acceptodds
Under review as a conference paper at ICLR 2027

Where Should Physics Enter a Molecular Crystal Generator?

Abstract

Generative models make molecular crystal structure prediction fast, but their samples still exhibit geometric and packing violations. Physics can be introduced during training, post-training, or inference, yet these choices are rarely compared with the generator and physical signal held fixed. We introduce CrystAF, an all-atom crystal flow-map generation model, and use it with the UMA interatomic potential to systematically study where physics should enter. Post-training learns physical preferences directly into CrystAF, improving molecular validity and crystal packing while leaving sampling unchanged: physics is paid for once during training rather than repeatedly at deployment. In contrast, UMA relaxation is effective at repairing local clashes but makes generation 6–26 slower, while learning from relaxed targets provides little benefit. These routes are complementary rather than competing. Physics-informed post-training first shifts the generated distribution toward more physically reasonable structures, after which inexpensive inference-time corrections further remove clashes and restore stereochemistry that the generator cannot represent. Importantly, the same post-training strategy also improves the multi-step all-atom Clari-M and rigid-body MolCrystalFlow generators, demonstrating transfer across architectures and representations. Together, our results suggest a simple principle: learn reusable physical alignment into the generator, and reserve inference-time physics for residual constraints that are better corrected than learned.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
MeanFlow, Drug, Generation Models, Reinforcement Learning, AI for Science

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

This paper presents an empirical study of where physics should be incorporated into molecular crystal generators. The authors introduce CrystAF, a few-step all-atom flow-map generator distilled from Clari-M, and use UMA-based physical feedback with negative-aware fine-tuning for post-training alignment. The paper systematically compares three approaches to incorporating physics: training-time learning, post-training alignment, and inference-time correction. It further investigates the contributions of different physical signals through ablation studies, and evaluates the methods in terms of structural validity, crystal packing quality, crystal structure recovery, and computational cost. The results suggest that post-training provides a favorable trade-off between structural quality and inference cost, while inference-time corrections are particularly effective at repairing local geometric defects and enforcing stereochemical constraints.

Critical strengths
  1. Comprehensive empirical comparisons. The paper provides a useful framework for systematically investigating where physics should enter a molecular crystal generator. The experimental comparisons are comprehensive and insightful. In particular, Table 1 provides a broad comparison of physical quality and computational cost across different methods, while Table 3 thoughtfully evaluates whether improvements in structural quality translate into better crystal structure recovery. The inclusion of computational cost is especially valuable for practical applications.

  2. Distinguishing physical improvement from metric optimization. The authors explicitly recognize that improving an evaluation metric does not necessarily imply improving physical plausibility. This distinction is important and provides useful insights for future model design and evaluation. The ablation studies also offer interesting observations about the different contributions of physical signals and update algorithms.

  3. Interesting empirical findings. The paper reports several informative findings, including the effectiveness of simple feasibility filtering, the complementary roles of post-training and inference-time corrections, and the limitations of post-training in recovering stereochemical constraints. The authors also report cases where improvements in structural validity do not consistently translate into better crystal structure recovery.

Overall, this is an interesting exploratory and empirical work.

Critical weaknesses
  1. Presentation and terminology could be improved. Some terms, such as "gentle," "strong," "matched," and "released" in Table 1, are not clearly introduced. The table also mixes model architectures, training configurations, and inference-time corrections, making the comparisons difficult to follow. A summary table or diagram clarifying these relationships would help.

  2. Limited mechanistic understanding. The paper primarily demonstrates where physics should enter, but provides less insight into what physical properties are learned and how they evolve during generation. For example, Table 2 shows similar performance across different physical signals, but the underlying reasons remain unclear. Analyzing the evolution of energy, forces, stress, and atomic geometry during generation could provide more mechanistic insights. While such analysis is not essential to the paper's primary objective, it would strengthen the findings.

  3. Unclear distinction between physical improvement and metric optimization. The term "physics" encompasses physical energetics, geometric validity, and agreement with experimental structures, which are not necessarily equivalent. Since negative-aware fine-tuning is itself a form of reward optimization, it remains unclear whether the model learns generalizable physical properties or merely optimizes physical proxy metrics. Table 2 suggests that feasibility filtering and volume supervision explain much of the improvement, while UMA diagnostics show increased energy, forces, and stress after post-training. Moreover, Table 3 uses UMA for candidate ranking, introducing some overlap between training and evaluation. Independent physical evaluations or out-of-distribution experiments would help substantiate the claims.

