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Paper summary
The paper studies higher-frequency wave-field prediction when only lower-frequency supervision is abundant and higher-frequency (target) supervision is scarce. The authors first show empirically (Fig. 1) that cross-frequency transfer is asymmetric: amplitude similarity across frequencies decays much more slowly than phase coherence, both in ground truth and in an FNO trained on lower frequencies and extrapolated to higher ones. This is formalized with a regional complex-field error decomposition (Proposition 1) and a frequency-sensitive upper bound (Corollary 2) that separate the error into an amplitude-mismatch term and a phase-mismatch term whose argument scales with frequency.
Motivated by this, APEX (1) freezes a lower-frequency-trained FNO and uses its log-amplitude output at the target frequency as a "coarse amplitude anchor"; (2) builds a lightweight, geometry-aware "phase prior" from a truncated sum of plane-wave-like terms with a domain-adaptive reference phase coefficient (Eq. 13), intended as a Green's-function-inspired surrogate for the oscillatory phase; and (3) uses both as conditioning signals for a U-Net-based conditional flow-matching model that generates the target complex field (log-amplitude + sin/cos phase representation). The pipeline is evaluated on three synthetic benchmarks (SimpleWave, Helmholtz, Maxwell) at three extrapolation gaps (HF20/50/100), against LF-extrapolation, fine-tuned, and jointly-trained FNO/HNO/CFM baselines, plus an ablation removing each conditioning signal and a sensitivity study over the HF supervision ratio.
Critical strengths
1. The transfer-asymmetry observation is a useful empirical framing, and Proposition 1 cleanly isolates where the two field components enter the error.
Separating amplitude mismatch (direct term) from phase mismatch (an oscillatory term with frequency-scaled argument) in Eq. 10 is a clear way to state why phase, not amplitude, should be the harder quantity to extrapolate, and it motivates the architecture directly rather than being decorative.
2. The method is simple and the components are well-matched to the stated problem. Freezing a cheap, already-trained LF model as a structural anchor, rather than trying to make a single network transfer the whole complex field, is a reasonable and backbone-agnostic design choice (Sec. 3.2 states this explicitly), and the ablation in Table 2 does show both conditioning signals contribute on the one benchmark where the ablation is reported.
Critical weaknesses
W1. The theoretical results do not explain the observed asymmetry; part of it is close to tautological given how phase similarity is measured.
Proposition 1 is a geometric identity (law of cosines applied to the amplitude-phase decomposition) and is correct, but it does not establish why phase mismatch should grow faster than amplitude mismatch with frequency — it only shows that if grows with , the phase term is weighted by inside a . Corollary 2 is explicitly flagged by the authors as "explanatory rather than tight" and assumes bounded amplitudes, so it adds little beyond restating the same point. Neither result shows that itself grows with the extrapolation gap; that claim rests entirely on the empirical similarity measures in Fig. 1, which is a different kind of evidence from the "formalize this asymmetry" framing in the text (p.4).
Moreover, the phase-similarity metric itself (Eq. 6, phase-factor coherence) is close to guaranteed to decay faster than the cosine-based amplitude similarity (Eq. 5) once travel-time differences reach , simply because phase is -periodic and enters through : any approximately linear growth of timing error with distance will wrap many times at higher and decorrelate the phase factor, while the same timing error leaves amplitude envelopes comparatively undisturbed because amplitude does not wrap. This is a property of the chosen similarity measures and the oscillatory representation, not a newly discovered property of wave fields. The paper would be stronger if it showed the asymmetry survives under a metric that is not inherently biased toward this conclusion (e.g., unwrapped phase error, or an amplitude metric equally sensitive to small structural shifts).
W2. The phase prior is an ungrounded heuristic, and this is never tested against simpler alternatives.
Eq. 13 defines the phase prior through "dominant propagation paths" with path lengths and fixed coefficients , and a "domain-adaptive reference phase coefficient" . The paper states these are "concrete instantiations... in Appendix D" but the main text gives no indication of how , , or are chosen, nor whether they are hand-tuned per benchmark or genuinely domain-adaptive. Without this, "Green's-function-inspired" is a label rather than a demonstrated connection to Eq. 2's actual Green's function.
More importantly, no ablation isolates whether the specific geometric content of the phase prior matters at all, as opposed to merely providing the flow-matching model with some smoothly-varying, frequency-dependent conditioning signal. Candidate controls that are absent: (a) a random or scrambled phase prior with the same statistics, (b) a naive linear-in- phase ramp with no path/geometry structure, (c) a learned phase prior instead of the fixed analytic surrogate. Table 2's "w/o Phase Prior" shows removing it hurts, which only shows conditioning on some phase-like signal helps, not that the Green's-function construction is the right one or better than a trivial baseline.
