acceptodds
Under review as a conference paper at ICLR 2027

Inference-Time Projection for Physically Valid Biomolecular Diffusion Models

Abstract

AlphaFold 3-style cofolding models predict biomolecular complexes with high structural accuracy, yet a large fraction of their outputs are physically invalid: chains overlap at interfaces, ligand bond lengths and angles are distorted, rings are non-planar, and stereocentres are inverted. Current approaches either steer the sampler with physics-informed potentials, which multiplies sampling cost and memory overhead making inference impossible on large complexes, or finetune the model, costing time and tying the fix to one architecture. We observe that, unlike structural accuracy, physical validity is fully verifiable at inference time from quantities the sampler already holds. We therefore treat physical validity as a constrained inference problem and introduce two closed-form projection operators applied to the diffusion model's denoised clean-coordinate estimate, : an inter-chain van der Waals projection that pushes apart the most severely clashing atom pairs, and a ligand distance-geometry projection that restores bond lengths, angles, internal contacts, planarity and chirality. Both operators are local, sparse and displacement-capped, require no network evaluations, gradients or importance sampling, and leave the denoiser and its weights untouched, so they can be dropped into any AF3-style sampler without retraining. Applied to two independently developed models, Boltz-2 and OpenFold-3, across five benchmarks (CASP15, CASP16, the PoseBusters monomer and complex sets, and the Boltz physical-validity test set), our method recovers perfect physical validity while preserving structural-accuracy and ligand-placement metrics. These gains are achieved with negligible runtime and memory overhead, providing a practical, model-agnostic route to physically valid all-atom structure prediction.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
alphafold, boltz, openfold, diffusion, projection. inference

Reviews

Among:
Shape:
1234this paper, Top 17%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.75 over 4 reviews, above 83% of the others.
Reviewer_f7yFOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper proposes an inference-time projection method for improving the physical validity of AF3-style biomolecular diffusion models. Two operators modify the denoised coordinate estimate during the final sampling steps. One corrects severe inter-chain steric clashes, while the other addresses ligand bond lengths, angles, internal clashes, planarity, and tetrahedral chirality. The method requires no retraining or additional denoiser evaluations.

The authors evaluate the approach on Boltz-2 and OpenFold-3 across five benchmarks, reporting 100% target-level best-of-five physical validity with nearly unchanged structural accuracy and minimal computational overhead. Ablation studies examine the timing of projection and compare in-loop correction with post-hoc alternatives. Additional analyses investigate covalent geometry and molecular packing.

Critical strengths

The main strength is the practical simplicity of the method. Bounded coordinate corrections can be inserted into existing AF3-style diffusion samplers without changing model weights or requiring additional denoiser evaluations. The approach addresses common geometric failures at inference time and appears applicable to independently developed models. The ablations in Table 2 also provide useful evidence that corrections are more effective during the low-noise tail than during churn or after sampling.

The empirical improvements are substantial under the reported evaluation protocol. On PoseBusters Complex, target-level best-of-five validity increases from 0.500 to 1.000 for Boltz-2 and from 0.585 to 1.000 for OpenFold-3, while the reported structural accuracy remains nearly unchanged (Table 1). The runtime comparisons in Table 4 show little additional cost. I also appreciate the authors’ effort to examine covalent geometry, packing, and nonbonded energies after projection.

Critical weaknesses

My main concern is that the headline accuracy–validity result relies on target-level best-of-five oracle evaluation. Table 3 defines validity as having at least one valid sample among five predictions. The reported 100% validity therefore does not establish that individual generated structures are consistently valid. It is also unclear whether the accuracy metrics in Table 1 use the same samples selected for validity. If different oracle selections are used, the nearly unchanged accuracy values may not establish that a single selected prediction is both accurate and valid. Per-sample validity and the accuracy of confidence-ranked valid candidates would make the practical benefit much clearer.

The comparison with the closest existing projection method is also incomplete. The paper states that inference-only GSP degrades structural accuracy, citing Chen et al. (2025a), but the cited inference-only experiments use different sampling settings. The revised Appendix D of that work also reports Boltz-2 post-processing experiments without full fine-tuning. These are not directly comparable, but they make the general claim about inference-only accuracy loss less clear. The absence of checkpoints for the fine-tuned GSP model is understandable, while a matched inference-only comparison using the same Boltz-2 checkpoint would be more informative. Without it, the advantage over existing projection approaches is harder to establish.

Questions for authors
  1. How are samples selected for the accuracy and validity columns of Table 1? Could the authors report per-sample validity and the structural accuracy obtained after selecting a valid prediction using model confidence? This would help establish whether the reported accuracy and validity can be achieved simultaneously in a practical selection procedure.
  2. Section 3.1 examines four CASP16 targets selected for their highest projection activity. Is the reported reduction in the raw denoiser’s penetration also observed across a broader, less selectively chosen set of targets? The current bootstrap intervals reflect 20 trajectories from these four targets.
  3. Could the authors clarify the relationship to inference-only GSP and, if possible, provide a matched comparison using the same Boltz-2 checkpoint and sampling budget? This would help distinguish the benefit of the proposed bounded corrections from existing inference-time projection methods.
  4. Does the implementation include any E/Z stereochemistry correction absent from Algorithms 3–6? If not, could the authors clarify the coverage of the validity evaluation? Please also specify the corrected planarity-check procedure and the Boltz-2 chirality parameter configuration in Appendix C.2.
4 comments
AuthorsOpenReview ↗

Evaluation metric and GSP comparison

How are samples selected for the accuracy and validity columns of Table 1? Could the authors report per-sample validity and the structural accuracy obtained after selecting a valid prediction using model confidence?

We thank the reviewer for the detailed and helpful review. The reviewer is right that a best-of-five oracle score says little about whether every individual prediction is physically valid. Our submission reported oracle numbers because this is the convention of the evaluation scripts released with Boltz and later used by GSP, and we wanted our evaluation to be directly comparable with theirs. Nevertheless, we acknowledge that consistency with established evaluation protocols does not overcome the inherent limitations of oracle-based metrics.

As suggested by the reviewer, we have replaced oracle-based reporting with per-sample validity and confidence-selected top-1 validity, alongside structural accuracy evaluated on the same confidence-selected predictions. We have also added an evaluation with PoseBusters, as requested by Reviewer VuH7. PoseBusters is an independent and widely used tool that checks ligand geometry, stereochemistry and protein–ligand contacts, so it lets us test whether the gains hold outside the validity checks used in the submission. We hope that this extended evaluation eliminates reviewers' main concern about our results.

Could the authors clarify the relationship to inference-only GSP and, if possible, provide a matched comparison using the same Boltz-2 checkpoint and sampling budget?

We thank the reviewer for this point and have performed evaluation of GSP using their appendix D experiment, which is possible without the unreleased fine tuning checkpoints. To ensure fair comparison, we use the same base model, Boltz-2, five diffusion samples per target, 10 recycling steps, 200 diffusion steps, identical inputs and precomputed MSAs, and the same random seed. We follow the constraint schedule, solver iterations and guidance weight implemented in the GSP code and apply their correction with all constraints enabled. The results given below will be added to the manuscript as well.

