acceptodds
Under review as a conference paper at ICLR 2027

RiMES: Riemannian Flow Matching with Equivariance and Stereochemical Regularization for Antibody CDR Co-Design

Abstract

Antibody complementarity-determining region (CDR) co-design requires compatible sequence and structural predictions under a specified framework and antigen context. We present **RiMES** (Riemannian flow Matching with Equivariance and Stereochemical regularization), an iterative full-atom co-design model that couples geometric message passing to Riemannian flow matching on residue frames. A local-frame velocity head supplies translation corrections between refinement rounds, while a differentiable rotamer-compatibility term and a soft C overlap penalty connect sequence prediction to local geometry. The flow objective uses mixed prediction- and noise-based starts with detached targets and shared encoder representations. Under known-interface conditioning, we report PLM-free amino-acid recovery of 53.5% on RAbD CDR-H3, 77.1% on joint six-CDR design, and 47.9% on the cluster-date-ordered SAbDab evaluation. Component ablations support the mixed-start configuration and intermediate flow feedback, while exposing trade-offs between recovery and local structural accuracy. We separately evaluate parent-conditioned redesign using protein language model embeddings. Masking the designed CDR before PLM encoding and retraining removes the parent-conditioned recovery advantage, demonstrating the importance of distinguishing the two input regimes. Together, these results support flow-assisted conditional CDR co-design, with all-atom packing, antigen-relative placement, and experimental function remaining important limitations.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Antibody design, protein design, Riemannian flow matching, equivariant generative modeling, geometric deep learning, sequence–structure co-design

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_tW78OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

This paper proposes RiMES, an iterative refinement framework for conditional CDR co-design. Given the native framework region, antigen, CDR length, and a reference-derived epitope, it jointly predicts CDR sequence and structure. The method uses a dual-stream equivariant EGNN to iteratively refine all-atom predictions over three rounds. On this backbone it adds three components. The first is a Riemannian flow-matching auxiliary objective on residue frames that provides small translation corrections between rounds. The second is a differentiable χ1 rotamer compatibility loss that couples sequence probabilities with side-chain geometry, together with collision and framework consistency penalties. The third is an optional adapter for parent-conditioned redesign that injects ESM-2-3B embeddings. The paper reports the following main results. For sequence recovery, AAR is 53.5% on RAbD CDR-H3 (dyMEAN 43.1%), 77.1% for six-CDR joint design, and 47.9% on the SAbDab temporal split, while structural metrics are mixed or unfavorable. A masked-input control shows that the parent-conditioned recovery rate of 72.9% drops to 42.4% when ESM cannot see CDR tokens. Ten trastuzumab CDR-H3 redesigns all express and bind HER2, with a best affinity of 1.46 nM versus 0.98 nM for the parent.

Critical strengths
  1. Transparent reporting with proactive disclosure of unfavorable evidence. The appendix presents results unfavorable to the paper, including AbLang2 scoring generated variants worse than the parent (Table 10) and no rank correlation between the Rosetta ΔΔG proxy and ten measured affinities (ρ = +0.05, Appendix C.6). It also explicitly identifies which analyses could not be reconciled.

  2. The input-masking control is a valuable negative result. After masking CDR tokens before ESM encoding and retraining, AAR drops from 0.729 to 0.424, below the PLM-free model (Appendix E.1). The parent-conditioned gain therefore mainly comes from information leakage through bidirectional ESM embeddings of native CDR context rather than from the architecture itself. This finding is relevant to all antibody design work that uses PLM features, and separating the two mechanisms is the right evaluation.

  3. The baseline audit and wet-lab panel exceed common practice. Appendix K verifies which coordinates each baseline actually writes, including who grafts native frameworks and who uses templates or AF2-enhanced antigens at inference, and annotates these asymmetries in all result tables. Ten designs were expressed, purified, and assayed, with the parent measured under the same protocol (Appendix C.6).

Critical weaknesses
  1. Main comparisons cannot be verified from the manuscript itself. Appendix D reports a paired advantage over FlowDesign of +0.096, whereas Table 1 shows +0.210. The authors' own accounting implies that the FlowDesign value in the main table should be about 0.42 rather than the reported 0.325. Appendix E.2 shows that the multi-CDR “All” rows for four of five baselines do not match the main table. These are not reviewer inferences. The authors state that the correspondence “still cannot be reconciled” and provide no code to resolve it (Appendix Q). A paper whose central comparison cannot be reconstructed from its own record does not meet the evidence threshold for acceptance.

