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Under review as a conference paper at ICLR 2027

MIR-QBIC: A High-Q All-Dielectric Metasurface Benchmark for Mid-Infrared Biosensing

Abstract

Deep learning is advancing nanophotonic device design, yet learning the sharp, high-quality-factor (Q) resonances relevant to molecular sensing remains constrained by data: these features are computationally demanding to resolve and annotate, and public datasets capturing them remain scarce. We introduce MIR-QBIC, an open dataset of 13,741 rigorous coupled-wave analysis (RCWA) simulations of Ge/CaF2 quasi-bound-state-in-the-continuum (quasi-BIC) metasurfaces operating over 5-8 um. Each structure is described by four interpretable geometric parameters and paired with broadband and adaptively resolved transmission spectra, together with resonance wavelength, radiative quality factor, dip depth, and Fano descriptors. The responses span a broad linewidth range with a sparse high-Q tail, and a substantial fraction of resonances lie in the amide-I region motivating mid-infrared biosensing. Numerical verification, frozen quality-factor-stratified splits, and a physics-aware evaluation protocol support systematic study of scalar prediction, adaptive-window reconstruction, and high-Q generalization. Six classical and neural baselines demonstrate the benchmark's utility and difficulty: similar quality-factor accuracy can accompany substantially different adaptive-window errors, while high-Q training coverage improves generalization without resolving the sharpest responses. MIR-QBIC provides a shared, physically grounded resource for advancing narrow-feature, high-dynamic-range spectral learning.

Primary area:
datasets and benchmarks
Keywords:
Datasets and benchmarks, Scientific machine learning, All-dielectric metasurfaces, High-Q resonances, Spectral reconstruction.

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_qxGvOpenReview ↗
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Paper summary

This paper presents a dataset of simulated transmission spectra for a family of dielectric structures and compares models that predict these spectra from geometry. The focus is on narrow resonances, with numerical validation and experiments examining how adding high-Q training examples affects prediction.

Critical strengths

The focus on narrow resonances is useful, since these are difficult both to resolve numerically and to predict. Providing broadband and adaptively resolved spectra makes this a potentially useful shared resource. The convergence checks and examination of how adding high-Q training examples affects prediction are also welcome.

Critical weaknesses
  1. My main concern with the spectral error is whether it tells us that the resonance is at the correct wavelength and has the correct linewidth. From a spectroscopy perspective, getting the shape correct but the peak position wrong can still yield a poor spectrum. Appendix E examines this separately, and the model ranking changes, which makes its limited coverage consequential.

  2. Coming from electronic-structure calculations, my first question is how well converged the reference data are, particularly in the most difficult cases. The dense-sampling check stops around Q=1357Q=1357, whereas the dataset reaches about 12600. The separate solver-convergence checks are welcome, but median errors may hide problems in precisely the cases the benchmark is intended to study.

Questions for authors
  1. Why is the physical-wavelength evaluation in Appendix E not part of the main evaluation using the full set? Similarly, why is the wavelength error in Table 4 calculated only for predictions within 100 nm of the reference? I would like to see statistics across all predictions, together with the fraction falling within the stated tolerances.

  2. Can more validation at the upper end of the Q range be shown? For both spectral sampling and solver convergence, I would like to see the larger discrepancies and how they depend on Q.

  3. I may be missing something, but I would interpret FWHM error as an error in the physical linewidth. Appendix C instead seems to describe a span on a fixed reference grid. Does this include errors in the predicted physical width? If not, the figure label should make this distinction clearer.

  4. I understand the reason for starting with lossless materials, but how much do the narrowest features depend on this approximation? Would wavelength-dependent complex refractive indices substantially broaden them? This would help clarify the connection to the proposed sensing application.

1 comment

Thank you for the constructive feedback. We now evaluate the full eligible test set, report the larger discrepancies in the high-Q tail, and clarify what the width diagnostic and lossless model measure.

Q1. Table 3 now reports placement-aware RMSE on all 1,805 fine-eligible samples over five seeds, with one deterministic fit for SVR. It also reports unconditional wavelength RMSE on all 2,070 test geometries, so large wavelength errors are included.