CASP15

MethodlDDT ↑lDDT-PLI ↑Published eval valid ↑PoseBusters valid ↑Time ↓Memory ↓
Boltz-20.449 / 0.4500.519 / 0.54561.5 / 63.6%35.0 / 25.0%55.4s11.9 GiB
GSP0.447 / 0.4490.520 / 0.544100 / 100%88.3 / 100%59.4s12.1 GiB
Ours0.448 / 0.4500.523 / 0.548100 / 100%100 / 100%56.0s11.9 GiB

CASP16

MethodlDDT ↑lDDT-PLI ↑Published eval valid ↑PoseBusters valid ↑Time ↓Memory ↓
Boltz-20.437 / 0.4370.307 / 0.31753.5 / 53.8%31.1 / 33.3%56.0s11.8 GiB
GSP0.433 / 0.4340.301 / 0.268100 / 100%86.7 / 77.8%62.6s12.1 GiB
Ours0.434 / 0.4320.299 / 0.265100 / 100%100 / 100%56.0s11.8 GiB

PoseBusters Complex

MethodlDDT ↑lDDT-PLI ↑Published eval valid ↑PoseBusters valid ↑Time ↓Memory ↓
Boltz-20.8995 / 0.90370.8066 / 0.808428.3 / 28.0%67.2 / 72.7%71.3s22.2 GiB
GSP0.8986 / 0.90270.8045 / 0.806099.0 / 98.8%98.1 / 98.8%83.9s22.2 GiB
Ours0.8993 / 0.90420.8070 / 0.810799.4 / 99.4%98.6 / 98.8%74.2s22.2 GiB

Notes: Accuracy and validity values are reported as per-sample / top-1. Per-sample averages across five generated structures per target; top-1 evaluates the highest-confidence prediction. Bold indicates the best value between GSP and Ours, including ties. Time is the mean structure-prediction runtime per target for five samples (seconds), excluding process start-up, input processing, and checkpoint loading. Memory is mean peak reserved GPU memory (GiB).

We evaluate both methods on CASP15, CASP16, and PoseBusters Complex, measuring structural accuracy (lDDT and lDDT-PLI), physical validity, inference time, and GPU memory usage. Our method achieves 100% per-sample PoseBusters validity on CASP15 and CASP16, compared with 88.3% and 86.7% for GSP, respectively, while maintaining comparable structural accuracy and lower inference time. Our method integrates physical corrections into the denoising process, allowing the learned prior to incorporate these corrections into the evolving structure rather than enforcing constraints solely on the final coordinates. The improvements observed under the independent PoseBusters evaluation therefore provide evidence that our approach addresses underlying physicochemical inconsistencies and generalizes beyond the specific criteria of the original evaluation protocol.

AuthorsOpenReview ↗

Broader projection activity analysis, E/Z and Planarity corrections and Boltz-2 chirality parameter.

Section 3.1 examines four CASP16 targets selected for their highest projection activity. Is the reported reduction in the raw denoiser’s penetration also observed across a broader, less selectively chosen set of targets?

We thank the reviewer for this question and have repeated the analysis on a much broader, non-selected set of targets. We instrumented the sampler on every target in CASP15, CASP16, and the PoseBusters Complex set on which the van der Waals projection can act at all. These are 225 targets, giving 1,125 trajectory pairs, none of which was selected based on projection activity or outcome.

The two findings of Section 3.1 hold across the full set.

First, the model retains a small, stable fraction of each correction. The rebound ratio is 0.908 (95% CI [0.899, 0.918]) across all 225 targets and lies between 0.904 and 0.921 on each dataset. It remains essentially unchanged when the four most projection-active targets, which we reported initially, are excluded (0.906).

Second, the penetration of the model's own, unprojected prediction x0raw decreases over the projection window, while that of the seed-matched control increases. The median decline per trajectory is 66.8% (95% CI [65.8%, 67.9%]), whereas penetration in the seed-matched control increases by a median of 12.5% (95% CI [10.7%, 13.8%]).

We will include the per-dataset breakdown in a new appendix table.

Does the implementation include any E/Z stereochemistry correction absent from Algorithms 3–6? If not, could the authors clarify the coverage of the validity evaluation?

We thank the reviewer for raising this point. E/Z stereochemistry violations are included in our published validity evaluation and are explicitly checked. As reported, we did not observe any such violations across the datasets in any samples, and therefore did not include a dedicated E/Z Algorithm in the manuscript. However, following reviewer VuH7's suggestion to conduct an independent PoseBusters evaluation, we identified incorrect E/Z double-bond isomers in some samples from two PoseBusters Complex targets. This is because Posebusters’ criteria for E/Z test is much stricter: it fails at about 55 degrees of twist, against 90 degrees allowed by the evaluation developed by Boltz. We have now implemented an E/Z correction which resolves these violations through a single rigid rotation of the smaller side of each affected bond to its correct planar geometry. We will add this step in the planarity algorithm description accordingly. The results reported above include this correction, which eliminates the identified E/Z violations without degradation in structural accuracy, inference time, or GPU memory usage. We thank the reviewer for helping us improve the completeness of our method.

Please also specify the corrected planarity-check procedure

We thank the reviewer for requesting this clarification. The modification in Appendix E.1 corrects an inverted condition in the five-membered-ring planarity evaluator (check_ligand_flatness) in https://github.com/jwohlwend/boltz/blob/main/scripts/eval/physcialsim_metrics.py#L120

Incorrect (Boltz): np.all(ring_5_dists <= 0.25, axis=-1)

Corrected (Ours): np.any(ring_5_dists >= 0.25, axis=-1)

The incorrect condition flags geometrically correct, planar rings as violations, whereas the corrected condition flags rings with at least one atom deviating by 0.25 Å or more from the best-fit plane. We quantified the effect across all generated samples using the unmodified published evaluator as the reference.

DatasetMethodCorrect evaluator (%)Incorrect evaluator (%)Difference (pp)
CASP15 (66)Boltz-261.5 / 63.661.5 / 63.60 / 0
Boltz-2x99.7 / 100.099.7 / 100.00 / 0
GSP100.0 / 100.0100.0 / 100.00 / 0
Ours100.0 / 100.0100.0 / 100.00 / 0
CASP16 (52)Boltz-253.5 / 53.853.5 / 53.80 / 0
Boltz-2x100.0 / 100.096.2 / 96.2+3.8 / +3.8
GSP100.0 / 100.096.2 / 96.2+3.8 / +3.8
Ours100.0 / 100.096.2 / 96.2+3.8 / +3.8
PoseBusters Complex (161)Boltz-228.3 / 28.027.3 / 27.3+1.0 / +0.6
Boltz-2x99.3 / 99.496.8 / 96.9+2.5 / +2.5
GSP99.0 / 98.896.5 / 96.3+2.5 / +2.5
Ours99.4 / 99.496.9 / 96.9+2.5 / +2.5

Notes: All validity values are per-sample / confidence-selected top-1. Difference is correct - incorrect evaluator, in % points.

the Boltz-2 chirality parameter configuration in Appendix C.2.