  2. Flow matching never actually generates any structure in this paper. The ODE integrator is implemented but disabled in all reported experiments (Appendix M.10). The flow appears only as an auxiliary training loss and two translation fine-tunes of magnitude 0.05. The only comparison that could establish its value, the no-flow comparison in Appendix G, is described by the authors themselves as having an unclear configuration, so its 13.7 AAR-point difference cannot be attributed. What remains is essentially dyMEAN-style iterative refinement plus rotamer and collision regularization.

  3. The structure channel is worse than the 2023 baselines it builds on. CDR-H3 RMSD is 1.762 on RAbD versus 1.573 for dyMEAN, and 2.407 versus 1.108 for FlowDesign on the temporal split (Table 1). Framework placement error in the antigen frame is 28 Å versus 24–25 Å for baselines (Appendix H). Bond-length validity is 0.155–0.182 (Table 15). All-antibody–antigen clashes are two orders of magnitude higher than native (307 versus 1.6, Table 20). A model with sequence gains accompanied by this level of geometric quality is difficult to use in practice, and the main text does not diagnose this degradation.

  4. The wet-lab panel tests a mechanism mismatched to the architectural contribution. The ten measured designs come from the parent-conditioned setting, whose own control attributes recovery to ESM leakage. The strongest binder is a double-residue edit with 1.5-fold worse affinity than the parent. The architectural contribution itself, PLM-free RiMES, has no experimental test.

Questions for authors
  1. Please provide the per-target evaluation records and scripts that produce Tables 1, 7, and 9, and explain the FlowDesign discrepancy, namely 0.325 versus the approximately 0.42 implied by your own accounting. If the main table cannot be regenerated from a public manifest, will you regenerate it?
  2. What exactly does the “no-flow” configuration in Appendix G remove? Can you run a strictly matched version with λf=λc=0, no fine-tuning, identical data and seeds, and at least two seeds?
  3. Is the 0.155–0.182 bond-length validity a model property or an artifact of the Kabsch placement step in Appendix P?
  4. What exactly are the “shadow paratope coordinates” used for final placement, and how much of the reported DockQ comes from this placement step rather than from generation itself?
7 comments
AuthorsOpenReview ↗

Response to reviewer tW78(Q1)

We thank the reviewer for the detailed assessment and concrete diagnostic requests. We have revised the manuscript to make our design choices, completed controls, source coverage and application scope explicit. Our responses below distinguish the evidence supporting the design from the limitations that remain.

Question 1: Can we provide records and scripts for Tables 1, 7 and 9, explain FlowDesign AAR 0.325 versus approximately 0.42, and regenerate unverifiable rows?

Response:

We agree that the central comparisons need an executable evaluation record. We have supplied metric_code/cal_metrics_all.py, its local helpers, dependencies, source hashes, a runnable coordinate example, per-target coverage and native/designed CDR sequences.

Anonymous evaluation code https://anonymous.4open.science/r/RIMES-1711/cal_metrics_all.py

We respectfully clarify a separate issue. The main table and appendix estimate different quantities, as stated in the appendix: main-table AAR uses the full 60-target by 40-attempt budget, with documented failed/unreadable generations assigned zero; paired appendix analyses condition on valid generations on shared targets. A higher valid-only AAR is therefore not, by itself, a contradiction. The metric calculator exports valid-only means; full-budget correction additionally requires an attempted/failure manifest. This explains why the estimators can differ; the exact original FlowDesign 0.325 remains unreconstructed from the available archive.

Loop weighting is a separate source of multi-CDR differences. Recovered pooled/equal-loop AAR is 0.478255/0.521036 for dyMEAN and 0.251235/0.271061 for dyAb; AbX's reported 0.632 matches recovered raw pooling. We therefore added a uniform residue-pooled comparison on 44 complete shared targets at the same relaxed phase: archived no-adapter 77.962%, FlowDesign 65.742%, AbX 63.680%, dyMEAN 48.670% and dyAb 25.591%. The first-minus-FlowDesign paired difference is +12.22 points, CI [+10.58,+13.91]. This supports the ordering among these recovered output sets under one evaluator, with the archived model's input provenance explicitly unverified.

The revised manuscript retains the headline cells as reported, adds the reproducible supplementary analysis, and removes reliance on unreconstructed rows for certified comparative margins or verified PLM-free state-of-the-art claims.

Action:

Completed: We added the appendix sections "Aggregation and original-table traceability" and "Additional Residue-Pooled Multi-CDR Evaluation," clarified the main-table caption and paired-comparison caption, and supplied evaluation code and per-target records.

AuthorsOpenReview ↗

Response to reviewer tW78(Q2, Q3)

Question 2: What does Appendix G remove, and can we provide a strict no-flow comparison with zero flow/consistency losses, no feedback or fine-tuning, and at least two matched seeds?