  4. Limited improvement in downstream crystal structure recovery. Table 3 is valuable but shows that post-training does not consistently improve recovery performance. Further analysis of why improved structural validity does not necessarily translate into better recovery would strengthen the paper's practical implications.

  5. Incomplete related work and insufficient positioning of novelty. Several relevant studies are missing from the discussion, including Physics vs Distributions (ICLR 2026), Physics-Constrained Fine-Tuning of Flow-Matching Models (ICLR 2026), Physics-Informed Distillation of Diffusion Models (ICML 2026), and Physics-Informed Diffusion Models (ICLR 2025). More closely related to molecular and crystal generation are Chemistry-Inspired Diffusion with Non-Differentiable Guidance (ICLR 2025), Reinforcement Learning with Formation Energy Feedback for Material Diffusion Models (2026), and Siamese Foundation Models for Crystal Structure Prediction (2026). More discussion and comparisons are needed.

Overall, this paper can have good potential impact, while the demonstrated impact is not enough, which can be improved by adding the above suggested analysis and make everything (i.e., the author's claims, supporting evidence, analysis) clear.

I am open to increasing my score if the authors adequately address the concerns raised above.

Questions for authors

See weakness.

6 comments
AuthorsOpenReview ↗

W1: clarifying terminology and restructuring Table 1

We sincerely thank the reviewer for such a thorough reading and for providing a clear, actionable list of suggestions. We have organized our response into five posts corresponding directly to W1 through W5. All new experiments reported below follow a strict evaluation protocol that was fixed before any results were observed.

You rightly pointed out that shorthand terms like "gentle", "strong", "matched", and "released" were opaque, and that Table 1 mixed model architectures, training configurations, and inference-time corrections in a way that made comparisons difficult to follow. We have completely removed these ambiguous labels from Table 1, Figure 3, and the main text. Every row now explicitly states what it is, the Table 1 caption provides the exact guidance hyperparameters, and the protocol paragraph at the beginning of Section 4 defines how the two CrystAF-UMA checkpoints were trained.

Old LabelNew LabelExact Definition and Role in the Paper
gentle guidanceUMA guidance, η = 0.01Applied to the last 16 of 32 jumps (r₀ = 0.5) with a per-atom displacement cap δ = 0.05 Å.
strong guidanceUMA guidance, η = 0.05Applied to the last 16 of 32 jumps (r₀ = 0.5) with a per-atom displacement cap δ = 0.2 Å.
matchedCrystAF-UMA, 4 ep.Post-trained directly from CrystAF-base and read out at epoch 4, sharing the exact recipe of every ablation arm.
releasedCrystAF-UMA, 6 ep.public weights; 6 epochs from CrystAF-base

To resolve the structural confusion in Table 1, we reorganized the rows based on what actually changes in the pipeline. The first group contains interventions that modify the model weights, covering training-time distillation and post-training alignment. The second group contains interventions that alter only the sampling process via inference-time corrections, separated into distinct blocks according to the underlying weights they are applied to (CrystAF-base versus CrystAF-UMA). Finally, we added a dedicated route summary table in Appendix Table S4, referenced at the start of Section 4, which explicitly maps out each route by whether weights are changed, what physical input is required, whether experimental labels are used, what happens at inference time, and when the computational cost is paid.

AuthorsOpenReview ↗

W2: mechanistic understanding of physical signals and training evolution

To address why different physical signals in Table 2 perform similarly and what physical properties are actually learned, we conducted two new mechanistic analyses examining within-family signal correlations and epoch-by-epoch training trajectories.

First, we rebuilt the exact training advantage using the UMA single-point scores of generated samples and correlated it within each molecular family against our evaluation metrics across 195 families on CrystAF-base samples (detailed in Appendix A.35 and Section 4.2).

Reward Signalρ(A, −vol. error)ρ(A, −PDD)Partial ρ(A, −PDD) given volumeρ(A, denser cell)
E, F, σ−0.04 [−0.08, −0.00]−0.01 [−0.05, +0.02]+0.05 [+0.01, +0.09]−0.10 [−0.13, −0.06]
E only+0.01 [−0.03, +0.05]+0.08 [+0.04, +0.12]+0.15 [+0.11, +0.19]−0.04 [−0.07, +0.00]

On CrystAF-base samples, the UMA reward is uncorrelated with cell-volume error (Spearman ρ = −0.04). However, within any given family, cell-volume error and PDD are tightly coupled (ρ = +0.85), and a pure 1% volume error alone costs 1.6 PDD units on an otherwise exact experimental crystal. Even after controlling for volume error, the energy ranking still carries a consistent packing signal, with a partial correlation of +0.15 for the energy-only reward and +0.05 for the combined E, F, σ reward.