The chirality parameter, K, for Boltz-2 is 1. We will add this information to the manuscript.

We thank the reviewer for their astute observations and helpful suggestions. We hope our answers have removed concerns; we look forward to continued discussion.

Thank you for the detailed response and the additional experiments. I appreciate the effort to address the concerns raised in my review.

The per-sample and confidence-selected top-1 results address my main concern about oracle-based evaluation. The matched GSP comparison and independent PoseBusters evaluation also make the empirical contribution considerably more convincing. I am particularly glad to see the mechanism analysis extended to 225 targets, with the main findings remaining consistent.

The explanations regarding E/Z stereochemistry and the planarity evaluator are helpful. For reproducibility, I would encourage the authors to include the new E/Z correction in the revised algorithm and clarify whether the Boltz-2 chirality parameter is κ = 1.

Overall, I find the rebuttal convincing. The additional evidence has substantially strengthened my assessment, and I am inclined to update my recommendation to weak acceptance.

Thank you for your constructive feedback; we appreciate the revised score.

Reviewer_VuH7OpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes inference-time geometric corrections for improving the physical validity of AF3-style biomolecular diffusion models without retraining. The method combines an inter-chain van der Waals correction with ligand distance-geometry corrections for local geometry, planarity, and chirality. These bounded updates are applied primarily during the low-noise tail of sampling.

Experiments on Boltz-2 and OpenFold-3 across five benchmark sets show that every evaluated target has at least one valid prediction among five samples under the adopted Boltz validity checks, while aggregate structural accuracy remains largely unchanged and computational overhead is small. Additional experiments investigate correction timing, post-processing alternatives, covalent geometry, and local packing.

Critical strengths
  1. A practical intervention with convincing evidence of low computational overhead. The method requires neither retraining nor additional denoiser evaluations and is demonstrated on two independently developed base models. Tables 1 and 4 show substantial improvements in target-level validity with largely unchanged structural metrics and low runtime and memory overhead. Completing targets for which Boltz-2x runs out of memory further supports its practical relevance.

  2. The paper investigates when corrections work and checks several potential side effects. The timing ablations and trajectory analyses help explain the effectiveness of corrections during the sampling tail. The post-processing comparisons and supplementary MolProbity, energy, and packing analyses provide evidence beyond the primary validity metric.

Critical weaknesses
  1. The incremental contribution over prior physics-guided sampling and simpler post-processing alternatives is not sufficiently discussed. A directly relevant omission is PhysDock (Zhang et al., 2025), which already applies physical corrections to denoised ligand structures during diffusion and uses the corrected coordinates in subsequent sampling. Its noise-dependent conformer-matching and force-field corrections differ from the operators proposed here, but the central denoise–correct–update principle is closely related. Consequently, the statement in Section 1 that only two methods directly address physical invalidity in biomolecular diffusion requires qualification, and the contribution needs to be positioned explicitly against this prior work. PhysDock paper; paper-associated sampling implementation.

    The bounded local operators, explicit inter-chain correction, and application to frozen cofolding models are meaningful distinctions. However, the current comparisons do not sufficiently isolate their contribution. I acknowledge the post-hoc projection experiments in Table 2 and the Phenix comparison in Appendix G.1. Nevertheless, the latter excludes ligand-bearing targets, while the former uses identical hyperparameters and a fixed iteration budget that need not be well suited to post-processing. A controlled comparison with an appropriately configured protein–ligand post-processing baseline would better establish the advantage of integrating corrections into sampling. Moreover, Table 2 finds equivalent performance for correcting the noisy iterate and the clean estimate in the tail, limiting the evidence for clean-estimate projection as a distinctive contribution.

  2. The headline validity claim is broader than the demonstrated reliability and scope of the evaluation. The reported 100% validity is a target-level best-of-five result: at least one sample passes the adopted checks. It does not establish that all generated samples are valid, or that a practically selected prediction is simultaneously valid and accurate. Appendix D explicitly reports 19 clash-free structures out of 20 in one diagnostic experiment. Validity-based filtering is feasible without an experimental reference, so the best-of-five result is useful; the missing evidence is the accuracy and joint success rate of predictions selected after such filtering.

    The Boltz checks are legitimate measures of geometric validity, but they are not equivalent to the complete PoseBusters suite or a general certificate of physical realism. Evaluating on the PoseBusters datasets does not resolve this distinction. The independent analyses in Appendix G are valuable, but protein-only MolProbity checks and Lennard-Jones energy comparisons do not substitute for broader ligand and complex-level validation. Section 4 appropriately acknowledges these limitations, whereas the headline claims remain stronger.

    The robustness evidence also leaves an important qualification unresolved. Table 8 supports reasonably broad tolerance to several vdW parameters, but does not systematically assess the ligand-specific tolerances, sweep count, and chirality margin. Different settings are used for Boltz-2 and OpenFold-3, and the sensitivity set is drawn from the principal evaluation benchmarks without a clear account of where the final parameters were selected. This does not demonstrate improper tuning, but it limits the evidence for general applicability.

Questions for authors
  1. How does the proposed method differ from PhysDock at the operator and sampling-integration levels? Could a controlled comparison or targeted ablation establish the contribution beyond the existing denoise–correct–update principle? A comparison of complete systems with different inputs would be less informative than one using the same frozen denoiser and sampling conditions.

  2. Can the post-processing comparison be extended to ligand-bearing complexes, allowing reasonable baseline-specific parameter selection and reporting runtime alongside quality? This would help determine whether the observed advantage persists against a competitive simple alternative.

  3. Are the oracle accuracy and validity metrics in Table 1 selected independently across samples? Please report per-sample validity and the joint validity–accuracy success rate for the same selected prediction, including a practical rule that filters invalid samples and then ranks the remaining samples by model confidence. Full PoseBusters evaluation on the applicable protein–ligand subset would further clarify the scope of the result.

  4. Where were the final hyperparameters selected, and was this set separate from the reported test targets? Please clarify the sensitivity of the ligand-specific settings and whether one shared configuration transfers between Boltz-2 and OpenFold-3.

5 comments
AuthorsOpenReview ↗

Comparison with PhysDock: operators, integration and controlled ablation

We would like to thank the reviewer for their thoughtful comments. We apologise for the delayed response, which mainly reflects our aim to answer fully, with new analyses, and partly unforeseen personal circumstances affecting the first author. We hope our responses and new results address the reviewer’s concerns.

the statement in Section 1 that only two methods … requires qualification

How does the proposed method differ from PhysDock … sampling-integration levels?

We thank the reviewer for these comments. We agree that PhysDock and our method share the general denoise–correct–update principle. Both correct the denoised estimate x̂₀ and feed the corrected structure back into the reverse update. We do not claim this principle as our contribution. We already discuss it in Related Work (Projected Diffusion Models, Predict–Project–Renoise) and will add PhysDock there. Our contribution lies in the operators themselves and in how they are integrated into the sampler. The table below summarises the differences.