Response:

Thank you for specifying the control. We agree that historical Appendix G cannot isolate flow. The author-identified checkpoints/rabd_noadapter_noflow configuration disables use_riemannian_flow, use_flow_iter and use_equivariant_adapter together, while retaining use_plm=True through linear projection and clash/rotamer weights 0.5/0.1. Its full reference is the parent-conditioned model. We now label this as combined adapter-plus-flow removal, distinct from the Euclidean-flow replacement. The historical source checkpoint/configuration was not independently recovered in the audit.

Rotational supervision and translation refinement serve complementary purposes. Although rotational velocities are not integrated during inference, their supervision provides geometric learning signals through the shared EGNN representations. Since hidden states are not detached, rotational-loss gradients also influence representations used for translation and sequence prediction. During inference, iterative translation feedback performs coordinate refinement, with optional ODE integration disabled. The absence of ODE sampling therefore does not make the flow objective inactive: its auxiliary supervision is a deliberate part of how our shared co-design model is trained.

Unlike simple residual correction, which directly learns coordinate updates, our method combines iterative refinement with flow-based geometric supervision. Thus, the evaluated approach is more accurately described as flow-supervised iterative refinement, rather than explicit rotational flow integration.

The reported model and newly evaluated no-flow runs give the following descriptive comparison:

\text{Model / seed} & \text{AAR (\\%)} & \text{CAAR (\\%)} & \text{H3 RMSD (A)} \\\\ \hline \text{Reported full model} & 53.50 & 33.40 & 1.762 \\\\ \text{New no-flow / 1} & 38.65 & 24.22 & 1.824 \\\\ \text{New no-flow / 2} & 39.64 & 25.29 & 1.818 \\\\ \end{array}$$ The reported model has higher AAR and CAAR and lower H3 RMSD than both new no-flow runs. This is a descriptive comparison across different input/checkpoint-selection protocols; it does not isolate flow's contribution. The separate matched two-seed comparison is reported in the appendix, while the dedicated rotational-loss control in the appendix tests the auxiliary-supervision mechanism directly. In that single-seed control, removing rotational supervision worsens framework-fitted refolding scRMSD by +0.224 Angstrom, 95% CI [+0.036,+0.412]. This provides specific evidence for the training role of rotational supervision, with the local-geometry trade-offs reported alongside it. **Action:** **Completed:** We clarified the historical Appendix G intervention and added the strict two-seed comparison, residual/rotational/feedback controls and evaluation records to "Independent Consistency and Matched Component Controls." This response uses the reported-model reference consistently, while keeping the descriptive summary separate from matched attribution. The Method and ablation discussion now distinguish auxiliary training supervision, inference correction and the three ablation interventions. ### Question 3: Is low bond-length validity a property of our predictions or an artifact of the final Kabsch placement? **Response:** We have tested this directly. On the same forward pass for one predetermined sample on each of all 60 targets, bond validity is 0.14235 before and after placement, versus native 0.99333 at 0.05-Angstrom tolerance. A global rigid transform preserves internal distances, so Kabsch placement cannot explain this low validity. The internal error precedes placement and remains a limitation of our predictions. This diagnostic also clarifies the scope of our physical losses: local $\chi_1$ compatibility and $\mathrm{C}_{\alpha}$ clash regularization encourage particular geometric properties; they do not enforce covalent bond lengths or certify all-atom validity. We defend their targeted roles using the corresponding measurements, without interpreting them as a complete physical model. This audit diagnoses the new checkpoint's mechanism rather than reconstructing every historical export row. We therefore assess the benefit of each regularizer through its targeted property, while treating the poor bond validity as a separate, unresolved constraint on the generated coordinates. **Action:** **Completed:** We added the same-forward before/after bond audit, native control, tolerance and checkpoint scope to "Shadow coordinates and the placement audit." The physical-quality discussion now distinguishes targeted regularization from bond validity, and the attachment includes all 60 paired records.
AuthorsOpenReview ↗

Response to reviewer tW78 (Q4)

Question 4: What are the shadow paratope coordinates, and how much does final placement affect DockQ?

Response:

We appreciate the request to make this mechanism explicit. The shadow paratope is a learned, model-predicted copy in the antigen-context stream, initialized around the antigen center and refined by message passing. Kabsch aligns the predicted antibody paratope to these predicted shadow coordinates and moves the whole antibody. It solves alignment between two predictions; its fitting target is not native paratope coordinates. The reference-derived epitope remains an explicit conditioning assumption.

Predicted placement is therefore part of our design: the antigen-context stream supplies a learned target pose, and the rigid alignment transfers that prediction to the antibody. It does not replace generation with native-framework grafting or a native-paratope fit. Its accuracy still requires measurement, so we added the requested same-forward audit on all 60 targets.