The within-100 nm conditional error remains a secondary measure of precision among predictions already close to the reference. Table 7 reports the fraction of scalar predictions within 100 nm and, separately, detection of the broadband minimum within ±50 nm. Appendix C.2 defines both measures and their denominators. The 976 boundary-clipped records omitted from the earlier canonical-grid comparison are included in the new evaluation (Appendix E.2).

Q2. We added checks on 30 high-Q cases, including cases with Q ≥ 8,000. Table 6 reports the median, 90th percentile, and maximum discrepancy within each Q bin (Appendix B.4).

For the order-11/order-17 comparison, these RMSE statistics are 0.1646, 0.4026, and 0.4562. Comparing the interpolated 40-point spectra with fresh production calculations gives 0.0263, 0.1101, and 0.2639. The median sampling discrepancy rises from 0.0193 in the lowest bin to 0.1436 in the highest. These results show why the high-Q tail retains low-reliability flags.

Q3. You are right about this distinction. The diagnostic measures a half-depth span on the reference detuning grid; it does not measure physical FWHM error or use predicted Q to convert the span into a physical width. We now state this explicitly in Appendix C.3 and clarify the historical FWHM labels in the Figure 7 caption. The placement-aware reconstruction does use predicted position and linewidth scaling (Appendix E.1).

Q4. Our lossless model reports radiative Q. Absorption and other losses reduce total Q through the additional decay channels in Equation 21 (Appendix G). Germanium is transparent over 5–8 µm, while CaF₂ approaches its absorption edge near the long-wavelength end of the band (Section 7), so the assumption of modeling it as lossless is reasonable.

Complex, wavelength-dependent indices can broaden and shift the resonances. We have not quantified that effect, as experimental studies are out of this paper's scope.

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Paper summary

This paper introduces a dataset of simulated metasurfaces, i.e. surfaces made of nano structures designed to resonate at specific wavelengths. Structures with high quality factors Q have narrow resonance bands; hence, the authors argue that the uniformly sampled spectrum provided by existing datasets may fail to capture the resonance for large values of Q. They thus propose a new dataset that pairs each global spectrum with an additional, more finely resolved spectrum centered around the resonance, and with the explicit values of the resonance parameters. They introduce a simple family of metasurfaces described by four geometric parameters, and sample 13,741 different metasurface configurations along with their ground truths, covering a wide range of quality factors Q. The authors then train six baselines to predict their ground truth from the 4 scene parameters, and conclude that sharp resonances remain hard to predict.

Critical strengths

I find the construction process of the dataset to be principled. As the authors' interest leans toward sharp resonance metasurfaces, their 4 parameters parameterization provides a simple framework for experimenting over a large range of values for Q. The solver settings are explicit, and the resulting simulations are validated by cross-checking against another RCWA implementation. They also propose a new metric, the adaptive-window RMSE, to isolate the quality of the predicted resonance profile, independently of the location and the size of the resonance band. Finally, I appreciate that the authors share the dataset, the baselines and the evaluation code.

Critical weaknesses

While I find the methodology to generate the dataset solid, I find the authors' motivations for building this dataset poorly supported. The authors say in the introduction that "A remaining need [...] is an open geometry-to-spectrum collection" (L042), but unfortunately they do not provide references showing evidence that this gap actually holds anyone back. (Q1) The paper presents the dataset as both a training resource and a benchmark, but I think it does not properly demonstrate either role.

Motivations. To motivate their dataset as a new training resource, the authors say that “Learning these responses requires data that resolve their narrow spectral structure” (L032). But such data can be generated on demand with previously existing solvers: the authors themselves generated their data with TORCWA. They state that the main motivation for pre-computing a dataset is cost (L046, L105), yet this motivation is never supported: I found no measured generation times. (Q2)

Downstream tasks. I find the lack of properly tested downstream applications concerning. After training, the only downstream task evaluated by the authors is forward prediction (L253). This is inconsistent with the title of the paper, which explicitly mentions "mid-infrared biosensing" but the authors never test it or show that their proposal fits this task (Q3). Experiments with inverse design are also standard and have been applied in several cited works (Ren 2022, Wang 2024), but are not conducted in the paper. (Q4) Regarding forward prediction, experiment in Section 6.1 shows that adding high-Q samples to training helps on the high-Q test. But that is not surprising: similar training and testing datasets logically reduce the domain gap. Moreover, as the authors acknowledge it, the gain in this experiment is confounded with the training-set size, while it would have been easy to remove this confounder (Q5).