PhysDockOurs
GoalStandalone protein–ligand docking modelInference-time validity correction for any AF3-style model
Molecule typesProtein + one small-molecule ligandProteins, nucleic acids, ligands
Acts onLigand onlyInter-chain contacts and ligand geometry
OperationReplaces the ligand: closest library conformer (high noise) or MMFF-relaxed copy (low noise)Nudges the model's estimate toward feasibility
Constraint sourceRDKit conformers, MMFFvdW radii, RDKit distance-geometry bounds
Bond lengths / anglesImplicit (conformer swap or MMFF)Distance intervals on bonded and angle pairs
Internal ligand clashesImplicit (conformer swap or MMFF)Lower bound on other intra-ligand pairs
PlanarityImplicit (conformer swap or MMFF)Pulls aromatic rings and C=C groups onto a fitted plane
ChiralityConformer swap; MMFF only preserves itNewton step on signed volume, latched against flip-back
E/Z stereoConformer swap; MMFF only preserves itNo dedicated term
Protein–ligand clashesNot modelledCorrected (ligands are separate chains)
Inter-chain clashesNot modelledCorrected
Size of moveWhole-ligand swapCapped per atom (0.2–0.45 Å)
When appliedHigh and low noise, switching at an adaptive thresholdFinal ~40 of 200 steps

Could a controlled comparison or targeted ablation … same frozen denoiser and sampling conditions.

Following the reviewer's suggestion, we re-implemented PhysDock's two operators (MIT-licensed, with attribution) inside our own frozen Boltz-2 sampler, at the same hook our projection uses. Everything is held fixed (weights, 200-step schedule, ρ, seeds, MSAs, recycling, evaluators); only the function applied to x̂₀ varies. 182 ligand-bearing targets; per-sample and top-1.

Table A: Physical validity

Valid % (per-sample / top-1)Boltz-2PhysDockOurs (ligand only)PhysDock + our vdWOurs
CASP1561.5 / 63.660.6 / 62.162.1 / 65.296.7 / 95.5100 / 100
CASP1653.5 / 53.853.1 / 53.853.5 / 53.8100 / 100100 / 100
PB complex28.3 / 28.023.0 / 24.833.0 / 34.285.3 / 85.799.4 / 99.4

Table B: Ligand-class violations

Any ligand-class violation %Boltz-2PhysDockOurs (ligand only)PhysDock + our vdWOurs
CASP153.3 / 4.53.3 / 4.50.0 / 0.03.3 / 4.50.0 / 0.0
CASP160.0 / 0.00.0 / 0.00.0 / 0.00.0 / 0.00.0 / 0.0
PB complex15.8 / 16.814.7 / 13.70.6 / 0.614.7 / 14.30.6 / 0.6

In summary:

PhysDock's operators do not improve validity on any of the three sets, and reduce it on PB complex (28.3 → 23.0). Transplanted into the same sampler under the same conditions, the shared denoise–correct–update principle does not by itself produce the result.

CASP16 is the cleanest ablation: CASP16 does not have a single ligand-class violation, so validity is purely the inter-chain question. PhysDock's operators leave it at 53.1% against the stock sampler's 53.5%; adding our inter-chain projection takes the same arm to 100%.

Ligand geometry. Within that shared scope the operators differ sharply: 14.7% of PB complex samples still carry a ligand violation after PhysDock's operators, against 0.6% after ours. Chirality: 13.4 / 13.7 (stock) → 12.8 / 11.2 (PhysDock) → 0.0 / 0.0 (ours); PhysDock's chirality guarantee is not an operator but an outer rejection-sampling loop (≤5 rounds × 20 samples), which cannot act within a rollout.

Conclusion: both terms are necessary. Adding our inter-chain term to PhysDock's operators clears every chain clash but leaves validity at 85.3% on PB complex, because their ligand operator still leaves 14.7% of samples with a ligand violation. Only the combination of a bounded inter-chain term and a bounded ligand-geometry term reaches 99.4%.

AuthorsOpenReview ↗

Comparison with force-field relaxation on ligand-bearing complexes

Can the post-processing comparison be extended to ligand-bearing complexes, allowing reasonable baseline-specific parameter selection and reporting runtime alongside quality? …

We thank the reviewer for this comment. Our original geometric minimisation could not deal with ligands, thus, we repeated the analysis with force-field relaxation (Amber14 for proteins and nucleic acids, OpenFF Sage 2.2.1 for small molecules). For each structure, we run the minimisation in vacuum with harmonic restraints of 10 kcal/mol/Ų on all heavy atoms (L-BFGS, at most 1,000 iterations).

We wanted to point that relaxation cannot be applied directly to raw model output. The force-field system requires checking polymers integrity, adding hydrogens and parametrising small molecules. The parameterisation of non-biological molecules often requires manual supervision and may result in relaxation failures if not handled correctly. This is one reason why, unlike the protein-only AF2-like models, current AF3-like predictors are not shipped with a relaxation step.

We therefore checked all components other than polymers, water, and single-atom ions for features that could cause relaxation to fail. (1) For a ligand, the force field chemical library must cover all atoms. This excludes metal-containing cofactors, as well as boron, silicon and selenium compounds. (2) Bond orders and formal charges must be valid; they are taken from a reference SMILES, the PDB Chemical Component Dictionary, mmCIF bonds or Open Babel inference, and must pass RDKit sanitization. (3) Partial charges must be computable. As this may not be possible for unusual or highly charged molecules, and very large ligands may time out. (4) The force field must assign parameters to every bond, angle, torsion and atom type, which fails for uncommon chemistry such as molecular oxygen.

A structure fails the checks if any ligand fails. Passing our checks shows that a ligand can be parametrised; it does not guarantee that its chemistry is correct. Inferred bond orders may be incorrect, protonation is assumed, and covalent links to the protein are ignored. Results are reported in the table.

DatasetPassed (targets / samples)Failed (targets / samples)Cause of failure (targets / samples)
CASP1562 / 3104 / 20Ligand chemistry (3 / 15); ion template (1 / 5)
CASP1651 / 2551 / 5DNA template (1 / 5)

We relaxed every structure, including those that failed the checks. Every structure that failed the checks also failed relaxation, and every structure that passed relaxed successfully. For the relaxed structures:

DatasetMethodTargets / samplesLigand targets (PoseBusters / LDDT-PLI)lDDTLDDT-PLIPublished eval valid %PoseBusters valid %Added time per target vs Boltz-2
CASP15Boltz-266 / 33012 / 110.449 / 0.4500.519 / 0.54561.5 (203/330) / 63.6 (42/66)35.0 (21/60) / 25.0 (3/12)base: 55.4 s
Relaxed Boltz-262 / 3108 / 70.426 / 0.4290.504 / 0.50394.2 (292/310) / 93.5 (58/62)97.5 (39/40) / 100.0 (8/8)+43.8 s (median +37.8 s)
Ours66 / 33012 / 110.448 / 0.4500.523 / 0.548100.0 (330/330) / 100.0 (66/66)100.0 (60/60) / 100.0 (12/12)+0.3 to +0.9 s
CASP16Boltz-252 / 2609 / 90.437 / 0.4350.309 / 0.31953.5 (139/260) / 53.8 (28/52)31.1 (14/45) / 33.3 (3/9)base: 56.2 s
Relaxed Boltz-251 / 2559 / 90.432 / 0.4320.328 / 0.33785.1 (217/255) / 86.3 (44/51)100.0 (45/45) / 100.0 (9/9)+44.5 s (median +38.4 s)
Ours52 / 2609 / 90.434 / 0.4340.310 / 0.282100.0 (260/260) / 100.0 (52/52)100.0 (45/45) / 100.0 (9/9)+0.2 to +0.7 s