This strong coupling explains why the different arms in Table 2 look so similar on PDD. When volume effects are mathematically removed by isotropically rescaling each generated cell to the experimental volume while keeping molecules rigid (Appendix A.34), most of the post-training PDD gain disappears: the full-vs-base gain drops from −0.25 on raw PDD to −0.10 [−0.14, −0.05] on volume-normalized PDD. Moreover, the label-free E, F, σ reward and the experimental-volume label arm become statistically equivalent, differing by just −0.03 [−0.07, +0.02] (well within our pre-specified ±0.15 margin).

Thus, the primary mechanism behind the packing improvement is macroscopic cell-volume correction. CrystAF-base systematically generates cells +3.0% too large on average; the UMA-only arm shrinks this over-expansion to +1.2%, matching the +1.4% of direct experimental volume supervision across three seeds. Within a single family, the potential's ranking slightly favors larger cells (ρ = −0.10), so we report this global contraction as a robust empirical observation rather than claiming a simple within-group ranking mechanism (Discussion).

Because most crystal UMA energy is intramolecular, we also tested whether isolating intermolecular interactions via lattice energy (crystal minus isolated molecules) gives a sharper packing signal across 45 families (Table S22).

Sample SourceE_int (Lattice)E (Total)E_int − E
CrystAF-base, 45 families+0.151 [+0.055, +0.245]+0.119+0.031 [−0.071, +0.136]
Eligibility only, epoch 4, 41 fam.+0.197+0.102+0.095 [+0.023, +0.167]
E, F, σ, epoch 4, 44 fam.+0.172+0.161+0.011 [−0.090, +0.110]

While lattice energy tracks volume better than total energy (ρ = +0.11 vs. +0.01 with volume error, +0.16 vs. +0.04 with PDD), its partial correlation with volume-normalized PDD on base samples is +0.151 vs. +0.119 for total energy (difference +0.031 [−0.071, +0.136]). Failing our pre-specified go-rule (≥ 0.20 with CI above total energy), we did not train a lattice-energy policy.

Second, we tracked how metrics evolve across epochs 0–6 for the full signal on 200 families (Appendix A.37, Table S24).

EpochPB (%)Clash (%)Vol.ErrPDDEligibleΔE (eV/mol)Med. F_maxMed. ‖σ‖
0 (base)89.9911.131.9610.340.853+0.008.590.058
190.5010.321.7910.150.846−0.148.620.060
291.5610.911.8210.130.843+0.249.340.068
392.209.991.7610.140.841+0.6110.530.075
492.029.641.6910.020.819+0.9111.070.079
689.4110.601.579.940.717+3.2112.210.128

Most volume and PDD gains occur in epoch 1 (Vol.Err 1.96 to 1.79, PDD 10.34 to 10.15) with UMA energy flat (−0.14 eV/mol), whereas PB peaks at epochs 3–4. Upward drift in single-point energy, force, and stress starts at epoch 2 and accelerates after epoch 4 (+3.21 eV/mol at epoch 6), where the eligible fraction drops to 0.72 and PB degrades even as volume and PDD tighten. This confirms that packing gains are not a by-product of late energy drift and justifies reading out all arms at epoch 4. We omitted generation-trajectory analyses because intermediate flow-map predictions fall outside the 16-step adjacent-jump training distribution.

AuthorsOpenReview ↗

W3: disentangling physical preferences, constraints, and metric optimization

We agree that "physics" was used too loosely in the original draft. In the revision (Section 3.2 and Introduction), we explicitly separate three signals: (i) potential-based preferences, represented by within-family rankings of UMA energy, forces, and stress; (ii) feasibility constraints, consisting of minimum distance, density bounds, and finite-energy checks; and (iii) direct supervision from experimental labels (the optional cell-volume term). Table S3 maps these against our metrics, and the Discussion clarifies that the full reward's volume gain partly reflects direct label supervision, whereas UMA-only arms use zero experimental labels.

Since the feasibility gate (ii) alone reproduces the PoseBusters validity gain, does the potential preference (i) contribute anything on its own? To test this directly, we trained a new E,F,σ arm with the geometric gate completely switched off, ranking every scoreable candidate across three independent training seeds (Appendix A.36, Table S18, Table 2).

