approach is to utilize the foundation model parameters to initialize training, or "fine-tuning", on a related problem where data is more limited. The authors do not demonstrate this in any way for their proposed model. Consequently, the central claim of the paper, that the proposed model is an EM foundation model, remains largely unsupported in my opinion. Without this evidence, it is unclear to me whether the data and the model are truly useful for the community, or just another surrogate model for an arbitrary class of EM systems, of which there are very very many by now in the literature

This work becomes substantially more valuable if the authors can show that their foundation model reduces training data requirements on some other related problem, especially one that has been studied in a prior publication. e.g., a problem where the authors of another publication predict the field patterns of some other EM system, and have some simulated training data to fine-tune the foundation model. Ideally the authors would demonstrate this for two or three such systems. I realize this is a lot of extra work, but this is really where the authors can prove that their data and their model are useful, and this goes from being of highly questionable value to extremely high impact.

Questions for authors
  1. In Section 4.1 the authors claim that training on fields does not reduce the in-domain S-parameter predictions. I'm not sure that is entirely accurate. In table 1 the mage-wMAE error goes up and the difference seems like it may be statistically significant. No? I don't see this as a major problem. I'd agree the error increase is modest compared to the improved generalization on OOD data, but I'd encourage the authors to simply state it this way.
3 comments

Thank you for the constructive review. We appreciate that you see an EM foundation model as an important problem, that this appears to be the first attempt to build one, and that you found the paper well written. Your point that a foundation model should learn a new task from fewer examples led to the transfer experiment below, which we believe strengthens the paper.

W1. Foundation model claim

While we view our joint model's superior OOD S-parameter prediction performance (compared to S-only pretraining) as a clear demonstration of transferability from fields to the downstream target task of S-parameter prediction, we agree that it does not demonstrate the traditional "foundation model" claim that a pretrained model can learn a new task from fewer examples.

To address this, we designed and ran a new transfer learning experiment (detailed below) and show that starting from our pretrained model significantly reduces the amount of data required to learn a new target.

Transfer learning experiment. We formulate a new task of predicting "resonance" (whether the minimum of ∣Sii∣\lvert S_{ii}\rvert at a driven port over the 1–20 GHz band is below −10 dB and away from the band edges, and if so, its frequency), a target the model never trained on, using N boards drawn from the training families and scored on the two held-out families. We fine-tune both our pretrained 340M models (joint and S-only) with increasing numbers of boards, and compare to an identical randomly initialized "from-scratch" model trained on the same task directly, as well as a downsized 52M model trained from scratch on the same task.

Experiment results are detailed below. We score resonance detection by AUROC, which measures how well the predicted probability separates resonant from non-resonant entries at any threshold (0.5 is chance), and the frequency MAE (GHz) over truly resonant entries, against the number of fine-tuning boards N. Fine-tuned: mean ± sd over three seeds. From scratch: one seed at each size.

NFine-tuned, field + S: AUROC ↑MAE ↓Fine-tuned, S only: AUROC ↑MAE ↓From scratch, 340M: AUROC ↑MAE ↓From scratch, 52M: AUROC ↑MAE ↓
1280.79 ± 0.033.49 ± 0.220.71 ± 0.013.53 ± 0.120.713.980.684.38
5120.81 ± 0.013.25 ± 0.040.69 ± 0.033.48 ± 0.080.743.550.703.48
2,0480.81 ± 0.013.30 ± 0.050.73 ± 0.013.35 ± 0.050.753.440.743.70
8,1920.83 ± 0.012.98 ± 0.110.79 ± 0.003.15 ± 0.040.763.650.753.60

Fine-tuning the jointly pretrained model separates resonant from non-resonant entries better than training on the target directly, at every N: its mean AUROC is about 0.8, against at most 0.76 from scratch. S-only pretraining transfers less: fine-tuning the S-only model is no better than training from scratch until N = 8,192. The jointly pretrained model also has the lowest frequency error at every N, falling to 2.98 GHz at 8,192 boards.

Data and compute. With 128 boards, the jointly pretrained model already exceeds the best from-scratch run (340M parameters, 8,192 boards), which used 64 times as many boards and about 330 times more compute (not counting pretraining).

Experiment details are in Sec. 3.6 of the revision, the performance and compute comparison is in Figure 4 (Sec. 4.2), and the full results table is in Appendix G.