We identified three types of failure here. (1) Structures that cannot be prepared for the force field produce no relaxed output, so five targets are missing from the relaxed rows. The four CASP15 ones are ligand targets and include the most challenging stereochemistry cases, meaning the relaxed CASP15 ligand results are based on only eight of the twelve ligand targets, whereas our method applies to all twelve. (2) Restrained minimisation does not separate clashing chains sufficiently, so inter-chain clashes remain a primary cause of failure: 14.9% of the CASP16 relaxed samples (eight complexes) and 5.2% of the CASP15 relaxed samples (four complexes) still have inter-chain clashes. (3) Lastly, minimisation cannot invert stereocentres; therefore, the one CASP15 ligand showing this retained both chirality and internal-clash violations.

We hope this analysis demonstrates that, while useful, relaxation depends on a fragile preparation pipeline and still leaves violations unresolved. In contrast, our projection works on every structure produced by the model, with no parameterisation and negligible overhead.

AuthorsOpenReview ↗

Evaluation protocol, PoseBusters validation and hyperparameter robustness

Are the oracle accuracy and validity metrics in Table 1 selected independently across samples? … report per-sample validity and the joint validity–accuracy success rate …

We acknowledge that the 'best-of-five' oracle validity metric is not the most accurate way to evaluate the effectiveness of our projection in fixing physical violations. For comparability with published results, our original evaluation used the same scripts as Boltz and the most closely related method, GSP. However, we agree that consistency with prior work does not justify the limitations of the oracle evaluation. To address this, we have removed the oracle metric and now report per-sample validity and confidence-ranked top-1 validity, as well as structural accuracy. All of these are evaluated using the same selected samples.

Full PoseBusters evaluation … further clarify the scope of the result.

As suggested, we now include an independent PoseBusters evaluation. Below are our results on CASP15, CASP16 and PoseBusters Complex. We report lDDT, lDDT-PLI, physical validity, inference time and GPU memory (per-sample / top-1). Our method achieves 100% PoseBusters validity on CASP15 and CASP16, and over 98.5% on PoseBusters Complex (over 99% under the published evaluation). A full comparison with Boltz-2x will be added to the main table of the manuscript.

DatasetMethodlDDT ↑lDDT-PLI ↑Published eval valid (%) ↑PoseBusters valid (%) ↑Time (s) ↓Memory (GB) ↓
CASP15Boltz-20.449 / 0.4500.519 / 0.54561.5 / 63.635.0 / 25.055.411.9
Ours0.448 / 0.4500.521 / 0.545100 / 100100 / 10054.611.9
CASP16Boltz-20.437 / 0.4370.307 / 0.31753.5 / 53.831.1 / 33.356.011.8
Ours0.433 / 0.4350.293 / 0.322100 / 100100 / 10055.211.8
PoseBusters ComplexBoltz-20.8995 / 0.90370.8066 / 0.808428.3 / 28.067.2 / 72.771.322.2
Ours0.8993 / 0.90420.8070 / 0.810799.4 / 99.498.6 / 98.874.222.2

We thank the reviewer: the PoseBusters evaluation has materially strengthened our paper.

Where were the final hyperparameters … separate from the reported test targets?

Our published configuration was chosen on the 134-target subset of CASP15, CASP16, PoseBusters Monomer and PoseBusters Complex reported in Tables 2 and 8. We then apply the selected hyperparameters to the full versions of these four datasets and the fifth held-out benchmark, the Boltz physical-validity Test set (541 targets).

Please clarify the sensitivity of the ligand-specific settings

We varied each ligand setting one at a time around the final configuration on CASP15, CASP16 and PoseBusters Complex, with paired, Holm-corrected significance tests. Physical validity (%), per-sample / top-1, on PoseBusters Complex unless stated otherwise; "stable" means at most two more invalid samples than the final configuration on every dataset.

SettingValues testedValidity
Bond buffer β_b0, 0.19, 0.20, 0.24, 0.30Stable 0–0.24. At 0.30 (past the 25 % tolerance): 90.1 / 91.9 (bond lengths)
Angle buffer β_a0, 0.20, 0.24, 0.30Stable only 0.20–0.24. At 0.30: 92.2 / 95.7 (angles). At 0: 92.0 / 91.3 (chirality)
Internal-clash buffer β_c0, 0.15, 0.19, 0.25Stable 0–0.15. At 0.19: CASP15 97.9 / 100. At 0.25 (past the 20 % tolerance): CASP15 95.8 / 97.0, PoseBusters Complex 97.5 / 98.8
Planarity buffer β_p0, 0.19, 0.30 ÅStable at all values
Sweeps per call N_sw0, 1, 2, 3, 5Stable 1–5. At 0 (ligand projection off): 82.0 / 83.2
Per-atom cap δ_ldg0, 0.1, 0.2, 0.45 ÅStable 0.1–0.45. At 0: 82.5 / 83.9
Chiral margin κ0, 0.1, 1.0, 2.0Stable 0.1–2.0. At 0: 94.7 / 94.4. However, 2.0 lowers LDDT-PLI, hence κ = 1.0
Ligand start t0, 0.05, 0.2, 1.0Stable 0.2–1.0. At 0.05: 97.9 / 98.1. At 0 (off): 82.0 / 83.2
  • Validity: stable over wide ranges for every setting except the angle buffer.
  • Accuracy: the only significant changes are −0.00014 lDDT (angle buffer 0) and at most 0.00065 LDDT-PLI.

whether one shared configuration transfers between Boltz-2 and OpenFold-3.

The two models use slightly different configurations (Appendix C.2); however, most of OpenFold-3's values lie inside the stable ranges above:

  • vdW α = 1.0, δ_max = 0.3 Å, β = 0.15 and K = 200 (Table 8: oracle validity 1.00 around the published Boltz-2 configuration);
  • ligand cap 0.25 Å, between two stable values (0.2 and 0.45);
  • N_sw = 3;
  • bond buffer 0.24.

Only two do not:

  • the internal-clash buffer of 0.19 is just outside (7 more invalid CASP15 samples, not significant);
  • the angle buffer of 0.10 lies between a failing value (0) and the stable range (from 0.20).

We hope the reviewer finds our responses and analyses satisfactory, we will update the manuscript as well. We apologise again for the delay and we are happy to continue the discussion.