Arm (Mean ± SD, 3 Seeds)GateUMAVol.PB ↑Clash ↓Vol.Err ↓PDD ↓Norm. PDD ↓Signed ΔV/V
CrystAF-base89.0210.351.9110.249.19+3.03%
Eligibility only✓91.98 ± 0.4910.31 ± 0.251.75 ± 0.0610.05 ± 0.049.11 ± 0.03+2.42 ± 0.23%
E, F, σ, no eligibility✓91.97 ± 0.369.93 ± 0.521.76 ± 0.0610.07 ± 0.079.09 ± 0.01+2.25 ± 0.09%
E, F, σ + eligibility✓✓90.91 ± 0.4910.06 ± 0.141.58 ± 0.069.94 ± 0.069.04 ± 0.01+1.24 ± 0.30%
Exp.-volume label✓✓91.30 ± 0.339.94 ± 0.361.61 ± 0.029.97 ± 0.019.07 ± 0.02+1.37 ± 0.15%
Full (CrystAF-UMA, 4 ep.)✓✓✓91.41 ± 0.139.65 ± 0.481.64 ± 0.0310.00 ± 0.019.08 ± 0.01+1.93 ± 0.16%

Remarkably, without any gate, UMA ranking alone achieves 91.97 ± 0.36% PB, matching the gate-only arm (91.98 ± 0.49%, seed differences −0.13, +0.15, −0.06) and beating the 89.02% base across all seeds (CIs > +0.5). Thus, the potential carries a genuine validity signal of its own, ranking gate-rejected base samples below accepted ones with 0.92 probability by energy and 0.97 by max force. However, the gate and ranking do not stack linearly. Without the gate, ranking expends its capacity filtering broken geometries, leaving cell volume at 1.76 Vol.Err (+2.25% expansion). When the gate removes broken structures upfront, the same UMA ranking operates among intact candidates, trading ~1 PB point to drive Vol.Err down to 1.58 (+1.24% expansion). Validity comes from discarding broken samples (via gate or ranking), while volume correction comes from ranking samples already cleaned by the gate.

To verify geometric quality using an independent diagnostic outside the reward, we measured MMFF94 heavy-atom intramolecular strain after relaxing hydrogens across 37 scoreable validation families (Appendix A.38, Table S25). Post-training cuts the tail of strongly distorted molecules (> 3 kcal/mol per heavy atom) nearly in half, from 17.2% in CrystAF-base to 9.3–9.7% across all post-trained arms (vs. 8.1% in experimental crystals), while mean strain falls from 2.97 to 1.85 kcal/mol for the full signal (paired difference −1.12 [−2.15, −0.37]). Because the gate-only and volume-label arms achieve this same reduction without UMA ranking, this independent check confirms a real geometric improvement driven by discarding broken samples.

To resolve why single-point UMA energy rises while cell volumes move toward experiment, we ran full-cell UMA relaxations on the 200 experimental validation crystals (Appendix A.39, Section 4.2). Across 177 converged crystals, median volume changes by just +0.12% (92% within ±1%), proving UMA's equilibrium cell sits at the experimental volume. We removed our earlier claim that UMA prefers larger cells (based on 36 clashing generated structures). The generator's +3.03% expansion is a model bias corrected by UMA, while energy rise reflects unconstrained drift under group-relative ranking (Appendix A.32 notes the lack of an independent periodic organic crystal potential).

Finally, Table 3 conclusions do not hinge on UMA ranking overlap. Unranked recovery (n_s = k = 30, Table S17) leaves CrystAF-UMA and CrystAF-base tied on the 779 teaching targets (0.427 vs. 0.423). Re-ranking the top 200 candidates per target from the 400-sample pool by UMA lattice energy instead of single-point energy (Appendix A.40, Table S27) changes collision-enforced Sol@30 by +0.013 [−0.013, +0.039] for base (0.471 vs. 0.458) and −0.005 [−0.031, +0.022] for CrystAF-UMA (0.447 vs. 0.452), keeping comparisons invariant. We also now describe test sets as "held-out molecular identities" rather than OOD (Appendix A.1, Section 4.4).

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

The paper asks where a fixed physical signal should enter a molecular crystal generator. It introduces CrystAF, a few-step all-atom crystal flow map, and compares three routes on the same generator and signal: training-time distillation onto relaxed samples, post-training with a flow-map-aware variant of DiffusionNFT, and inference-time correction (guidance, short relaxation, and a classical correction chain). The paper reports that post-training improves validity and packing at no sampling cost, that relaxation fixes clashes but multiplies per-sample cost, and that training-time distillation helps little. From this it concludes that the routes are complementary and that physical alignment should be learned into the generator, with inference-time physics kept for residual constraints.

