acceptodds
Under review as a conference paper at ICLR 2027

Environment-Conditioned Molecular Spectral Prediction: A Controlled Study of Data, Representation, and Architecture

Abstract

Molecular absorption cross sections govern atmospheric retrieval and biosignature detection, but experimental coverage extends to only a few hundred species, motivating learned emulators. Unlike the single-condition spectra targeted by prior ML spectroscopy work, atmospheric cross sections are environment-conditioned: the same molecule absorbs differently across temperature and pressure. The available labels also carry source-dependent floors. Experimental spectra have an instrumental detection limit near cm/molecule, whereas simulated spectra extend down to . We formulate this task as learning a molecule-conditioned continuous function over wavenumber and evaluate it on 570 experimental HITRAN species under 4-fold molecule-wise cross-validation, comparing 29 configurations across 6 design axes with record-level paired significance testing on a fixed set of 1493 held-out spectra. Synthetic data augmentation is the biggest contributor to test performance on real experimental data: synthetic-only training does not transfer to measured spectra (median ), yet 50% synthetic augmentation in training lifts the median R from 0.46 to 0.60 over experimental training alone. Masking sub-threshold simulated points from the loss beats clipping them at the limit, which is indistinguishable from no treatment. Given these choices, simple encodings win or tie with expressive ones, and equivariant backbones give no advantage over a plain invariant GNN at a matched 5M-parameter budget.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
machine learning for science, sim-to-real transfer, graph neural networks, equivariant neural networks, empirical study, molecular spectroscopy

Reviews

Among:
Shape:
1234this paper, Top 30%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_85pgOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper investigates the prediction of absorption cross-sections, a property determined by molecular structure, temperature, and pressure. The authors also provide a systematic comparison of simulated data augmentation, label processing, representation methods, and network architectures. The results indicate that an appropriate amount of simulated data and the use of label masking can improve the prediction of experimental spectra, while more complex architectures do not demonstrate a consistent advantage.

Critical strengths

The task is of practical significance. The use of molecule-based cross-validation, combined with the exclusion of molecules that appear in both the simulated and experimental datasets, helps to mitigate data leakage. The experiments cover a range of design factors and report both effect sizes and negative results, providing a useful benchmark for future research.

Critical weaknesses
  1. The most distinctive aspect of the task, that is, whether the model has learned how temperature and pressure alter the spectra, has not yet been fully verified. If the overall error is primarily driven by the inherent differences in spectral shapes between distinct molecules, a model could potentially achieve a decent aggregate performance even if it only predicts typical spectra (e.g., near room temperature) and remains insensitive to variations in temperature and pressure.
  2. The benefits of synthetic data augmentation may be coupled with the training budget. Since the number of training epochs is held constant across configurations, adding synthetic data significantly increases the total training data; the authors should control the training budget to isolate the effects of increased computational resources.
Questions for authors

Please refer to the weakness part above.

3 comments

Thank you for your constructive comments, for both questions, please refer to Official Comment by Authors.

I thank the authors for providing additional results. I also appreciate the practice of acknowledging the issues in their previous version. As my concerns are mostly addressed, I keep my original score of weak acceptance.

Thank you for your constructive reviews.

Reviewer_tZ16OpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2(+1)
Read review
Paper summary

This paper studies environment-conditioned prediction of molecular absorption cross sections, motivated by atmospheric retrieval and biosignature detection, which require spectra for many molecules over a wide range of temperatures and pressures. The task is formulated as molecule-conditioned continuous regression: a molecular graph encoder produces an embedding, and a shared MLP decoder is queried at (wavenumber, temperature, pressure) to predict log₁₀σ. Using 570 molecules (1493 records) of experimental HITRAN cross sections as the evaluation set, and line-by-line simulated spectra of 53 small molecules as auxiliary training data, the authors run a one-axis-at-a-time controlled study of 29 configurations across six design axes: data source, treatment of the simulated label floor, wavenumber encoding, temperature/pressure encoding, loss and weighting, and backbone (six graph encoders, including invariant, equivariant, and attention-based models, matched at about 5M parameters). Evaluation uses 4-fold molecule-wise cross-validation with record-level paired Wilcoxon tests and rank-biserial effect sizes. The main findings are:

  • adding 50% simulated data raises median R² on experimental spectra from 0.46 to 0.60, whereas training on simulated data alone fails (median R² = −71.5);
  • masking simulated points below the experimental detection limit from the loss helps moderately;
  • simple encodings, the ℓ₁ loss, and a plain invariant GNN match or outperform more expressive alternatives.
Critical strengths
  1. A new and relevant task formulation and benchmark. Most existing ML work on molecular spectra predicts a single spectrum per molecule at a fixed, near-ambient condition. This paper instead treats temperature and pressure as explicit inputs and formulates environment-conditioned cross-section prediction as molecule-conditioned continuous regression over wavenumber. It also provides an empirical study of this setting on real experimental HITRAN data, with molecule-wise splits that require generalization to unseen molecules. This is consequential because atmospheric retrieval and biosignature detection need cross sections for many molecules beyond those with measured data, and I am not aware of a prior systematic study of this setting.

  2. A carefully controlled study design. The study varies six design factors (data source, label-floor treatment, wavenumber encoding, temperature/pressure encoding, loss, and backbone) one at a time under otherwise fixed settings, and documents the configuration in force for each axis (Table 6). It removes molecules shared between the simulated and experimental sets before fold assignment to avoid leakage, matches all backbones at about 5M parameters, and uses record-level paired tests with effect sizes rather than relying on p-values alone. This matters because it makes the individual comparisons interpretable and gives future work a fixed protocol and fold assignment to compare against.

Critical weaknesses
  1. The evaluation data are concentrated near ambient conditions, so the generality of the conclusions for the motivating scenarios is unclear. The paper is motivated by atmospheric retrieval and biosignature detection, where spectra are needed across a much wider range of temperatures and pressures. However, most of the experimental (evaluation) records are near ambient conditions: according to Table 1 and Section 5.4, about 90% of the records lie between 278 and 323 K, and all are within 0–1 atm. The study therefore mainly measures generalization to unseen molecules near ambient conditions rather than generalization across environmental conditions. It remains unclear how well the conclusions transfer to the scenarios the authors describe.

  2. The simulated data are only coarsely described, and the source of the augmentation gain is not identified. The paper gives the general procedure (line-by-line computation from HITRAN parameters with Voigt profiles for 53 small molecules), but several details that affect the sim-to-real gap and reproducibility are missing: the computation tool, the broadening gas, the line-wing truncation, and whether the spectra are convolved with an instrument line shape. Moreover, the simulated data cover a much broader and denser temperature/pressure range (up to 100 bar) and contain an order of magnitude more records than the experimental training folds. The current experiments cannot tell whether the performance gain comes from the larger data volume or from the physical information encoded in the simulated spectra.

  3. The contribution and take-away for the community are unclear, and the model comparison is limited in scale. It is not clear what the main conclusion of the paper is for the community beyond the specific configuration chosen. In the backbone comparison, controlling all models at about 5M parameters is reasonable for fairness, but this is a relatively small scale in modern AI research. It remains unclear whether the conclusions (e.g., that equivariant and attention-based backbones give no advantage over a plain GNN) would change when the models are scaled up.

Questions for authors
  1. Can the authors evaluate how well the model captures the temperature/pressure dependence itself? For example, for test molecules with records at several temperatures, does the predicted change in the spectrum match the measured change? Results stratified by temperature (e.g., outside 278–323 K) would also help show how the conclusions transfer to the motivating scenarios.
  2. Please provide the missing details of the simulated data: the computation tool, the broadening gas, the line-wing truncation distance, and whether the spectra are convolved with an instrument line shape. How was the 50% subset distributed over the temperature/pressure grid?
  3. To separate data volume from physical information in the augmentation gain, could the authors report (a) augmentation restricted to simulated records near the experimental conditions (e.g., 278–323 K, about 1 atm), and (b) augmentation with simulated spectra whose molecular graphs are shuffled across species?
  4. Do the backbone conclusions hold at larger scales (e.g., 20M–50M parameters) and with per-backbone hyperparameter tuning? Since all backbones share one hyperparameter setting, could the ordering reflect optimization rather than architecture?
  5. What do the authors see as the main, generalizable take-away of this study for practitioners building spectral emulators beyond this specific configuration?
3 comments

Can the authors evaluate how well the model captures the temperature/pressure dependence itself? For example, for test molecules with records at several temperatures, does the predicted change in the spectrum match the measured change? Results stratified by temperature (e.g., outside 278–323 K) would also help show how the conclusions transfer to the motivating scenarios.