Reviewer_6xxMOpenReview ↗
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3
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2
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Paper summary

This manuscript proposes an elegant training-free inference-time method for improving the physical validity of AlphaFold 3-style structure prediction models. It applies bounded geometric corrections to denoised clean-coordinate estimates during the final low-noise sampling steps, combining an inter-chain van der Waals operator for steric clashes with a ligand distance-geometry operator addressing bonds, angles, internal clashes, planarity, and chirality. The method leaves model weights unchanged and requires no additional denoiser evaluations. Experiments evaluate Boltz-2 and OpenFold-3 across five benchmarks: CASP15, CASP16, PoseBusters monomers and complexes, and the Boltz physical-validity test set. The authors report 100% target-level validity under oracle best-of-five evaluation, while largely preserving structural accuracy with negligible measured runtime and memory overhead.

Critical strengths
  1. Practical value of a lightweight, training-free correction. The method improves physical validity without retraining, modifying model weights, or requiring additional denoiser evaluations. Its bounded geometric corrections incur negligible reported runtime and memory overhead, making integration into existing prediction pipelines practical. This is consequential because it addresses physical defects while preserving the computational advantages of pretrained structure prediction models.

  2. Consistent validity improvements with limited impact on structural accuracy. Experiments on Boltz-2 and OpenFold-3 across five benchmarks report 100% target-level physical-validity pass rates under oracle best-of-five evaluation, while largely preserving structural accuracy. Ablations and additional geometry, packing, and energy assessments strengthen the empirical support. These results suggest that the benefits extend beyond a single model implementation and support the central claim that local inference-time corrections can improve validity without a substantial accuracy trade-off.

Critical weaknesses

None

Questions for authors
  1. The main results use oracle best-of-five evaluation and do not clearly establish whether the same practically selected prediction achieves both the reported validity and accuracy. Per-sample validity rates and the accuracy of confidence-ranked valid predictions would provide stronger evidence.

  2. Could the authors provide an independent assessment of ligand strain and stereochemistry, given that Appendix G’s MolProbity analysis excludes ligands?

  3. Table 8 mainly studies vdW parameters. Please compare vdW-only, ligand-geometry-only, and combined configurations, reporting results separately for each violation type.

  4. Table 3 reports no E/Z or planarity violations in the oracle-selected predictions. Please provide additional cases demonstrating the correction of these violations and explain how the proposed operators enforce E/Z stereochemistry.

6 comments

Please respond to the questions raised in my review as soon as possible. If you do not engage in a substantive discussion in accordance with ICLR’s guidelines, I will consider lowering my rating.

We sincerely apologize for the delay in our response and thank the reviewers for their patience. Unfortunately, serious unforeseen personal circumstances affecting one of the authors prevented us from completing our responses to reviewers 6xxM and VuH7 over the past two days. We recognize that we should have communicated this earlier, and we apologize for not doing so. We are now finalizing our responses and will ensure that they are submitted in time for the discussion.

AuthorsOpenReview ↗

Per-Sample Validity and Independent PoseBusters Evaluation

We thank the reviewer for their useful comments on our work. We once again sincerely apologize for the delayed response, which was caused by unforeseen personal circumstances that affected the first author's ability to work on the rebuttal over the past few days. We hope that our responses and updated results will help clarify the points raised and address the reviewer's concerns.

The main results use oracle best-of-five.. Per-sample validity rates and the accuracy of confidence-ranked valid predictions would provide stronger evidence.

We would like to thank the reviewer for this thorough feedback. We acknowledge that the 'best-of-five' oracle validity metric is not the most effective way of accurately assessing the ability of our projection to fix physical violations. Our original evaluation employed the same scripts as Boltz and the most closely related method, GSP, in order to ensure consistency and comparability with previously published results. We agree, however, that consistency with previous work does not justify the limitations of the oracle evaluation. To address this concern, we have removed the oracle metric and now report per-sample validity and confidence-ranked top-1 validity together with structural accuracy, both of which are evaluated using the same selected samples. Furthermore, in line with reviewer VuH7's suggestion, we now include an independent evaluation using Posebusters in our analysis. Posebusters is a widely used framework for assessing physical validity. Here, we present the results of our evaluation on CASP15, CASP16 and the PoseBusters Complex. We report on structural accuracy (lDDT and lDDT-PLI), physical validity, inference time and GPU memory usage. Our method achieves 100% per-sample PoseBusters validity on CASP15 and CASP16 and over 99% for PoseBusters Complex dataset. A full comparison with Bolt2-x will be added to the manuscript main table.

DatasetMethodlDDT ↑lDDT-PLI ↑Published eval valid ↑PoseBusters valid ↑Time ↓Memory ↓
CASP15Boltz-20.449 / 0.4500.519 / 0.54561.5 / 63.6%35.0 / 25.0%55.4s11.9GB
Ours0.448 / 0.4500.521 / 0.545100 / 100%100 / 100%54.6s11.9GB
CASP16Boltz-20.437 / 0.4370.307 / 0.31753.5 / 53.8%31.1 / 33.3%56.0s11.8GB
Ours0.433 / 0.4350.293 / 0.322100 / 100%100 / 100%55.2s11.8GB
PoseBusters ComplexBoltz-20.8995 / 0.90370.8066 / 0.808428.3 / 28.0%67.2 / 72.7%71.3s22.2GB
Ours0.8993 / 0.90420.8070 / 0.810799.4 / 99.4%98.6 / 98.8%74.2s22.2GB

We believe these changes provide a more rigorous and transparent assessment of our projection ability to fix physical violations.

Could the authors provide an independent assessment of ligand strain and stereochemistry, given that Appendix G’s MolProbity analysis excludes ligands?

We thank the reviewer for highlighting this issue, and we agree that the original manuscript did not provide an independent assessment of ligand strain and stereochemistry outside our own evaluations. We have now used Posebusters to extend our evaluation to include a complete assessment of physical validity for the ligands and the protein–ligand interactions. Results can be found in the table above (PoseBuster valid column). In particular, PoseBusters provides an independent assessment of the chemical and physical plausibility of ligand-containing complexes. These checks are performed directly on the raw, unrelaxed predictions and are the following: (i) the chemical identity and stereochemical consistency of the ligand requested, including molecular connectivity, tetrahedral chirality and double-bond stereochemistry; (ii) the geometry of the ligand within the molecule, including bond lengths and angles, internal steric clashes, aromatic and double-bond planarity, ring geometry and conformational strain; (iii) the interactions between the ligand and other components of the complex, including the minimum distance between the ligand and the protein, steric overlap with the protein and interactions with cofactors. In our opinion, adding PoseBuster to our MolProbity analysis provides a comprehensive evaluation of the physical validity of biologics and ligands. We hope that the reasoning reported here and the additions to the main manuscript address the reviewer’s concerns.

Reviewer_gfhNOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes an inference-time correction method for AF3-style biomolecular diffusion models. Two projection operators modify the denoised coordinate estimates during the final, low-noise portion of sampling: one reduces inter-chain steric clashes, while the other corrects ligand geometry, including bond lengths, angles, internal clashes, planarity, and chirality. The corrections are displacement-capped and require neither retraining nor additional network evaluations. The authors evaluate the method on Boltz-2 and OpenFold-3 across five benchmark sets, with comparisons against the unmodified models, Boltz-2x steering, and post-hoc correction. They report at least one physically valid prediction among five samples for every evaluated target, with largely unchanged aggregate structural accuracy and little additional runtime or memory cost.