Q1. In-distribution mag-wMAE

Agreed, your comment is fair. Sec. 4.1 of the revision now says that field supervision slightly increases in-distribution S-parameter error while reducing it substantially out of distribution.

Reviewer_GeG2OpenReview ↗

Clarification on my feedback

I thank the authors for their response.

Yes, I agree, the authors show evidence of transfer learning, but it is just transfer learning my opinion, and not "foundation modeling". The authors show transfer learning is done between two problems that are created by the authors, and that are (relatively) closely-related to each other. This demonstrates that their model can be used for transfer learning, but this is not especially new or surprising in machine learning or EM in particular. Showing that the weights of a deep network can be transferred between two tasks has been done ad nauseam in machine learning, and even in EM field more recently. Predicting 3D field patterns has also been done before, although I'd grant the authors that their architecture is much better than past work and somewhat interesting (thus my weak reject instead of strong reject).

What would be interesting, and new in EM, is if you can show that your model helps solve tasks from other papers/research. Cite a paper or two and then replicate their problem setting. Then show that your model helps reduce training data complexity on that problem. Then I think you have evidence of a foundation model. Without this, I think you essentially show that you can build a deep net that predicts 3D field distributions (not especially interesting) and that transfer learning works for your model (not especially interesting), but not that it is a foundation model.

Again, I realize this is a lot of extra work, and I appreciate what the authors are trying to do quite a bit, but without this crucial evidence I think the paper falls short of its claims.

AuthorsOpenReview ↗

Foundation model scope

Thank you for the follow-up and for your recognition that our architecture is much better than past work.

We want to be clear about what we mean by "foundation model", so that our claim is not overstated. Following Poseidon (Herde et al., 2024), we mean a model pretrained on broad data that can be adapted to new tasks with less data than training from scratch. For us, the scope of this foundation model is limited to (1) the physics of time-harmonic Maxwell's equations, (2) driven, passive circuit-board and package structures (patterned metal layers on dielectric, with vias and solder balls) within an 8 × 8 mm footprint, and (3) predictions of S-parameters, and of complex vector fields at arbitrary locations around the board, over the 1–20 GHz band.

Within this scope, our pretraining data is broad, as demonstrated by the large volume (250k simulations) and variety of 3D geometry families in our dataset (25 families across many device types), as opposed to a single or small number of parameterized design families, often 2D or 2.5D, as is typical of prior EM surrogate work. The capability to adapt to downstream tasks is demonstrated both by joint training on fields and S-parameters improving S-parameter prediction on held-out families compared with training on S-parameters alone (Table 1), and by the new fine-tuning experiment in Sec. 4.2 (the conventional foundation model fine-tuning approach you suggested).

We also would like to clarify that though the downstream task from Sec. 4.2 is somewhat related to the S-parameter prediction task, it removes the frequency query token from the input (which was part of every field and S-parameter query sequence during pretraining) and learns a new query token embedding and a new output head. This is a sufficiently different task that it is not immediately obvious that the same model would provide a good foundation, yet with 128 boards the fine-tuned model beats the best from-scratch run, which used 64 times as many boards and about 330 times the compute, not counting pretraining.

We agree that fine-tuning on problems from other papers is a valuable next step, and we see it as future work that builds on this claim.

Reviewer_KbbtOpenReview ↗
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Paper summary

This paper proposed a transformer-based predictor for 3D electromagnetic system, in particular for predicting electromagnetic fields at any desired configurations (e.g., location and frequency) as well as the matrix of scattering parameters (S-parameters) based on some given input geometry of the system.

Critical strengths

The way of using transformer with cross-attention mechanism to design a predictor that yields both electromagnetic fields and S-parameters is timely and sensible. Also, treating the specific configuration of interest (e.g., the location of interest) as tokens while feeding the input 3D setting directly into the decoder after compressing into appropriate latent vectors, makes a lot of sense and interesting.

Critical weaknesses

The main weaknesses are: (i) no clear justification for designing the robust loss function; (ii) no justification for considering the evaluation metric; (iii) trained/evaluated only based on simulated data, rather than real data; (iv) related with (iii), no comparison with "direct running through simulator". Let me detail a bit more in the following.