Please refer to Official Comment by Authors

Please provide the missing details of the simulated data: the computation tool, the broadening gas, the line-wing truncation distance, and whether the spectra are convolved with an instrument line shape. How was the 50% subset distributed over the temperature/pressure grid?

SettingValue
ToolHAPI, the HITRAN Application Programming Interface, function absorptionCoefficient_Voigt
Unitscm^2/molecule
Spectral range and step300 to 10,000 cm-1 at 0.02 cm-1
Line-wing truncation25 cm-1 absolute distance from each line centre
Broadening gasair only, with the air fraction set to 1.0; no self-broadening component
Instrument line shapenone; no convolution is applied, so the spectra are monochromatic at the 0.02 cm-1 grid step
Temperature grid9 values from 100 to 800 K
Pressure gridthe 22 petitRADTRANS values from 1e-5 to 100 bar, converted to atm by dividing by 1.01325

We will add the detail to Appendix.

On how the 50% subset is distributed over the grid: subsets are sampled at the level of records, that is individual (molecule, isotopologue, T, P) spectra, uniformly at random under a fixed seed, and are nested so that the 25% set is contained in the 50% set. Every molecule and isotopologue is therefore retained, and roughly half of the conditions of each are kept. We will report the realized histogram over the grid in the Appendix.

Q3 and Q4

The experiments are queued and we will report the results as soon as the allocation arrives in time. We would not be able to tune hyperparameters per backbone within the rebuttal period, so we will keep the claim narrow, as the submission already stated.

To separate data volume from physical information in the augmentation gain, could the authors report (a) augmentation restricted to simulated records near the experimental conditions (e.g., 278–323 K, about 1 atm), and (b) augmentation with simulated spectra whose molecular graphs are shuffled across species?

We ran both controls the reviewer proposed. Taken together, we can conclude that, the gain comes from the breadth of thermodynamic conditions the simulated spectra cover, and only marginally from the correct correspondence between molecular structure and spectrum. All runs below use the operating configuration and are tested on the same 1493 held-out experimental records.

Control (a): We rebuilt the simulated pool using only records within the core experimental window, T in [277, 324] K and P in [0.8, 1.2] atm, and repeated the 50% augmentation.

ConfigurationMed. R2rMean MAEr
Full-range simulated (operating config.)0.6541-0.4945-
Near-matched T/P, batch 64, 150 ep.0.45990.863 (large)0.61200.888 (large)
Near-matched T/P, batch 16, 150 ep.0.59700.581 (large)0.52210.587 (large)

The near-matched pool is much smaller, so at batch 64 it also receives far fewer optimizer steps. We therefore repeated it at batch 16, which restores the step count to approximately that of the full-range run. This recovers a large part of the loss (the two near-matched runs differ at |r| = 0.880), but the full-range run still wins by a large effect on both metrics. Restricting the simulated data to the conditions the test set actually occupies makes it substantially less useful, even at matched optimizer budget.

Control (b): We permuted graphs across the simulated species under a fixed seed, so that no isotopologue retains the graph of its own molecule. This holds volume, grid density, thermodynamic coverage and label domain exactly fixed and destroys only the structure-to-spectrum correspondence.

ConfigurationMed. R2rMean MAEr
Full-range simulated (operating config.)0.6541-0.4945-
Graphs shuffled across species0.63670.265 (small)0.50820.281 (small)

Shuffling costs only a small effect. Most of the benefit of simulated augmentation survives the destruction of the correspondence between a molecule and its own spectrum.

The two controls sharpen the interpretation we offered in sec 5.1. The simulated data is not transferring species-specific chemistry. What transfers is a prior over the functional form of a cross section: how log σ\sigma varies with wavenumber and, in particular, how it responds to temperature and pressure, and that prior is learned from the spread of thermodynamic conditions.

We will add both controls to sec 5.1 and state the conclusion in the revision.

Do the backbone conclusions hold at larger scales (e.g., 20M–50M parameters) and with per-backbone hyperparameter tuning? Since all backbones share one hyperparameter setting, could the ordering reflect optimization rather than architecture?

We re-ran all 6 backbones at a matched 20M-parameter budget (realized counts 19.89M–20.14M, within 1% of target), under the same operating configuration as the 5M comparison, and the conclusion is unchanged.