Critical strengths

The method requires no retraining and is tested on Boltz-2 and OpenFold-3 across five benchmark sets. The reported gains in the targeted validity checks come with little change in aggregate accuracy or inference cost, which could make the method useful in practice. I also appreciate the comparisons with post-hoc correction and the geometry checks in Appendix G.

Critical weaknesses

1. GSP is central to the motivation but absent from the experiments.

The paper describes Gauss-Seidel Projection (GSP) [1] as trading accuracy for efficiency (lines 93-95) and states that applying it only at inference degrades accuracy (lines 133-135). These claims help motivate the proposed method, yet the experiments never compare against GSP.

The sampling budgets also differ: GSP's main results use two-step sampling, whereas this paper applies corrections during a 200-step trajectory. Without a comparison under matched conditions, differences in accuracy cannot be attributed to the projection method itself.

I understand that the finetuned GSP checkpoints were unavailable. That limits a comparison between the complete models, but it does not explain why the authors did not compare the forward projection operators with frozen pretrained weights. I would expect a comparison using the same base model and sampling schedule, with comparable constraints and correction budgets.

Without it, I cannot tell whether the gain comes from the proposed operators or from applying physical corrections late in a much longer sampling trajectory. Table 2 compares the method with the authors' own post-hoc variants, which does not answer this question. This leaves the paper's claimed advance over its closest methodological predecessor unsupported.

2. The reported 100% validity does not establish the claim made in the paper.

Table 1 uses oracle results over five samples. Table 3 makes the validity definition explicit: a target counts as successful if any of its five samples is valid. A 100% score therefore says that each target has at least one valid candidate. It does not say that all generated structures are valid. Appendix D illustrates the difference: lines 1121-1123 report that only 19 of 20 structures in the diagnostic experiment are clash-free. This is consistent with perfect best-of-five coverage, but not with an unqualified claim of perfect output validity. Section 4 also acknowledges that the operator does not guarantee feasibility.

I also could not determine whether the accuracy and validity columns in Table 1 refer to the same selected structures. If the most accurate candidate differs from the valid candidate, separate oracle scores do not show that one output is both valid and equally accurate. The claim of removing violations "without sacrificing accuracy" needs to be evaluated jointly on the structures that would actually be selected at inference.

Appendix G provides useful checks, but they have narrower scope than the main claim. The MolProbity analysis removes ligands, and the post-relaxation energy comparison measures structures after an additional corrective procedure. Neither establishes comprehensive physical validity of the raw outputs.

I would need to see per-sample validity, the remaining violations by category, and accuracy measured jointly with validity under a specified inference-time selection rule. The current results support improved best-of-five coverage; they do not establish the broader conclusion stated in the paper.

Questions for authors
  1. Can you compare GSP's forward projection with your operators using the same frozen base model and sampling schedule, with comparable constraints and correction budgets? If not, what prevents this comparison independently of the unavailable finetuned checkpoint?

  2. How is the sample selected for each column of Table 1? Please report per-sample validity and joint accuracy and validity under a practical selection rule, such as selecting the highest-confidence valid candidate.

  3. What exactly was changed in the planarity evaluator mentioned in Appendix E.1, and how does it affect the pass rates? Please provide the evaluator modification and a breakdown of residual violations across all generated samples.

4 comments
AuthorsOpenReview ↗

Evaluation metric and GSP Comparison

How is the sample selected for each column of Table 1? Please report per-sample validity and joint accuracy and validity under a practical selection rule, such as selecting the highest-confidence valid candidate.

We thank the reviewer for the careful and constructive assessment. We agree that best-of-five oracle validity is not the most informative metric for assessing physical validity. We would like to clarify that Table 1 was constructed using the same evaluation scripts as used by Boltz and by GSP and hence, our aim was to report the same way as previously published methods, including metrics used. Nevertheless, we agree that consistency with previous work does not eliminate the limitations of oracle evaluation. To address this concern, we have retired the oracle metric and will report the per-sample validity and confidence-selected top-1 validity on the same selected samples in the paper. Moreover, as per the suggestion of the other reviewer, VuH7, we additionally provide an independent evaluation using Posebusters, a widely adopted framework for assessing physical validity.

Can you compare GSP's forward projection with your operators using the same frozen base model and sampling schedule, with comparable constraints and correction budgets? If not, what prevents this comparison independently of the unavailable finetuned checkpoint?

We thank the reviewer for this important suggestion. We have conducted the experiment comparing GSP's inference time projection with our method using pretrained Boltz-2 weights, five diffusion samples per target, 10 recycling steps, 200 diffusion steps, identical inputs and precomputed MSAs, and the same random seed. We followed the constraint schedule, solver iterations and guidance weight implemented in the GSP code and applied their correction with all constraints enabled. GSP projection is as performed in their updated Appendix D post-processing, without fine-tuning: 100 Gauss–Seidel iterations on the final coordinates. Ours runs at each of the last 40 steps.

CASP15

MethodlDDT ↑lDDT-PLI ↑Published eval valid ↑PoseBusters valid ↑Time ↓Memory ↓
Boltz-20.449 / 0.4500.519 / 0.54561.5 / 63.6%35.0 / 25.0%55.4s11.9 GiB
GSP0.447 / 0.4490.520 / 0.544100 / 100%88.3 / 100%59.4s12.1 GiB
Ours0.448 / 0.4500.523 / 0.548100 / 100%100 / 100%56.0s11.9 GiB

CASP16

MethodlDDT ↑lDDT-PLI ↑Published eval valid ↑PoseBusters valid ↑Time ↓Memory ↓
Boltz-20.437 / 0.4370.307 / 0.31753.5 / 53.8%31.1 / 33.3%56.0s11.8 GiB
GSP0.433 / 0.4340.301 / 0.268100 / 100%86.7 / 77.8%62.6s12.1 GiB
Ours0.434 / 0.4320.299 / 0.265100 / 100%100 / 100%56.0s11.8 GiB

PoseBusters Complex

MethodlDDT ↑lDDT-PLI ↑Published eval valid ↑PoseBusters valid ↑Time ↓Memory ↓
Boltz-20.8995 / 0.90370.8066 / 0.808428.3 / 28.0%67.2 / 72.7%71.3s22.2 GiB
GSP0.8986 / 0.90270.8045 / 0.806099.0 / 98.8%98.1 / 98.8%83.9s22.2 GiB
Ours0.8993 / 0.90420.8070 / 0.810799.4 / 99.4%98.6 / 98.8%74.2s22.2 GiB

Notes: Accuracy and validity values are reported as per-sample / top-1. Per-sample averages across five generated structures per target; top-1 evaluates the highest-confidence prediction. Bold indicates the best value between GSP and Ours, including ties. Time is the mean structure-prediction runtime per target for five samples (seconds), excluding process start-up, input processing, and checkpoint loading. Memory is mean peak reserved GPU memory (GiB).