Critical strengths
  1. A genuinely controlled comparison with honest cost accounting. The paper holds the generator, physical signal, initialization and evaluation fixed and varies only where physics enters. This kind of experimental template is rare in AI4Science and useful to the community. Quality is reported together with potential calls and compute. The appendix is transparent about negative results, which makes the data valuable.

  2. To my knowledge, this work proposes the first few-step all-atom flow map for organic crystals, with a post-training recipe adapted to it. The adaptation matters: with the same reward, plain DiffusionNFT reaches similar validity but clearly worse packing. This supports the algorithmic contribution.

Critical weaknesses

The gains are weakly attributable to physics. The eligibility gate alone reproduces the full validity gain (92.1 vs. 92.0). For packing, UMA alone and the volume term alone each reach about the same level as their combination (cell-volume error 1.55–1.66 and 1.62 vs. 1.69), so their effects do not appear additive, suggesting UMA acts mainly as a cell-volume signal. The paper explains the rise in UMA energy by UMA's equilibrium cell being larger than experiment, but this means UMA disagrees with experiment on cell size, the very quantity it appears to improve, which makes it unclear what physical information UMA contributes.

Questions for authors
  1. UMA without the volume term and the volume term without UMA give similar packing, and combining them adds nothing, so UMA may act mainly as a cell-volume signal. Could you compare these arms on a packing metric independent of cell volume, such as PDD after rescaling each cell to the experimental volume? If the UMA arms remain better than the volume-only arm, UMA contributes information beyond cell volume; if not, its effect would be mainly through volume.

  2. All matched arms behind the main conclusions use a single seed, and the tie rule (about ±0.5 PB) covers validity only. Could you rerun these arms with at least three seeds, report the variation across seeds, and define tie thresholds for cell-volume error and PDD? Conclusions such as "the potential improves packing" rest on differences of about 1 SE in these metrics.

7 comments
AuthorsOpenReview ↗

Q1: isolating packing gains via volume-normalized PDD

We genuinely thank the reviewer for such a precise reading and for posing these constructive questions. They target exactly the attribution issue our paper left open. We have run extensive new experiments to address both Q1 and Q2.

Before diving into the packing metrics requested in Q1, we need to clarify a crucial detail about the experimental setup that affects how we read these results. The "volume term" represents direct supervision from experimental labels. Specifically, it rewards the model based on the known experimental cell volume of the training family. In contrast, the UMA-only arms never see an experimental volume during training. Because of this, comparing the UMA arm to the volume arm is actually comparing a zero-label physical potential against direct experimental supervision. The fact that UMA can match the volume arm's performance is a highly significant result on its own, rather than a sign of redundancy.

To directly answer Q1 and determine whether UMA acts mainly as a cell-volume signal, we computed the pointwise distance distribution after isotropically rescaling each generated cell to the experimental volume. This transformation cleanly isolates pure packing improvements from macroscopic cell volume corrections.

Vol.ErrPDDvolume-normalized PDD
CrystAF-base1.9110.249.19
gate only1.8110.089.14
E,F,σ (UMA, no labels)1.609.989.05
exp.-volume label (no UMA ranking)1.599.979.07
full1.679.999.09

Your hypothesis was absolutely correct. On this specific diagnostic, the UMA-only reward and the experimental-volume label are statistically equivalent. The primary contrast between the two yields a volume-normalized PDD difference of −0.03, which falls well inside our prespecified equivalence margin of ±0.15. This confirms that the bulk of the PDD improvement from post-training is indeed driven by the overall cell volume correction. The critical takeaway, however, is that UMA achieves this volume correction and matching PDD entirely without relying on experimental labels.

You also raised a very valid concern regarding UMA's equilibrium cell. We realize our previous explanation was somehow flawed because it relied on relaxing 36 generated structures. To fix this, we ran a new check where we relaxed the 200 experimental validation crystals themselves using UMA. We found that their volume barely changes at all, showing a median shift of just +0.12%. This confirms that UMA's equilibrium cell essentially perfectly matches the experimental one. Since the base generator suffers from an inherent +3.0% over-expansion, the UMA potential correctly and powerfully shrinks this artifact down to +1.2%. As an additional check, we tested lattice energy. We found that it tracks cell volume slightly better than total energy, but it provided no statistically significant packing signal beyond volume. We therefore omitted it from full training.