Paired over the same 1493 records, within each architecture:

BackboneMed. R2, 5MMed. R2, 20MMedian Δ\DeltarVerdict
GNN0.65410.64400.00900.2335M wins (small)
MGNN0.63680.61960.01630.3145M wins (medium)
GraphTransformer0.60840.59230.01620.2825M wins (small)
GotenNet0.64460.64500.00040.026no difference (p = 1.00)
SEGNN0.64950.63580.00610.1945M wins (small)
EquiformerV20.59960.59810.00100.031no difference (p = 1.00)

4 backbones are slightly worse at 20M, 2 are statistically unchanged, and none improves. The best single configuration across all 12 runs remains the 5M GNN (median R2 0.6541).

At 20M, GNN, GotenNet and SEGNN remain statistically at the top; MGNN sits behind by a medium effect (|r| = 0.329); GraphTransformer and EquiformerV2 are last by large effects (|r| = 0.599 and 0.513 against the GNN). Equivariance still fails to order the axis: SEGNN ties the invariant GNN (|r| = 0.037, Holm p = 0.21) while EquiformerV2 loses by a large effect, exactly the same as we reported at 5M.

However, at 20M, GotenNet edges the GNN by a small effect (median 0.6450 vs 0.6440, |r| = 0.159), where the two were indistinguishable at 5M. GotenNet's instability resolves with capacity, its mean R2 rises from 0.1876 at 5M to 0.5309 at 20M, because the catastrophic fold-0 result that dominated the 5M mean (fold-0 mean R2 = −0.845) disappears. So additional capacity bought GotenNet robustness rather than accuracy.

We didn't hypertuning per backbone, therefore we keep our narrow claim. We will add the 20M comparison to sec 5.6 in the revision.

What do the authors see as the main, generalizable take-away of this study for practitioners building spectral emulators beyond this specific configuration?

We thank the reviewer for pushing on this, the extra experiments ended up changing how we read our own results, and we think the combination is more interesting.

No backbone surpass a plain invariant GNN, and we didn't have a good explanation for this in the submission. However, the shuffled-graph control (Q3) offers some insights. When we permute the molecular graphs across simulated species, destroying the correspondence between a molecule and its own spectrum, performance drops by only a small effect (|r| = 0.265). If the graph itself is contributing that little, it is not surprising that making the graph encoder more expressive contributes nothing either. The bottleneck is not how we read the structure.

Our simulated spectra are unusable on their own, however, used as augmentation, they are the largest effect in the paper (|r| = 0.532 against a fully converged, fully matched baseline). Meanwhile, the near-matched-T/P control costs a large effect (|r| = 0.581) even at matched optimizer steps. So the value is in the breadth of conditions.

For practitioners building spectral emulators beyond this specific configuration, we would like to suggest spending more effort on the labels, as every data-side axis moved the metric; and use cheap simulators for coverage as breath as we can afford. Breadth beats fidelity here.

We believe those points generalise past spectroscopy to any scientific ML setting where labels are instrument-limited and partly synthetic.

Reviewer_gfbPOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper predicts absorption cross-sections using a molecular graph encoder and a continuous decoder, based on molecular structure, wavenumber, temperature, pressure, and isotopologues. Experiments employ molecular-level four-fold cross-validation, comparing 29 configurations across six aspects. After adding half of the records from the simulation library, the median R² increased from 0.4634 to 0.5967, and the MAE decreased from 0.6164 to 0.5303. Masking simulated values below the detection limit also improves performance. The performance of simple encoding and invariant GNN is comparable to or better than the complex schemes compared.

Critical strengths
  1. Overlapping species were excluded before cross-validation splitting. The authors first removed 13 isotopologues from 8 overlapping molecules to prevent test species from appearing in the training set in the form of simulated data.
  2. The experiment examined multiple choices in practical modelling. The experiment investigated data, label processing, representation, loss, and backbone, and provided the actual number of parameters and the configuration of each axis (Tables 4 and 6).
Critical weaknesses
  1. Even with the same number of training epochs, the number of updates can vary significantly. The “same training budget” referred to in the paper (lines 264–265 on page 5) uses 150 epochs and a batch size of 64 (Table 5 on page 16). However, the experimental and simulated records in Table 1 number 1,493 and 28,314, respectively, with each record sampled from 60,000 data points (page 4); “50% simulated” refers to half of the simulated dataset (lines 206–209 on page 4). **This means that approximately 14,157 simulated records were added to the roughly 1,120 experimental training records in each fold. If all records are traversed in each round and the final batch is retained, the total number of updates would increase from approximately 2,700 to 35,850. Here, the definition of an “epoch” needs clarification: does it refer to a complete traversal of all records, or merely running a fixed number of batches?