No comparison with existing datasets. If the dataset’s role is to provide a new benchmark, then the authors should show that their dataset brings something new. First, the authors never show that their dataset is coherent with existing benchmarks. Evaluating the six models of Table 4 on a task common to their dataset and existing ones, such as spectrum prediction, and showing that the leaderboard stays roughly consistent across datasets would support that their new benchmark is coherent with each model's established performance. (Q6) Second, and more importantly, the paper never demonstrates what this dataset reveals that others do not. In Table 4, the leaderboard on adaptive-window RMSE is almost identical to the one on broadband RMSE, hence it does not confirm that their dataset reveals a new performance axis that others do not. The authors should conduct additional experiments to provide supporting evidence that their new evaluation complements existing ones. (Q7) The result "all models struggle at high Q" discussed in Sec 5 does not establish anything on its own.

The storyline. I believe the storyline of this paper needs an important rewrite. The introduction should give context: it should say what exists, why it is not sufficient, why it matters, and how it differs from close works. Here, the authors’ survey of the literature is poor, and they fail to support why existing resources are insufficient with numbers. As a quick diagnostic, I counted 15 references in this paper, all fitting in one page. Close works have 3 to 5 times more: 43 for Deng et al. (2021), 80 for Kim et al. (2023), and 59 for Lilja et al. (2026). While reference count is not a proper metric on its own, it suggests that the paper is insufficiently positioned in the literature.

Furthermore, as a non-specialist in nanophotonics, I find the paper notation-heavy, and advanced terms are not defined. The abstract and introduction chain the jargon terms (quasi-BIC, radiative Q, Fano descriptors) without explaining them. I believe papers at a general ML conference should do their best to be accessible to non-specialists, which the authors fail to do here.

Minor comments. Table 4 has no standard deviations: it is unclear whether close results, such as CNN (0.124) vs Coordinate (0.127), are due to noise (Q8).

Conclusion. Overall, despite finding this dataset to be a well-crafted resource, I find the narrative to be insufficiently justified, and more importantly, the necessity of this dataset is not demonstrated. Although I acknowledge the quality of the authors’ methodology, I lean towards a clear reject: I find that the lack of context, motivation and evidence, and the lack of accessibility make the paper not acceptable in its current form. I believe it needs a substantial rewriting to position the dataset in its context, with a coherent storyline, and to establish its relevance. I am open to re-evaluating my score, conditional on an intensive rework from the authors.

Questions for authors
  • Q1. Could you provide the range of Q covered by existing datasets, such as ADM, to support your claim of a gap in the literature?
  • Q2. Could you report the computation time required to generate the dataset?
  • Q3. Could you show that a model trained on your dataset is useful for mid-infrared biosensing?
  • Q4. Could you show experiments on a simple design task, such as finding geometries with a resonance in a narrow range of quality factor and wavelength, compared to a baseline that does not use the dataset (for example, direct optimization through TORCWA)?
  • Q5. Could you fix the coverage study of Section 6.1, by using an identical training-set size?
  • Q6. Could you evaluate the methods of Table 4 on an existing dataset, such as ADM, on a common task such as spectrum prediction, and check whether the ranking is consistent with the one on your dataset?
  • Q7. Could you provide experimental evidence that your dataset reveals something about models that existing datasets do not?
  • Q8. Could you report standard deviations in Table 4, and use a statistical test to put in bold models that are not significantly different from the best one?
1 comment

Thank you for the constructive feedback. We added dataset comparisons, controlled experiments, and measured generation costs and rewrote the introduction and related work.

Q1. We analyzed ADM’s public data (Deng et al., 2021) on its native 2,001-point grid, retaining peaks with at least four grid points across their FWHM. Apparent Q has a median of 44, a 95th percentile of 169, a 99th percentile of 198, and a maximum of 240. These are sampled absorptivity-peak estimates.