(i) no clear justification for designing the robust loss function

The authors proposed a robust training objective based on Student-t distribution with learnable degrees of freedom parameter \nu that controls the fatness of the tail. Interesting, but it is hard to grasp how to get the exact formulation (3). I think the right way to do is: describe how the authors are modeling the likelihood function (including all the details such as the assumption of uncorrelatedness across dimension (I guess ?)); why such modeling makes sense including why Student-t; why use logarithm to design the actual loss function. But currently, there is no clear construction for (3) and it is hard to judge whether (3) is a sensible choice or not.

(ii) no justification for considering the evaluation metric

Evaluation metics look OK as they resemble common metrics in several different fields. However, whether they are also the right and common choice in this field is not clear. The main issue comes from lack of reference for the evaluation metric -- here the reference should come from EM literature by the way.

(iii/iv) trained/evaluated only based on simulated data, rather than real data; no comparison with direct simulator-based approach

All the training and evaluation are done based on simulated data. Unless the authors can argue that simulator can be treated as the real world, this is a clear limitation of this work. Now suppose that simulator is good enough and the goal of this work is to "skip" the actual running of the simulator to get the predicted output using a much lower cost. However, such cost reduction has not been reported in this work hence it is hard to gauge the true benefit of this work. That is, I think there should be a clear comparison, something like: proposed vs. simulator-running where both evaluation metrics as well as the computational costs (e.g., memory, energy, wall-clock time etc) are reported in a side-by-side manner. Without such comparison, I think one may just run the simulator unless the computational cost gain is significant.

Questions for authors

As mentioned above, if the authors can clarify:

(i) how the authors constructed training objective (3) (ii) whether evaluation metrics are standard/common in EM literature (iii) computational cost comparison with "simulation-running" baseline

then I would be happy to adjust my assessment.

5 comments

Thank you for the clear review, and for listing exactly what would change your assessment. We appreciate that you found the cross-attention design for predicting both fields and S-parameters timely and sensible, and the treatment of query configurations as tokens over a compressed geometry representation interesting. We address each of your questions below.

(i) How Eq. (3) is constructed

Eq. (3) comes from the negative log-likelihood of a multivariate Student-tt with scale matrix eℓIe^{\ell}\mathbf{I}, without the normalizing term C(ν)C(\nu):

−log⁡p(r)=ν+d2log⁡ ⁣(1+∥r∥2e−ℓν)+d2 ℓ+C(ν).-\log p(\mathbf{r}) = \frac{\nu+d}{2}\log\!\left(1+\frac{\lVert\mathbf{r}\rVert^2 e^{-\ell}}{\nu}\right) + \frac{d}{2}\,\ell + C(\nu).

The log is there because we train by maximum likelihood. It assumes:

  1. One scale for all 12 field components. After impedance scaling, E\mathbf{E} and η0H\eta_0\mathbf{H} have the same units, so we use one scale to fit both, and model no correlation between components. Without that scaling, H\mathbf{H} is ~377× smaller and would be ignored.
  2. A separate scale for each probe. The network predicts a scale parameter ℓ\ell per probe (Kendall and Gal, 2017). Field magnitudes on one board span ~80 dB (Fig. 5c–d of the revision), so a single scale would not fit them all well.
  3. Student-tt form with a learned ν\nu. We chose this form originally to limit the influence of very large residuals. In Table 2, switching from MSE to this loss form cuts the median per-probe error from 0.769 to 0.406 for E\mathbf{E} and from 0.971 to 0.509 for H\mathbf{H}. However, in response to your question and a related question from reviewer C9sM, we ran a follow-up experiment to better identify where the performance improvement comes from (see experiment details in our response to C9sM and in Appendix E of the revision), and found that it comes from the learned per-probe scale, not from heavy tails. A Gaussian with the same per-probe scale performs comparably in distribution and is better or tied out of distribution. Every model in the paper is trained with Eq. (3), but the simpler Gaussian objective is a promising choice for future research.

(ii) Are the metrics standard in EM?