W3. Evaluation is confined to small synthetic grids with no real or more complex data, and only one benchmark gets the ablation and supervision-sensitivity study.
All three benchmarks are synthetic, on fixed small grids ( or ), with scalar or single-polarization fields. There is no evaluation on a real-world or higher-resolution/more complex-geometry dataset, which matters because the central practical motivation (Sec. 1) is that "higher-frequency samples... require finer discretization, stricter control, and substantially higher simulation or measurement cost" — a claim about real deployment settings that the experiments never probe. In addition, Table 2 (ablation) and Table 3 (supervision-ratio sensitivity) are reported only for Helmholtz; the paper does not say whether the same ablation trend holds on SimpleWave or Maxwell, so the generality of W2's "both components help" conclusion within the paper's own evidence is unconfirmed on 2/3 benchmarks.
W4. No variance/seed information, and no training/inference cost accounting.
Table 1–3 report single numbers with no standard deviation or seed count. Given that the margins over the best baseline are sometimes modest relative to the baseline spread (e.g., Maxwell HF100: APEX vs. HNO-Joint vs. FNO-Joint — all three within about 3% of each other), it is not possible to assess whether the ranking is stable. The paper also never reports the added training/inference cost of running a frozen FNO plus a U-Net CFM enhancer relative to the single-model baselines (FNO-FT, HNO-FT), which matters for a paper whose motivation is a cost-sensitive data regime.
Questions for authors
- Isolating the asymmetry claim from the metric. Can you show the amplitude/phase asymmetry in Fig. 1 holds under an unwrapped or otherwise non-periodic phase-error metric, to rule out that the effect is an artifact of phase being circular while amplitude is not?
- Phase prior ablation. How sensitive are the Table 1/2 results to the specific choice of , , and in Eq. 13? Does a random-phase or linear-ramp control with matched statistics perform comparably to the Green's-function-inspired prior?
- Generality of the ablation. Do the Table 2 and Table 3 trends (both components help; APEX > CFM-Joint at every supervision ratio) hold on SimpleWave and Maxwell as well as Helmholtz?
- Variance. How many seeds were used for Tables 1–3? Please report mean ± std, particularly for the closest-margin cells (e.g., Maxwell HF100).
- Cost. What is the added training and inference cost of the frozen-FNO + CFM pipeline relative to FNO-FT/HNO-FT?
3 comments
Weakness 3 / Question 3
We have extended the ablation and target-frequency supervision experiments to SimpleWave and Maxwell, complementing the original Helmholtz results.
The additional ablation results in Appendix E.2 (Table 8) further demonstrate the contributions of both components across the three benchmarks. The coarse amplitude anchor supports overall complex-field reconstruction accuracy, while the phase prior provides additional guidance for recovering phase-sensitive oscillatory structures. The results on SimpleWave and Maxwell support the effectiveness of both components beyond the Helmholtz benchmark.
We have also extended the supervision-sensitivity analysis in Appendix E.4 (Table 10). Across all four HF supervision ratios, APEX achieves lower overall H¹ error and higher overall AWPC than CFM-Joint on both SimpleWave and Maxwell, consistent with the Helmholtz results in Table 3.
Regarding the evaluation scope, we acknowledge that the current experiments are limited to simulation-based benchmarks with fixed spatial grids. We have clarified this limitation in Sec. 6 and Appendix F, with real-world measurements, higher-resolution fields, and more complex propagation geometries identified as directions for future work.
Weakness 4 / Questions 4–5
We have added training-seed experiments on Maxwell in Appendix E.5 (Tables 11–12). Given the limited rebuttal period, we focus on HNO-Joint, which has the closest H¹ performance to APEX at Maxwell HF100 among the baselines in Table 1. Both methods are evaluated using three training seeds (0, 1, and 2). The following results report the mean ± standard deviation across training seeds.
| Method | Metric | HF20 | HF50 | HF100 | Overall |
|---|---|---|---|---|---|
| HNO-Joint | H¹↓ | 0.863 ± 0.029 | 0.915 ± 0.022 | 0.962 ± 0.024 | 0.937 ± 0.024 |
| HNO-Joint | AWPC↑ | 0.421 ± 0.025 | 0.335 ± 0.012 | 0.275 ± 0.013 | 0.331 ± 0.016 |
| APEX | H¹↓ | 0.710 ± 0.053 | 0.796 ± 0.035 | 0.950 ± 0.029 | 0.882 ± 0.032 |
| APEX | AWPC↑ | 0.813 ± 0.027 | 0.724 ± 0.034 | 0.633 ± 0.009 | 0.706 ± 0.020 |
At Maxwell HF100, APEX consistently achieves lower H¹ error than HNO-Joint across all three training seeds, with a substantially higher AWPC. These results further support the stability of APEX under different training initializations. We have also added 95% bootstrap confidence intervals for the main comparisons across all three benchmarks in Appendix E.7 (Table 13).