ADM covers 100–500 THz at 0.2 THz spacing. Requiring four samples across an FWHM gives an approximate resolvable Q of 375 near the band center; the corresponding estimate for QNM-Net is about 240.

MIR-QBIC contains 604 records above Q = 1,000, reaching about 12,600, through adaptive sampling around each resonance. The numerical sensitivity of these records is reported in Appendix B.4.

Section 2 and Table 1 now compare these resources alongside RIDL, Metaformer, and Wei and Geng, covering spectral band, material, sampling, annotations, placement-aware evaluation, and availability.

Q2. Section 3.1 reports approximately 3,574 GPU-hours, at about 4.5 minutes per sample on an RTX 4090 and 9.4 minutes on V100 nodes. This includes the 13,741 released records, verification sweeps, and excluded geometries. Researchers can use the computed and annotated data without repeating this work.

Q3. The biosensing connection is resonance design near molecular absorption bands: 4,212 of 13,741 resonances (30.7%) lie in the 5.9–6.5 µm amide-I interval. We evaluate forward prediction of resonance position, radiative Q, and nearby spectral profiles (Sections 3.4 and 4.3).

Downstream biosensing experiments and analyte-response measurements are outside this release (Section 7; Appendix G).

Q4. Developing and benchmarking inverse-design algorithms is outside the scope of this current dataset and forward-benchmark study. Our experiments establish reference performance for forward prediction; we claim neither an inverse-design method nor an optimization advantage over direct TORCWA optimization. Our geometry–response pairs will provide, when released, the data needed for researchers to enable further problem formulations. To be noted, this dataset is being leveraged for the formulation of inverse design that is aimed for a separate paper.

Q5. Both training sets now contain 7,692 records. Across five paired seeds, high-Q log₁₀ Q RMSE drops from 0.559 to 0.218 for Coordinate and from 0.701 to 0.234 for MLP. Both improve in every seed pair, and the gains remain after reliability filtering (Section 6.1; Appendix F.2).

Q6. We ran all six baselines on ADM using its official split, held-out validation, and training-only normalization. Gradient-trained models use the selected MIR-QBIC backbones and training settings, spectrum-only outputs, and five seeds. SVR uses one deterministic fit.

The comparison supports the requested consistency check: the five gradient-trained models have identical rankings across datasets (Spearman ρ = 1.000). Including SVR gives ρ = 0.943, with only SVR and Transformer swapping places. Coordinate ranks first on both. Table 12 reports the full results, and Appendix H describes the comparison protocol.

Q7. Placement reliability changes the model ranking. Coordinate has the lowest spectral RMSE, but Transformer places resonances more reliably: 28.5% of its predictions miss by more than one characteristic linewidth, compared with 34.8% for Coordinate. Even within the quarter of Coordinate predictions with the lowest broadband errors, 15.2% miss by more than one characteristic linewidth (Section 6.3; Appendix E.1).

We also checked what uniform sampling loses using ADM’s densely sampled spectra (Section 6.2; Appendix I; Table 13). At 50 uniform points, narrow peaks lose a median 76% of their amplitude, compared with 24% for broad peaks; 78% of narrow peaks shift by more than their reference width. Yet whole-spectrum RMSE is similar for the two groups: 0.034 versus 0.028. At 90 uniform points, matching MIR-QBIC’s total sampling budget, amplitude losses remain 69% versus 13%. Increasing the point count alone therefore does not preserve narrow features.

The paired spectra also let us test a training constraint directly. Adding consistency with resonance weighting reduces broadband RMSE by about 10% and adaptive-window RMSE by 4%, without changing the architecture (Appendix F.5; Figure 10).

Q8. Table 3 now includes five-seed means and standard deviations for gradient-trained models; SVR uses one deterministic fit. CNN’s log₁₀ Q RMSE is 0.124 ± 0.005, compared with Coordinate’s 0.127 ± 0.005.

Sections 1–2 now explain quasi-BIC, radiative Q, and Fano asymmetry in plain terms and compare MIR-QBIC with the closest resources.