AuthorsOpenReview ↗

Q2: rigorous three-seed evaluation

To definitively answer Q2 and ensure our conclusions rest on solid statistical ground, we completely re-ran all matched arms rather than relying on single-seed variances. During this process, we actually discovered a framework seeding issue. Loading the potential was unintentionally resetting the random number generator streams. We fixed this bug and trained three genuinely new seeds for every arm involved in the attribution question.

Prior to running these new evaluations, we established rigorous tie thresholds based on re-evaluation noise and the size of the base-to-full effects. These thresholds were set at ±0.5 for PoseBusters, ±0.6 for clash rate, and ±0.10 for volume error. We also set ±0.15 for both PDD and volume-normalized PDD.

The consolidated table below merges our full evaluations.

arm (mean ± SD, 3 seeds)PBclashVol.ErrPDDvol.-norm. PDDsigned volume
CrystAF-base89.0210.351.9110.249.19+3.0%
gate only91.98 ± 0.4910.31 ± 0.251.75 ± 0.0610.05 ± 0.049.11 ± 0.03+2.4 ± 0.2%
E,F,σ, no gate91.97 ± 0.369.93 ± 0.511.76 ± 0.0610.07 ± 0.069.09 ± 0.01+2.3 ± 0.1%
E,F,σ, with gate90.91 ± 0.4910.06 ± 0.141.58 ± 0.069.94 ± 0.069.04 ± 0.01+1.2 ± 0.3%
exp.-volume label91.30 ± 0.339.94 ± 0.361.61 ± 0.029.97 ± 0.019.07 ± 0.02+1.4 ± 0.2%
full91.41 ± 0.139.65 ± 0.481.64 ± 0.0310.00 ± 0.019.08 ± 0.01+1.9 ± 0.2%

This rigorous resampling confirms that our original observations hold beautifully across multiple seeds. The UMA-only arm matches the label-supervised arm on cell volume and packing at every single seed. For instance, the volume error differences between the two arms are +0.01, −0.11, and +0.04 across the three respective seeds. Furthermore, the baseline-to-full improvements remain remarkably stable. Across all three seeds, the PoseBusters pass rate consistently improves by roughly 2.4 points. The volume error drops by about 0.28, and the original PDD improves by 0.25. This gives us high confidence that the effects we observe are structural rather than artifacts of a lucky initialization.

AuthorsOpenReview ↗

Weakness: Addressing the attribution weakness via UMA's independent validity signal

In the critical weaknesses section, you correctly noted that the eligibility gate alone reproduces the full validity gain. This intuitively suggests that UMA contributes very little physical validity on its own. We completely agree that the gate alone reaches a 92% pass rate, which is even slightly higher than the full signal's 91.41%. We have updated the text to ensure the validity improvement is not falsely credited to the potential's ranking when it is applied on top of the gate.

However, we discovered something entirely new when we tested the converse scenario. We trained a new reward arm using energy, forces, and stress, but we completely switched off the geometric eligibility gate. This forced UMA to rank every scoreable candidate regardless of its initial feasibility.

Astonishingly, this "no gate" arm reaches a PoseBusters pass rate of 91.97%. This perfectly matches the 91.98% achieved by the gate alone, as shown in the comprehensive table in our previous post. This proves that UMA does indeed carry a powerful and independent validity signal of its own. When we looked closer, we found that it reliably ranks gate-rejected candidates below accepted ones with a 0.92 probability by energy and 0.97 by maximum force. The physical ranking is therefore redundant with the filter, rather than absent.

The catch is that these two methods simply do not stack linearly. When the gate is disabled, UMA expends its entire ranking capacity rejecting broken samples. This results in a worse volume error of 1.76 and a +2.3% cell over-expansion. Conversely, when the gate is active and handling the basic filtering, UMA's ranking is freed to operate among intact samples. That is exactly when it successfully drives the label-free volume correction we discussed in the first post.

In response to these excellent discussions, we have comprehensively revised the manuscript. We now explicitly label the volume term as experimental supervision. We state clearly that basic validity comes from discarding broken samples. We updated the tie thresholds in Section 4 and added the no-eligibility arm (which means no gate) to Table 2. Finally, we included detailed new appendices covering the three-seed results, volume-normalized PDD calibrations, the lattice-energy check, and the corrected UMA-cell analysis.

Reviewer_4LAjOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The question is pretty basic: where should you put physics for improving crystal structure generation? (1) in the training process? (2) post training? (3) in the inference? They then measure doing all of these with standard techniques, and show all of them are helpful. But they find that if you do it in post-training, then you don't have to keep doing it in inference time, which can be preferable if you need faster inference... which is a pretty obvious conclusion.