We evaluate both methods on CASP15, CASP16, and PoseBusters Complex, reporting structural accuracy (lDDT and lDDT-PLI), physical validity, inference time, and GPU memory using Boltz’s evaluation scripts. We additionally perform an independent evaluation using PoseBusters, a more comprehensive framework for assessing physical validity. While GSP and our method both achieve 100% physical validity scores on CASP15 and 16 using boltz evaluation scheme (Published eval valid), our method achieves 100% per-sample PoseBusters validity on these datasets, compared with 88.3% and 86.7% for GSP, respectively. On PoseBusters Complex, our method also matches per-sample validity (98.6% versus 98.1%), while maintaining comparable structural accuracy. With frozen weights and a matched 200-step schedule, GSP’s forward projection is a strong baseline. Our in-loop projection matches it there and passes more of the independent PoseBusters checks on the CASP ligand targets, at lower projection cost.

AuthorsOpenReview ↗

Fig 8 diagnostic experiment and Planarity evaluator correction

lines 1121-1123 report that only 19 of 20 structures in the diagnostic experiment are clash-free. This is consistent with perfect best-of-five coverage, but not with an unqualified claim of perfect output validity.

We thank the reviewer for pointing to this passage; our wording there could be clearer. The numbers in that paragraph are computed on the sampler iterate xₜ, which is the quantity Figure 8 tracks over steps 140–199, and not on the structures returned by the sampler and scored by the evaluator. As the reviewer points out, it is a diagnostic experiment. The closing sentence of that paragraph, "The figure is meant to show when corrections are retained, not to measure validity", was intended to convey this, but it does not state which coordinates the numbers refer to. We will revise the paragraph to say so explicitly.

What exactly was changed in the planarity evaluator mentioned in Appendix E.1, and how does it affect the pass rates? Please provide the evaluator modification and a breakdown of residual violations across all generated samples.

We thank the reviewer for requesting this clarification. The modification in Appendix E.1 corrects an inverted condition in the five-membered-ring planarity evaluator (check_ligand_flatness) in https://github.com/jwohlwend/boltz/blob/main/scripts/eval/physcialsim_metrics.py#L120

Incorrect (Boltz): np.all(ring_5_dists <= 0.25, axis=-1)

Corrected (Ours): np.any(ring_5_dists >= 0.25, axis=-1)

The incorrect condition flags geometrically correct, planar rings as violations, whereas the corrected condition flags rings with at least one atom deviating by 0.25 Å or more from the best-fit plane. We quantified the effect across all generated samples using the unmodified published evaluator as the reference. Every five-membered ring examined was planar (maximum deviation 0.009 Å), yet the incorrect condition falsely flagged samples.

DatasetMethodCorrect evaluator (%)Incorrect evaluator (%)Difference (pp)
CASP15 (66)Boltz-261.5 / 63.661.5 / 63.60 / 0
Boltz-2x99.7 / 100.099.7 / 100.00 / 0
GSP100.0 / 100.0100.0 / 100.00 / 0
Ours100.0 / 100.0100.0 / 100.00 / 0
CASP16 (52)Boltz-253.5 / 53.853.5 / 53.80 / 0
Boltz-2x100.0 / 100.096.2 / 96.2+3.8 / +3.8
GSP100.0 / 100.096.2 / 96.2+3.8 / +3.8
Ours100.0 / 100.096.2 / 96.2+3.8 / +3.8
PoseBusters Complex (161)Boltz-228.3 / 28.027.3 / 27.3+1.0 / +0.6
Boltz-2x99.3 / 99.496.8 / 96.9+2.5 / +2.5
GSP99.0 / 98.896.5 / 96.3+2.5 / +2.5
Ours99.4 / 99.496.9 / 96.9+2.5 / +2.5

Notes: All validity values are per-sample / confidence-selected top-1. Difference is correct - incorrect evaluator, in % points.

AuthorsOpenReview ↗

Molprobity and post-relaxation energy comparison

The MolProbity analysis removes ligands...

We thank the reviewer for this observation and agree that a comprehensive assessment of physical validity should include both ligand geometry and protein–ligand interactions. In our original submission, we used MolProbity to specifically assess the structural quality of the biological macromolecules in our predicted complexes. MolProbity is primarily designed for macromolecular structure validation and provides limited coverage of small-molecule ligand geometry and stereochemistry. To address the reviewer's concern, we have extended our evaluation to include PoseBusters and results can be found in our response above. PoseBusters provides complementary validation across three key dimensions: (i) chemical identity and stereochemical correctness, including molecular connectivity, tetrahedral chirality, and double-bond stereochemistry relative to the intended ligand; (ii) intramolecular ligand geometry, including bond lengths, bond angles, internal steric clashes, aromatic-ring and double-bond planarity, ring conformations, and molecular strain; and (iii) intermolecular physical plausibility, including protein–ligand steric clashes, van der Waals overlap, and interactions with other components of the complex. The addition of PoseBuster to the already present MolProbity analysis offers a complete evaluation of the physical validity of biologics and ligands.

the post-relaxation energy comparison measures structures after an additional corrective procedure. Neither establishes comprehensive physical validity of the raw outputs.

We thank the reviewer for this observation and agree that post-relaxation energies alone would not establish the physical validity of the raw outputs. The post-relaxation comparison, and the alpha-complex neighbour counts analysis, had a different purpose. They were not designed to measure physical validity, but to test a possible failure mode of our approach: steric clashes could in principle be removed simply by expanding the structure, at the expense of compactness and local packing. To investigate this possibility, we performed complementary energy and alpha-complex analyses, comparing our projected structures against the original Boltz-2 predictions. After an identical short relaxation, the projected and base structures reach the same energy (median 145.5 vs. 145.1 kJ/mol per residue), and the alpha-complex neighbour counts are unchanged (Table 7b). This indicates that the projection resolves the severe contacts without moving the structure away from the local energy minimum that the base model reaches, and without artificial expansion. These analyses are therefore complementary to, rather than a substitute for, a direct evaluation of physical validity. The direct evaluation of physical validity is made on the raw, unrelaxed structures: with the published evaluation script, with MolProbity for the protein chains, and now independently with PoseBusters for the ligands (see our response above).

We sincerely thank the reviewer for prompting these analyses as they have materially strengthened the paper. We appreciate the opportunity to address these concerns and are keen to engage in further discussion.

We thank the reviewer again for their comments. As the discussion period closes tomorrow, we wanted to check whether our response have sufficiently addressed concerns raised. If any remain unresolved, we would be glad to address them before the deadline.

Comments on the paper

1 comment

We would like to thank the reviewers for their time and their suggestions for improving the manuscript. We have uploaded a revised version that incorporates the changes requested by the reviewers. We would like to point out that the main text does not yet include the updated Table 1 with per-sample / top-1 scores and the GSP comparison, and still retains the best-of-five oracle validity table, as we are still running an updated PoseBusters evaluation for Boltz-2x and our OpenFold-3 implementation, and evaluating GSP on the remaining datasets (PoseBusters Monomer and Test). We will retire the best-of-five oracle results in Table 1 and replace them with the per-sample / top-1 scores and the GSP comparison in the camera-ready version; in the meantime, these results are included in Appendix F.

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

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