  2. Several instances of text and annotations can be corrected directly. A period is missing at the end of “loss gives a medium boost over no treatment” (lines 96–98 on page 2). “six design axis” in Figure 1 should be changed to “six design axes” (page 2), and “experimenatl” in Figure 6 should be changed to “experimental” (page 17) . Table 2 should also indicate R² ↑ and MAE ↓.

  3. There is still a lack of direct comparison to determine exactly how much benefit the temperature and pressure inputs provide. Section 5.4 compares scalar and Fourier encoding (page 8). To examine the effects of these two variables independently, the architecture should remain unchanged while the temperature and pressure inputs are removed. The experimental coverage also warrants review: the experimental temperatures P5–P95 are concentrated between 278.15 and 323.15 K, with a pressure range of 0–1 atm (Table 1, page 4). We recommend reporting errors by temperature and pressure intervals and indicating which test conditions fall outside the training coverage.

  4. Previous work has also investigated spectral prediction under varying environmental conditions. The abstract summarizes prior research as “single-condition spectra” (lines 15–17 on page 1). “A deep learning system to transform cross-section spectra to varying environmental conditions” (Moser et al., 2022) learns pressure-dependent spectral transformations from reference spectra and evaluates their transferability to measured data. The paper should directly compare the input requirements, prediction conditions, and usage of simulated and measured spectra between the two studies to clarify the novel contributions of the molecular graph method presented here.

5.The explanation of the lower bound of the label should be grounded in the transformed target. Training uses log10(σ+10⁻³⁰) (lines 202–204 on page 4); thus, the cross-section range from zero to 10⁻³⁰ accounts for only approximately 0.301 logarithmic units. To explain the improvements shown in Table 3, you need to clarify how points below the threshold contribute to the loss at this scale. Please provide the target values for “no treatment,” “clip,” and “mask” separately, specify the order of operations (clipping, adding ε, and taking the logarithm), and clearly state the denominator used when calculating the average loss.

Questions for authors

Key Questions

  1. If the number of training iterations for the “Experimental only” group is increased by 50%, what percentage of the gains shown in Table 2 remain? What are the results if the total number of updates and the learning rate schedule are matched to those of the hybrid group?
  2. Compared to a model with the same architecture but without temperature and pressure inputs, how much improvement do these inputs provide? Are there any test conditions that fall outside the scope of the training data?

Secondary Questions

  1. After the log10(σ+10^-30) transformation, what target values are used for “no treatment,” “clip,” and “mask,” respectively? What denominators are used when calculating the average loss for each?
7 comments

Key Questions

Please refer to Official Comment by Authors

After the log10(σ+10^-30) transformation, what target values are used for “no treatment,” “clip,” and “mask,” respectively? What denominators are used when calculating the average loss for each?

The order of operations is clip, then add epsilon, then take the logarithm. The clip touches simulated samples only; experimental data is never modified. The three configurations differ as follows, where sigma is the raw cross section in cm2 per molecule and the noise floor epsilon is 1e-30.

ConfigurationFlagSigma for a sub-floor simulated pointResulting targetEnters the loss?
No treatmentclip disabledunchanged, down to about 1e-255log10(sigma + 1e-30), which equals -30.000 to float precision whenever sigma is far below epsilonyes, weight greater than 0
Clip to floorclip 1e-30, mode floorset to 1e-30log10(2e-30) = -29.699yes, weight greater than 0
Mask from lossclip 1e-30, mode zeroset to 0 and the point is marked unmeasuredexcludedno, weight equals 0

The denominator is a count of valid points in the batch, and a masked point leaves both the numerator and the denominator.

Several instances of text and annotations can be corrected directly

We thank the reviewer for catching and will fix all of them

Previous work has also investigated spectral prediction under varying environmental conditions

We thank the reviewer for pointing us to Moser et al. (2022), which we had missed and which we will add to the related work.