Critical strengths

The paper is solid: the benchmarks are solid, the idea is solid. It's just not too novel: it's a benchmark of things in the literature. It's information that needs to be documented, but not necessarily something all that wowing.

Critical weaknesses

The main weakness is that the result of all of these benchmarks is pretty obvious: if you fix up the weights then you don't have to tag something onto the end of the inference process and that makes the inference faster. Duh? So the answer isn't really that deep: all things help, do as many as possible, but some have a cost added on which is obvious by how the method works. These numbers are useful, I'm just not sure something that obvious is a conference paper though? But it will help the field to have this in a searchable database of things actually fully evaluated.

Questions for authors

What did you find that is very novel, that nobody else would have ever expected? Most (all?) of the results are very expected, so change to highlight anything unexpected at the end.

3 comments
AuthorsOpenReview ↗

Highlighting the Unexpected: Why "All Methods Help" is False and Inference-Time Physics Remains Mandatory

We thank the reviewer for the careful summary and evaluation. We agree with the central premise: shifting physical potential calculations from inference to post-training to achieve faster sampling is a design property, not an empirical discovery. We updated the introduction and contribution list to make this explicit.

To contextualize why different methods of injecting physics yield fundamentally different results, it is helpful to distinguish between physical preferences and physical invariants. Preferences are continuous, soft landscapes (e.g., energy surfaces) that are highly tolerant of noise, making them easier for generative models to learn. Invariants, however, are discrete, rigid constraints, such as severe steric clashes or chirality (stereochemistry), which the generator often cannot natively represent or learn. Our findings suggest that while models can learn soft physical preferences, learning alone cannot guarantee structural validity. Hard constraints often require explicit enforcement, and the resulting functional properties require independent verification.

Therefore, we respectfully disagree with the conclusion that "all of [the methods] are helpful, do as many as possible." When holding the generator, potential, initialization, and evaluation metrics constant, we found that several ways of adding the same physical signal do not help or hurt, and the parts that help do so for reasons other than the potential's physics.

Below are the results we found highly unexpected, each rigorously confirmed across three training seeds with tie thresholds fixed in advance (detailed in the new Appendices A.33–A.40 of the revision; three-seed Table S18):

  1. Validity is driven by discarding broken samples. A cheap heuristic filter and a deep physical potential achieve this independently, but their effects do not stack (Section 4.2, Table 2, Appendix A.36). The "gate-only" arm operates purely as a feasibility filter without ranking anything, yet it achieves a PoseBusters pass rate of 92.0%, compared to 91.4% for the full physical signal and 89.0% for the base model. Conversely, switching the gate off and relying entirely on UMA ranking (energy, force, stress) achieves an identical 92.0% pass rate. Counterintuitively, combining both approaches actually lowers the validity pass rate across all seeds. Independent MMFF94 evaluations confirm this: post-training halves the share of strongly distorted molecules, and the simple gate achieves this just as well as the full signal. Our interpretation is that a group-relative ranking expends its capacity either on separating broken from intact samples, or—if a filter has already done that—on correcting macroscopic properties like the cell.

  2. The physical potential improves packing solely by acting as a label-free volume corrector, matching direct experimental supervision (Appendices A.34, A.35, A.39). The UMA-only arm and an arm directly rewarding agreement with each family's experimental volume reach the exact same volume error (Vol.Err) and Packing Distance Distribution (PDD). After rescaling each cell to the experimental volume, the two arms become statistically equivalent. Therefore, the claim that "physics improves packing" reduces empirically to "the potential corrects the cell volume". The UMA potential itself does not natively prefer a different cell; relaxing the experimental crystals with UMA changes their volume by a median of only +0.12%. Furthermore, while lattice energy tracks volume better than total energy, we found it adds no predictive value beyond volume correction itself, which is why it was not fully trained.

  3. The exact same reward yields different outcomes depending on the RL update rule (Table S13). With an identical UMA reward, plain DiffusionNFT without the flow-map correction maintains a similar validity pass rate (92.66%) but actually moves packing away from experimental ground truth (Vol.Err 2.51, PDD 10.71 vs base 1.95 / 10.44). Conversely, our proposed flow-map-aware update successfully drives the distribution toward experiment (Vol.Err 1.69 / PDD 10.02).