There is no universally accepted accuracy metric for learned EM surrogates, which is part of why we built EMVal. Our metrics follow the precedents in this literature:

  • Relative L2L_2 on fields, as in Augenstein et al. (2023) and Ma et al. (2025); other field surrogates normalize L2L_2 or L1L_1 errors differently (Li et al., 2021; Gu et al., 2022; Chen et al., 2022; Lim and Psaltis, 2022). It is dominated by strong fields.
  • Median per-probe error also checks weak fields, which matter for coupling and interference. James et al. (2026) use the same median of per-point relative error for magnetostatic fields, because per-point relative error diverges where the true field vanishes.
  • riRMSE is the RMSE over the real and imaginary parts of complex S-parameters, as in Sjödin et al. (2025); other S-parameter surrogates report absolute or relative errors, or R2R^2 (Karahan et al., 2024; Liu et al., 2024; Sahu et al., 2025; Kim et al., 2024).
  • mag-wMAE measures magnitude error in dB, the unit RF specifications use, as do Chen and Tan (2021) for insertion loss. Its weighting is not standard. We chose a −20 dB midpoint for uses such as antenna matching, where the exact depth of a deep dip matters little; Table 5 of the revision reports the error at every magnitude, including below −40 dB.

Classical computational EM has a validation standard, Feature Selective Validation (IEEE Std 1597.1), but it compares two curves, such as a simulation and a measurement, with scores designed to agree with engineers' visual judgment, and is not used in learned-surrogate work. The revision adds this survey as Appendix H.

(iii) Simulated data only

Evaluating against the simulator rather than physical measurements is the standard practice for learned physics surrogates: most work in this area trains and scores against the solver it replaces (Li et al., 2021; Pfaff et al., 2021; Takamoto et al., 2022; Gu et al., 2022; Chen et al., 2022). Our goal is to replace the simulator, so the simulator is the reference. Comparing against measurements would mix our error with the simulator's own modeling error and with fabrication variation, and those are present whichever of the two is used.

(iv) Cost compared with the simulator

Per board, both on one NVIDIA A10G:

Our modelPalace (FEM)
S-parameters, all ports, 101 frequencies0.13 s275 s (median)
Peak GPU memory2.9 GB7.9 GB (median), 9.5 GB (p90)

The model predicts a board's S-parameters about 2,100 times faster than the solver and uses about a third of the memory, so our model provides a significant computational advantage over traditional simulation. The revision reports these numbers in a new Results subsection (Sec. 4.5).

Thank you for the clarifications, especially regarding the comparison with the simulator. Amazing gain! However, I'm still concerned about the way (3) is constructed -- why multivariate student-t distribution. As in many learning cases, nature per se is very complicated hence all models are wrong (quoting George Box), since any model would fail to completely express the full complications imposed by the nature. However, depending on the purposes, some models can be useful. And in this work, the authors chose "multivariate t-distribution" for their modelling. And I was asking the reason for this: Why multivariate t-distribution? And it should be in relation with some sort of (physical) characteristics of EM.

In other words, the authors could have (simply) chosen multivariate Gaussian distribution, rather than student-t distribution. And this gives some nature questions: Why student-t? Is it because nature gives more of a fat-tailed-behavior to EM? Or is it related to some epistemic uncertainty associated with covariance matrix of multivariate Gaussian due to lack of simulation during training? (by noting that multivariate t-distribution can be obtained as a posterior of multivariate Gaussian with uncertain covariance matrix; though, given that the authors are using sufficiently many simulated data, I'm not sure this kind of Bayesian justification is sensible ..).

In short, I was expecting to see some EM-related, physics-based, justification for multivariate-t distribution for the modelling. But currently it seems that student-t is some mere choice of "one" of the models, among many. Without such justification, I'm not sure whether the authors' approach can really position as a foundational model in EM.

AuthorsOpenReview ↗

Loss function clarification

Thank you for your response and further clarification.

Early in development, we trained our model with a standard MSE loss and observed that the distribution of residuals (pooled over field probes) was heavy-tailed. Our initial adoption of a Student-tt-inspired loss was an attempt to account for this empirical observation of heavy tails, and was not driven by any a priori theoretical argument guided by the physics of EM. The choice that is motivated directly by EM is the scaling of the H\mathbf{H} residual by a factor of η0\eta_0 (the impedance of free space) to match the units and scale of the E\mathbf{E} residual, which gives the largest single improvement in Table 2.