However, the two methods take different inputs and therefore address different problems. Moser et al. learn a transformation of an existing measured cross section of a given molecule to a different pressure, so the method requires that a reference spectrum of that molecule already exists. Our model takes only the molecular graph, the wavenumber and the thermodynamic state, and never sees a spectrum of the test molecule at any condition, which is what the molecule-wise cross-validation enforces. The distinction matters for the motivating application: in exoplanet atmospheres, a large fraction of candidate biosignature molecules have never been measured in a laboratory and in some cases cannot be synthesized in quantity, so no reference spectrum exists to transform.

Thank you for the response and additional experiments, which address some of my concerns. However, the revised table considerably narrows the gap between experimental-only and mixed-data training. The current results do not support the claim that adding simulated data provides a substantial benefit.

I suggest training all four configurations—Exp, 25% sim + Exp, 50% sim + Exp, and 100% sim + Exp—to convergence and plotting R² and MAE against training steps. These curves should show both performance at equal step counts and the final converged results. My main question is whether mixed-data training clearly outperforms experimental-only training once both have converged. Even if mixed-data training requires more steps, a clear improvement in final performance would still demonstrate the value of adding simulated data. The current comparison does not answer this question, so I maintain my current score.

We thank the reviewer for the follow-up.

All 4 configurations were already trained to convergence. Every configuration was trained for 150 epochs, and the numbers in our revised table are final converged results.

We will attach the training curves for all 16 runs (4 data configurations × 4 folds). Validation R2 and test loss plateau at the following epochs:

ConfigurationBatch sizePlateau epoch, by foldEpochs trained
Experimental only1650 / 40 / 80 / 60150
25% sim + Exp6480 / 40 / 60 / 80150
50% sim + Exp6440 / 80 / 80 / 60150
100% sim + Exp6440 / 40 / 80 / 80150

The latest plateau in any fold of any configuration is epoch 80, so every run was carried at least 1.9× past its own convergence point.

In fold 0 of the 50% configuration, test R2 peaks near 0.458 at epoch 40–50 and then declines to 0.394 by epoch 150. We report the final epoch for every configuration regardless, because choosing the best epoch per fold would mean selecting on the test set, which understates the 50% configuration. The remaining 15 runs are flat from their plateau to epoch 150.

Measured at convergence against the compute-matched experimental-only baseline, over 1493 paired held-out records:

ConfigurationMed. R2rMean MAEr
Experimental only (batch 16)0.6043–0.5278–
25% sim + Exp0.61580.064 (negligible)0.53240.044 (negligible)
50% sim + Exp0.62760.433 (medium)0.51770.423 (medium)
100% sim + Exp0.65140.549 (large)0.50320.560 (large)

So our answer is yes for 50% and 100% simulated data and no for 25%. We agree that "Substantial" overstates a median improvement of 0.045 in R2, but the converged comparison supports a consistent improvement: modest in magnitude, growing monotonically with the amount of simulated data, and reliable enough across records to register as a large rank-based effect at 100%. We will change the phrase in the revision accordingly.

Comments on the paper

3 comments

To all reviewers: corrected simulated data and full re-run

We thank all three reviewers for their careful reading. Before answering individual points, we must report an error we found ourselves while preparing this response. In generating the simulated spectra we converted the petitRADTRANS pressure grid from bar to atm by multiplying by 1.01325 rather than dividing. Every simulated spectrum was therefore computed at a pressure about 2.7% higher than intended. We have corrected the conversion, regenerated the entire simulated dataset, and re-run all 29 configurations across all six design axes.

The table below replaces Table 2 in the submission.

Config.Med. R2Med. Δ\DeltarMean MAEMed. Δ\Deltar
Experimental only0.4567––0.6201––
25% sim + Exp0.6158-0.1074-0.8000.53240.07910.824
50% sim + Exp0.6276-0.1358-0.8140.51770.09770.859
100% sim + Exp0.6514-0.1547-0.8610.50320.11020.878
Simulated only-25.857326.23111.0005.2827-4.1922-1.000

Three changes are worth flagging explicitly.

First, the augmentation benefit no longer saturates. In the submission the 25%, 50% and 100% configurations were statistically close, and we argued that the benefit saturated once all 53 simulated species were present. On corrected data the three separate from one another: 25% versus 50% gives r = 0.420, 50% versus 100% gives r = 0.391, and 25% versus 100% gives r = 0.597. The gain is monotone in volume and 100% is best on both metrics. We have removed the saturation argument from Section 5.1 and, while we retain 50% as the operating configuration throughout the rest of the paper for compute reasons, now report 100% as the best configuration.