Reviewer_CN53OpenReview ↗
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Paper summary

The paper introduces MIR-QBIC, a dataset comprising 13,741 RCWA simulations of Ge/CaF₂ quasi-BIC dimer metasurfaces operating in the 5–8 µm wavelength range. Each design includes four geometric parameters, a 50-point broadband spectrum, a 40-point resonance-adaptive spectrum, and labels for resonance wavelength, radiative quality factor, resonance depth, and Fano parameter (Sec. 3). The simulations undergo numerical validation (Table 3), and fixed in-distribution and high-Q evaluation splits are established. Six baseline models are benchmarked, with the coordinate-based model achieving the lowest spectral RMSE (Table 4). Incorporating high-Q samples into the training set substantially reduces prediction error for high-Q designs, lowering the log-scale Q RMSE from 0.56–0.62 to 0.23–0.27 dex (Sec. 6.1).

Critical strengths

Verification and release are careful. There are checks against a higher Fourier order, a finer grid and a second solver (Table 3), dense 241-point validation (Table 5), Q-reliability flags, fixed splits, and an open-licence release with a loader and evaluator. This makes it a credible, reusable resource.

Critical weaknesses

The main adaptive-window metric does not test where the resonance is placed. The scope and ML novelty are limited for ICLR: one material system, four parameters, lossless simulations and standard baselines.

Questions for authors

Could you make placement-aware RMSE in physical wavelength a primary metric, report it over 5 seeds on all eligible samples, and explain why 976 samples drop out? Could you add a size-matched control for the augmentation study and report high-Q results without the low-reliability samples?

1 comment

Thank you for the constructive feedback. We have now completed the three checks you requested: evaluation on the full eligible test set, a control at the same training size, and an analysis excluding low-reliability records.

Q1. Placement-aware physical-wavelength RMSE is now part of the main evaluation in Section 4.3 and Table 3. It covers all 1,805 fine-eligible test samples over five seeds, with one deterministic fit for SVR. Each predicted profile is placed using its predicted resonance wavelength and Q; outside that window, the reconstruction uses the predicted broadband spectrum (Appendix E.1).

The 976 records were excluded only from the earlier comparison that required a common detuning grid, because their windows were clipped at the band boundaries. They were always included in the dataset and main adaptive evaluation. The new placement-aware score includes them all (Appendix E.2).

Q2. We repeated the study with 7,692 training samples in each setting: 7,692 low-Q records versus 6,318 low-Q plus 1,374 high-Q records. Both use the same validation set (1,650), high-Q test set (1,375), model configurations, and training budget. Across five paired seeds, high-Q log₁₀ Q RMSE drops from 0.559 to 0.218 for Coordinate and from 0.701 to 0.234 for MLP. Every seed pair improves.

We then excluded the 304 low-reliability test records with Q ≥ 1,000 and rescored the same predictions on the remaining 1,071 cases, without retraining. The improvement remains. These results show that high-Q coverage helps at fixed training size and that the gain also holds after reliability filtering (Section 6.1; Appendix F.2).

Comments on the paper

1 comment

We thank all reviewers for their constructive feedback. The placement-aware evaluation now covers all 1,805 eligible test samples, and the main results include unconditional wavelength errors and variation across seeds. We also added size-matched high-Q controls, further numerical checks on the high-Q tail, and a comparison with ADM. Sections 1–2 have been rewritten to explain the physical terms and show more clearly where MIR-QBIC differs from existing resources (Table 1).

Our contribution is the dataset and the work needed to make it usable: generating the spectra, resolving and annotating the resonances, checking numerical reliability, and providing a reproducible evaluation protocol. We deliberately kept one lossless material system and four geometric parameters to study narrow resonances under controlled conditions. The standard baselines establish reference performance, while the paired spectra, reliability flags, frozen splits, loader, and evaluator allow others to build on this work.

We want researchers to be able to study these difficult responses without first repeating the simulation and annotation effort. We hope MIR-QBIC will be useful for that purpose, and we ask the reviewers and chair to reconsider the paper based on the added evidence and its contribution as a dataset paper only.

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