We have additionally included a computational cost comparison in Appendix E.8 (Table 14), reporting total training time, per-sample inference latency, FLOPs, and peak allocated GPU memory on the Helmholtz benchmark. All measurements are conducted on an NVIDIA RTX 4090 GPU.
| Method | Training (s) | Inference (ms) | FLOPs/sample | Memory (GiB) |
|---|---|---|---|---|
| FNO-FT | 503 | 3.582 | 0.0139 G | 0.0613 |
| HNO-FT | 802 | 5.790 | 0.0332 G | 0.0315 |
| CFM-Joint | 16,756 | 1,943 | 18.798 T | 0.207 |
| APEX | 1,468 | 2,301 | 18.930 T | 0.247 |
The training times include LF pretraining and HF fine-tuning for FNO-FT/HNO-FT, and LF pretraining followed by HF enhancement training for APEX. Both APEX and CFM-Joint use 50-step midpoint sampling at inference.
FNO-FT and HNO-FT offer substantially faster inference, but their reconstruction accuracy remains limited under scarce HF supervision. APEX uses additional generative inference computation to achieve higher prediction accuracy, reflecting an accuracy–computation trade-off.
Compared with CFM-Joint, APEX reduces total training time by approximately 11.4× while achieving better reconstruction accuracy. Its two-stage design learns transferable structural information from abundant LF data before training the generative enhancer on limited HF samples. This separation allows the enhancement stage to focus on target-frequency reconstruction, enabling more effective use of scarce HF supervision. Improving the sampling efficiency of the generative enhancer remains a direction for future work, as discussed in Appendix F.
Thank you very much for your constructive review. As the discussion period is nearing its end, we would greatly appreciate any feedback on whether your concerns have been addressed or if further clarification is needed. Thank you for your time and consideration.
We thank the reviewer for the detailed comments and constructive suggestions. We have revised the manuscript to clarify the theoretical interpretation and phase-prior construction, and added experiments on phase-error metrics, ablations, training-seed stability, and computational cost. All modifications are highlighted in blue in the revised manuscript.
We have clarified the role of the theoretical analysis in Sec. 2.3. Proposition 1 provides an exact decomposition of regional complex-field error into amplitude and phase-sensitive contributions. Corollary 2 further characterizes the explicit frequency dependence of the phase-related error bound through travel-time mismatch. These results reveal the different mechanisms through which amplitude and phase errors contribute to higher-frequency prediction, providing a complementary interpretation of the empirical asymmetry observed in Fig. 1.
To further examine the influence of phase periodicity, we have added a non-periodic phase-error evaluation in Appendix E.1 (Table 7). Specifically, we use PUMA-based phase unwrapping to compute phase RMSE on the full test sets of SimpleWave, Helmholtz, and Maxwell. Across all three benchmarks, unwrapped phase error increases substantially beyond the reference frequency. These results further support the observed amplitude–phase asymmetry under a non-periodic phase-error metric.
We have expanded Sec. 3.3 to clarify the Green's-function-inspired construction. Based on the geometric propagation interpretation of the Green's-function representation, Eq. (13) constructs a lightweight multipath surrogate using dominant propagation paths and effective phase coefficients. Its phase provides source- and geometry-aware oscillatory cues for the generative enhancer, complementing the structural information supplied by the coarse amplitude anchor. The propagation paths and their weights are specified in advance, while the reference phase coefficient is computed from the target spectral variable and sample-dependent medium properties. The benchmark-specific configurations are provided in Appendix D (Table 6).
We have further evaluated the sensitivity to the number of paths M, path weights am, and reference phase coefficient κref on Maxwell in Appendix E.3 (Table 9). Here, α denotes the scaling factor applied to κref.
Removing the reflected path degrades overall reconstruction performance, particularly at larger frequency gaps. The model is relatively robust to changes in path weights, while the reference phase scale has a more pronounced influence on prediction accuracy. The default parameters serve as a representative configuration, leaving room for further improvement.
To examine the contribution of geometric information, we have added two phase-prior controls on Helmholtz in Sec. 5 (Table 2). Simple Phase Ramp uses frequency-dependent linear phase variation without propagation geometry, while Geometry-Shuffled Prior applies spatial rotations or flips to the original prior to disrupt its geometric alignment. Both controls use the same network architecture and training settings.
The simple phase ramp improves upon removing the phase prior but remains less effective than APEX. The geometry-shuffled prior performs even worse than removing the phase prior. These results indicate that the geometric alignment of the proposed prior contributes to higher-frequency reconstruction beyond providing a generic phase-like conditioning signal.