However, we appreciate you pressing on the point of whether the complexity of the Student-tt is strictly necessary for this model's performance, since this motivated us to conduct the follow-up experiment described in Appendix E and in our earlier reply. In it, we trained a model with a Gaussian loss (while keeping the per-probe scale) and found that it performs comparably to the Student-tt loss in distribution and is better or tied out of distribution. Thus, we determined that the performance improvement over MSE comes from the learned per-probe scale, not from Student-tt's heavy tails. While we are unable to retrain our large main models during the rebuttal period due to time and budget constraints, we agree that future work should consider adopting the simpler Gaussian form as a default, and test whether this conclusion holds at the full model scale.

Our intuition for why per-probe scaling (in both the Gaussian and Student-tt forms) is necessary comes from the fact that the fields on a board span many orders of magnitude (about 80 dB; Fig. 5c–d), so a single scale does not fit them all well. This is also likely why the pooled residuals looked heavy-tailed under MSE: mixing probes with very different error scales gives heavy tails, which is the scale-mixture view of the Student-tt that you mention, with the mixing coming from the spread of field magnitudes rather than from uncertainty about the covariance.

We do not believe the choice of loss function used during training is central to whether the trained model can be regarded as a foundation model. Instead, we adopt the common definition of a foundation model as one that is pretrained on broad data and can be adapted to new tasks. We demonstrate these capabilities for our own model through generalization to out-of-distribution device families (Table 1), and fine-tuning to a new target with fewer examples and far less compute than training from scratch (Sec. 4.2: with 128 boards it beats the best from-scratch run, which used 64 times as many boards and about 330 times the compute, not counting pretraining).

Reviewer_3TmrOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies time-harmonic electromagnetic surrogate modeling for 3D PCB and package structures. It introduces approximately 250k simulations from 25 template families and a 340M-parameter neural operator that jointly predicts complex E/H fields at arbitrary query positions and S-parameters across frequencies and port pairs. The model combines occupancy-sparse voxel patches, query-based decoding, relative RoPE in continuous physical coordinates, and an impedance-scaled robust field objective. EMVal evaluates near fields and S-parameters on ID designs and two held-out geometry families. Joint supervision leaves ID S-parameter performance approximately unchanged while reducing OOD riRMSE from 0.153 to 0.102 and magnitude-weighted MAE from 0.940 to 0.489 dB. Smaller-scale component ablations and comparisons with GINO and Transolver supplement this result.

Critical strengths
  1. The joint field/response formulation produces a consequential transfer benefit. Table 1 controls model scale and training corpus: ID S-parameter accuracy changes little, while OOD riRMSE and magnitude error decrease by approximately 33% and 48%. This directly supports the central empirical claim that field supervision improves cross-family representations, beyond demonstrating ID curve fitting (Sections 3.6 and 4.1). The more distinctive contribution is unified field/port-response learning across multiple 3D PCB/package families and evidence of cross-family benefits from joint supervision, beyond earlier device-specific or scattering settings.
  2. The representation, objective, and evaluation are thoughtfully aligned. The model handles 3D material geometry, port conditions, and continuous spatial queries. Reporting both global relative L2 and local-q50 exposes the genuine tradeoff between MSE and Student-t rather than presenting the robust objective as uniformly superior. Three-seed component and architecture studies provide useful supporting evidence (Tables 2–3).
Critical weaknesses
  1. Family-level evidence is insufficiently detailed to assess the consistency of the reported OOD benefit. Section 3.1 describes 25 training families and approximately 2k OOD designs from two additional, excluded families. It provides representative device categories and examples, but not an explicit family-by-family inventory, counts, or separate results for the two OOD families. The pooled result therefore does not show whether both held-out families benefit similarly. The fixed footprint, port range, and frequency range are acknowledged limitations of scope, not evidence that the reported evaluation is invalid (Sections 3.1 and 6).
  2. The main model configuration is not specified in enough detail for reproduction from the manuscript alone. Sections 3.3–3.4 give the 340M parameter count, voxelization, patching, query interface, objective, optimizer, and sampling schedule, but do not state the depths, hidden widths, and attention-head counts of the main system/query encoders and decoder, or the convolutional-stem configuration. Appendix B specifies several baseline configurations, which does not determine the main model configuration. In addition, training-resource reporting in Section 3.7 does not provide inference latency, so the practical acceleration relative to FEM remains unquantified.
Questions for authors
  1. Please provide the exact training/OOD family inventory, family counts, and separate results for the two held-out families, or identify an existing attachment containing them. Do both OOD families show a joint-supervision benefit?
  2. Please provide the main model configuration, including module depths, hidden widths, attention heads, and convolutional stem, or point to a released configuration. If inference measurements are available, please report geometry-encoding time and cached-encoding field-query/frequency-sweep time, together with the query workload, hardware, and FEM timing scope.
3 comments

Thank you for the careful review and the positive assessment. We appreciate that you called the transfer benefit of joint supervision consequential, citing the controlled comparison in which field supervision reduces held-out S-parameter error by about a third to a half, and that you noted our use of both relative L2L_2 and local-q50q_{50} to show the tradeoff between field objectives.