Second, the over-resolved wavenumber encoding is no longer unstable. In the submission it was the least stable configuration in the sweep, with a mean R2 of -73.1. On corrected data it is statistically indistinguishable from the baseline encoding, at a Holm-adjusted p of 0.97 on R2. We have deleted that example and the claim built on it.

Third, L1 with magnitude weighting now beats L1 with uniform weighting by a small effect on both metrics (r = 0.141 on R2, r = 0.210 on MAE), where uniform weighting won in the submission. The operating configuration has changed accordingly, and the backbone comparison was re-run under it.

The conclusions that survive unchanged are the two the paper leads with. Training on simulated data alone fails on measured spectra, while the same data used as augmentation is the largest effect anywhere in the study. Masking simulated points below the detection limit beats imputing them at the limit, which remains indistinguishable from no treatment at all. The backbone result also survives and is now cleaner: the plain invariant GNN has the highest median R2 on its axis outright.

To all reviewers: the training budget was matched in epochs only

We thank reviewers gfbP and 85pg for catching it. Our claim that configurations share a training budget held only in epochs.

In our training script the loader is constructed as a standard PyTorch Geometric DataLoader over the fold's training set with shuffle enabled, and the inner loop iterates it to exhaustion, an epoch is therefore one complete pass over all records. The batch size counts records, that is molecular graphs, and each record carries 60,000 sampled wavenumber points, so one optimizer step sees batch_size times 60,000 supervised points. The learning-rate schedule is indexed by epoch, with MultiStepLR milestones at epochs/5, epochs/2 and epochs/1.1, which for 150 epochs is epochs 30, 75 and 136.

We now have run the control, that holding the experimental-only configuration fixed and reducing the batch size from 64 to 16, an epoch becomes about 70 steps and 150 epochs about 10,500 steps, roughly 3.9 times the original budget and the same data. The training curve is flat after about 40 epochs, so further updates do not change the result; we will include the curve in the revision. Median R2 for experimental-only training rises from 0.4567 to 0.6043.

The augmentation effect therefore shrinks substantially but does not disappear. Against the 50% augmented configuration we carry forward, at median R2 0.6276, the remaining gap is about 0.023 in median R2; against the best configuration, 100% at 0.6514, it is about 0.047. The paired tests against that baseline are in the table below, and we will present this comparison as the headline in the revision.

Config.Med. R2Med. Δ\DeltarMean MAEMed. Δ\Deltar
Experimental only, batch 16 (compute-matched baseline)0.6043––0.5278––
25% sim + Exp0.6158-0.0023-0.0640.53240.00200.044
50% sim + Exp0.6276-0.0229-0.4330.51770.01600.423
100% sim + Exp0.6514-0.0446-0.5490.50320.03090.560

The magnitude of the augmentation gain was overstated in the submission, and a substantial part of what Table 2 attributed to simulated data was attributable to optimizer steps. The corrected comparison shows a smaller but still substantial gain, and we will revise the abstract and the contribution list to the compute-matched numbers.

To all reviewers: does the model learn temperature and pressure?

All three reviewers asked for the ablation that removes the thermodynamic inputs entirely. We have run it. The configuration is the operating one (50% simulated, mask, Fourier dim 64 encoding, single head, L1 with magnitude weighting, GNN), with the temperature and pressure inputs removed from the decoder and everything else held fixed.

Removing the two inputs costs 0.0906 in mean R2, from 0.5347 to 0.4441, with a 95% confidence interval of [0.0699, 0.1102] and 85% of the 1493 held-out records getting worse. The model is therefore using the conditioning rather than predicting one typical spectrum per molecule.

Temperature binRecordsMoleculesMean R2, fullMean R2, no T and PMean gain [95% CI]Records improvedHolm p
All14935700.53470.44410.0906 [0.0699, 0.1102]85%1.1e-132
T < 278 K5980.23210.16890.0632 [-0.1880, 0.2708]53%0.19
278 K to 323 K9155500.52040.43030.0900 [0.0692, 0.1102]85%3.1e-83
T > 323 K5194780.59420.49960.0946 [0.0744, 0.1200]89%5.5e-62
Both tails combined5784810.55720.46580.0914 [0.0620, 0.1234]86%2.3e-51

The sub-278 K bin is underpowered and we do not claim it: 59 records drawn from only 8 molecules, a confidence interval of [-0.1880, 0.2708] that spans zero, and p = 0.19.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.