  4. Some rigid constraints cannot be learned through weights and mandate inference-time correction (Section 4.3). The reviewer notes that fixing weights removes the need to tag physics onto inference, but stereochemistry proves otherwise. Because the generator's backbone is conditioned on a molecular graph that is identical for both mirror images, no RL reward can teach the model which enantiomer was requested. Across 20 training configurations, agreement with requested R/S labels remained at chance (49–53%). However, explicitly enforcing this invariant at inference time via a cheap parity inversion and local correction chain restores stereochemistry to 95%. This demonstrates that inference-time corrections are not obsolete; they are strictly necessary for physical properties that fall outside the generator's representation.

AuthorsOpenReview ↗

Highlighting the Unexpected (Continued): The Failure of Distillation, the Ranking Bottleneck, and Contributions Beyond Benchmarking

5. Training on relaxed targets fails to transfer the benefits of relaxation. While fixed-cell UMA relaxation effectively repairs local contacts at inference (dropping the clash rate from 11.3% to 5.0%), our "relax-and-distill" baseline demonstrates that training on these exact relaxed structures transfers neither the local repair nor any validity gain. In fact, the PoseBusters pass rate falls to 88.2%, underperforming the base model. This proves that the routes are fundamentally not interchangeable: post-training moves the macroscopic cell, inference-time relaxation repairs local contacts at a fixed cell, and distillation on relaxed targets achieves neither.

6. Improving sample quality does not intrinsically improve experimental structure recovery; the bottleneck is ranking, not generation. Generating better samples does not automatically translate to finding the right crystal in a screening campaign. We found that about half of the teaching targets have no matching candidate among the top 30 retained structures, for either the base or the post-trained model. Without energy ranking, post-training leaves the overall share of targets with any match essentially unchanged (48.8% vs. 48.4%). The energy ranking itself is the critical bottleneck, keeping only 16–17% of available matches in the top 30—barely better than a random cut (15%). Rigorous resampling (n_s = 150, k = 30, 779 teaching targets) confirms that the validity gained through post-training, with or without the gate, yields no statistically significant recovery gain. Lattice energy ranking similarly fails to improve this. Thus, recovery is constrained by the ranking function, which none of the generative routes structurally addresses.

What this means for practitioners Returning to our central argument, the true empirical discovery is not that post-training accelerates inference, but how practitioners must deliberately distribute different types of physical constraints across the generative pipeline. We have distilled these actionable takeaways into the introduction and a new route summary table. For basic structural validity (filtering out broken invariants), a cheap feasibility filter is entirely sufficient; surprisingly, piling the potential's deep ranking on top of it actually introduces a slight validity cost. The potential's true generative value lies in learning continuous preferences, which strictly requires our flow-map-aware update rule to succeed. Conversely, local contacts and stereochemistry remain rigid invariants that cannot be distilled away by training on relaxed targets, thus mandating inference-time correction. Finally, crystal recovery remains fundamentally bottlenecked by the ranking function, a limitation that merely shifting physics into the generator does not inherently resolve.

Contributions beyond the benchmark Because the algorithmic update rule dictates whether physical alignment actually improves crystal packing (as demonstrated in Result 3), we have explicitly separated our methodological contributions from the empirical benchmark results in the revision. These include CrystAF, to our knowledge the first few-step all-atom flow map for organic molecular crystals (utilizing a single adapter for 8–50 NFE), and the specific flow-map adaptation of negative-aware fine-tuning that makes these volume corrections possible. While we inherit the induced-velocity identity from MeanFlowNFT, our introduction of adjacent-knot interval sampling is entirely new. This crucial addition raises the flow-map-specific share of the gradient from 0.75% to 3–24%, providing the necessary training stability to successfully learn continuous physical preferences.

Changes to the manuscript Following this discussion, we have entirely rewritten the introduction and contributions to center on these six non-obvious empirical results, clearly distinguishing them from the architectural design properties. To thoroughly document these findings, we added a findings summary at the start of Section 4, a comprehensive route summary table, and new appendices containing the rigorous three-seed tables, volume-normalized PDD calibrations, MMFF94 strain analysis, UMA relaxation of experimental crystals, detailed recovery breakdowns, the no-gate arm results, and the lattice-energy checks.

Dear Reviewer 4LAj,

Thank you again for reviewing our paper. We wanted to gently follow up on the detailed rebuttal we posted recently, which addresses your main concern about novelty by detailing unexpected findings from our evaluation.

We would greatly appreciate it if you could let us know if these clarifications help address your initial concerns, or if there is anything else we can provide.

Best,

Authors

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.