W1 / Q1. Held-out families

The held-out OOD families are two planar copper-strip geometries: crossed strips (two perpendicular strips that overlap in a plus, T, or L shape; 1k designs) and fishbones (one spine crossed by several parallel bars; 1k designs), each with either 1 or 2 ports. Both families benefit from field supervision:

Held-out familyModelriRMSE [95% CI]mag-wMAE (dB) [95% CI]
Crossed stripsfield + S0.046 [0.044, 0.048]0.197 [0.187, 0.207]
S only0.082 [0.079, 0.085]0.389 [0.367, 0.409]
Fishbonesfield + S0.157 [0.153, 0.162]0.781 [0.749, 0.816]
S only0.223 [0.218, 0.229]1.490 [1.432, 1.554]

Joint supervision reduces riRMSE by 44% on crossed strips and 30% on fishbones, and mag-wMAE by about half on both.

The revision reports these per-family results in Appendix B (Table 4) and lists every design family in Appendix C (Table 6).

W2 / Q2. Model configuration and inference cost

The configuration of the 340M model, which the revision adds as Table 7 in Appendix D:

ModuleConfiguration
Voxelization2563256^3 voxels (~31 µm) across the 8 mm board; 16316^3-voxel patches
Patch stem3 convolutional layers, kernel 3; (channels, stride) = (24, 1), (48, 2), (96, 2)
System encoder9 blocks, width 1088, 17 heads, FFN ratio 4, QK-norm, 3D RoPE
Query encoder3 self-attention layers, width 1088, 17 heads, FFN ratio 4
Query decoder8 cross-attention layers, width 1088, 17 heads, GEGLU feed-forward
Field headlinear map to 12 field components and the log-scale ℓ\ell
S-parameter headMLP with tanh output
Parameters340,341,474

Inference cost

Measured on one NVIDIA A10G, bf16, batch size 1, median over 30 held-out boards:

ModelPalace (FEM)
Geometry encoding, once per board and driven port0.05 s
Fields at 10k probes, one frequency, one driven port, from an existing encoding0.23 s
S-parameters, all ports, 101 frequencies, from geometry (encoding included)0.13 s275 s (median)

The encoding is reused for every later field query on the same board and port, so the first field query on a new board takes 0.27 s in total. The Palace time is the median per board on one A10G, covering meshing and an adaptive 1–20 GHz sweep. The model predicts S-parameters about 2,100 times faster. The revision reports these timings in Sec. 4.5.

Reviewer_3TmrOpenReview ↗

Follow-up after author response

Thank you for the detailed response. The per-family results directly address my concern about the consistency of the OOD improvement: both held-out families benefit from joint field supervision, and the reported values are consistent with the aggregate results in the original submission. The additional model configuration addresses my main questions about the architectural specification. The inference timings, together with the hardware, query workloads, and FEM timing scope, also make the practical efficiency substantially clearer. I consider my main concerns addressed by the information provided. These clarifications strengthen my positive assessment of the unified field/S-parameter formulation and the demonstrated benefit of joint supervision. I maintain my recommendation of 3 (Weak acceptance).

Thank you for the follow-up and for confirming that the per-family results, model configuration, and inference timings address your concerns. The revision includes these in Appendix B (Table 4), Appendix D (Table 7), and Sec. 4.5.

Comments on the paper

2 comments

Thank you all for the careful reviews. We have uploaded a revised PDF, with new and changed text in blue. This comment summarizes the changes.

What the reviewers found valuable

  • The controlled comparison in Table 1: for two models of the same architecture, scale, and training data, adding field supervision lowers held-out S-parameter error from 0.153 to 0.102 riRMSE and from 0.940 to 0.489 dB mag-wMAE. Reviewer 3Tmr called this "a consequential transfer benefit" and Reviewer C9sM "the paper's strongest contribution."
  • The problem and approach: Reviewer GeG2 called an EM foundation model an important problem and noted that "it appears that this is indeed the first attempt to build such a model for EM systems"; Reviewer Kbbt found the cross-attention design for predicting both fields and S-parameters "timely and sensible."
  • The evaluation: reporting both relative L2L_2 and local q50q_{50} exposes the tradeoff between field objectives (Reviewers 3Tmr and C9sM).

New experiments

  • Fine-tuning on a new target (GeG2, C9sM; Sec. 3.6, Sec. 4.2, Figure 4, Appendix G). We fine-tune the pretrained 340M models to predict resonance, a target they never trained on, using 128 to 8,192 boards from the training families, and score them on the two held-out families. The jointly pretrained model separates resonant from non-resonant boards better at every training-set size (AUROC about 0.8, against at most 0.76 for models trained on the target from scratch). With 128 boards it already exceeds the best from-scratch run, which used 64 times as many boards and about 330 times more compute (not counting pretraining).
  • The Student-tt normalizer (C9sM, Kbbt; Appendix E, Table 8). With the full likelihood, ν\nu falls to its lower bound and field error roughly doubles. With ν\nu fixed at 12, results are close to the default except for higher out-of-distribution S-parameter error. A Gaussian with the same learned per-probe scale is comparable in distribution and better or tied out of distribution, so the gain over MSE comes from the learned scale, not from heavy tails.
  • Inference cost (3Tmr, Kbbt; Sec. 4.5). On one NVIDIA A10G, the model predicts a board's S-parameters for all ports at 101 frequencies in 0.13 s, about 2,100 times faster than the FEM solver (median 275 s), with about a third of its peak GPU memory.
  • Results for each held-out family (3Tmr, C9sM; Appendix B, Table 4). Joint supervision lowers riRMSE by 44% on crossed strips and 30% on fishbones, and mag-wMAE by about half on both.
  • S-parameter error by true magnitude (C9sM; Appendix B, Table 5). Joint supervision lowers the error in every magnitude bin, including below −40 dB, which the weighted metric de-emphasizes.

Added detail

  • Design families with board counts (Appendix C, Table 6) and the full model configuration (Appendix D, Table 7).
  • Metrics in prior EM surrogate work (Appendix H).
  • Compute used by each study (Sec. 3.7).

Revised claims

  • Sec. 4.1 and the abstract: field supervision slightly increases in-distribution S-parameter error while reducing it substantially out of distribution; the abstract now says joint supervision "largely preserves" in-distribution accuracy (GeG2).
  • Abstract and Sec. 3.4.1: Eq. (3) is described as a heteroscedastic objective of Student-tt form rather than as robust (C9sM, Kbbt).

Correction to Table 3

While preparing the revision, we audited the Table 3 baselines. Transolver was evaluated with 512 query points per pass but trained with 2,048, and in its unified mode each prediction depends on how many queries share the pass. We fixed this, sized all three models to 52M active parameters (the scale of our Table 2 ablations), kept the same augmentation for all, tuned the baselines' learning rates, and reran each with three seeds. The ranking holds: our model has the lowest mean error on every metric in both evaluation tiers, followed by GINO and then Transolver; Transolver improves in distribution but stays close to the zero-prediction baseline out of distribution. Sec. 4.4 and Appendix F give the revised table, the baselines' configurations, and the learning-rate selection.

AuthorsOpenReview ↗

Summary of the discussion

We thank all reviewers for the discussion. A brief summary:

  • 3Tmr (3): confirmed that the per-family results, model configuration, and inference timings address their main concerns.
  • Kbbt (2 →\rightarrow 3): raised their score after the simulator comparison and our discussion of the loss. In response to their remaining question about the Student-tt, the latest revision adds the MSE run to Appendix E alongside the Student-tt and Gaussian objectives.
  • GeG2 (2): agrees that the paper shows transfer from pretraining. We clarified the scope of our foundation-model claim: time-harmonic EM, circuit-board and package structure inputs, and generalization across geometries and tasks (fields, S-parameters, and resonance properties). Fine-tuning on problems from prior papers remains future work.
  • C9sM (2): our response reports results for each held-out family, the Student-tt normalizer experiments, and S-parameter error by true magnitude. We have not yet heard from this reviewer whether our response addresses their concerns.

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

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