Antibody-antigen DockQ changes from 0.00278 to 0.14776 after placement: paired difference +0.14498, 95% CI [+0.11084,+0.18237]. Global DockQ changes from 0.24915 to 0.34554 and also includes H-L interfaces. Before-placement coordinates are in an unplaced internal frame, so the comparison establishes placement's importance within our pipeline; the nonlinear score does not permit an additive percentage attribution between generation and placement. The final antigen-interface scores also show that placement remains a substantial limitation. Because the target pose is learned, evaluating our conditional generation pipeline includes this predicted placement stage. The same-forward audit quantifies both its contribution and the remaining placement error.

Action:

Completed: We defined the predicted shadow-coordinate pathway in the Inference Pipeline and added the before/after interface-specific DockQ audit, epitope assumption and internal-frame interpretation to the appendix. regenerate_placement.py recomputes the means and intervals from the 60 supplied records, interface mappings and source hashes.

Reviewer_cnELOpenReview ↗
Rating
2
Confidence
1(−2)
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes RiMES, an antibody CDR sequence–structure co-design framework that integrates Riemannian Flow Matching with iterative equivariant graph-based refinement. The method introduces residue-frame flow supervision and intermediate translation corrections, together with stereochemical regularization to encourage sequence–structure compatibility. Experiments on RAbD and SAbDab benchmarks demonstrate improvements in amino-acid recovery, while structural accuracy remains mixed. The paper also distinguishes PLM-free design from parent-conditioned redesign and investigates the impact of potential information leakage from PLM inputs.

Overall, the motivation is clear and the proposed methods are well aligned with it. However, I believe the current experimental evidence is insufficient to fully establish the effectiveness of the proposed components, particularly in improving structural quality and sequence–structure compatibility. I would consider raising my score if the authors provide additional experimental evidence to better support these contributions.

Critical strengths

S1. Clear motivation and well-aligned methodology. The paper presents a clear motivation, and the proposed components are logically aligned to improve structural refinement and sequence–structure compatibility.

S2. Extensive experimental evaluation. The paper evaluates multiple CDR design tasks and reports a broad range of sequence and structural metrics. The ablation studies provide useful insights into the contributions of individual components, with notable improvements in sequence recovery.

Critical weaknesses

W1. The proposed method aims to improve structural refinement and sequence–structure compatibility, but its main gains are in amino-acid recovery, while several structural metrics remain inferior to existing baselines. The paper also lacks direct evaluation of sequence–structure consistency. Refolding consistency or inverse folding experiments could provide stronger evidence.

W2.In the PLM-free setting, adding Rotamer Loss improves AAR (0.494 → 0.535) but worsens CDR RMSD (1.731 → 1.762). This trade-off raises questions about whether the module consistently improves sequence–structure compatibility.

W3. Although the model learns both rotational and translational velocities, only translation corrections are used during refinement. A comparison with simpler residual coordinate correction would help establish the necessity of Riemannian Flow Matching.

Questions for authors

Please see Weakness

10 comments
AuthorsOpenReview ↗

Response to reviewer cnEL

Thank you for recognizing the motivation of our design and identifying the experiments needed to assess it more directly. We have added independent refolding, matched loss-on/off controls, a direct residual-correction baseline, and two full/no-flow training seeds to the revised manuscript. These tests clarify the contributions of our design and their limits.

Question 1: Can we provide direct sequence-structure consistency evidence, and how does structural quality compare with the controls?

Response:

Thank you for this suggestion. We have added the requested direct test: independent sequence-only refolding. For the saved original Seed 1 cohort, we refolded five predetermined designs for each of all 60 targets, giving 300 designs with no evaluation failures. ESMFold received paired H/L sequences without generated coordinates or structural templates. Generated-versus-refolded CDR scRMSD is 2.153 Angstrom after framework-only fitting and 1.492 after loop self-fitting. This evaluates agreement between our generated sequence and structure independently of native-sequence recovery.

The summary below places the reported full-model recovery and loop-shape results alongside the evaluated controls:

\text{Condition} & \text{AAR (\\%)} & \text{Local RMSD (A)} & \text{Refold scRMSD (A)} \\\\ \hline \text{Full*} & 53.50 & 1.762 & 2.032 \\\\ \text{No rotamer loss} & 40.59 & 1.751 & 1.976 \\\\ \text{Direct residual} & 38.80 & 1.807 & 2.098 \\\\ \text{Strict no-flow} & 38.65 & 1.824 & 2.043 \\\\ \text{Translation-only flow} & 40.71 & 1.760 & 2.256 \\\\ \text{Matched EGNN control} & 39.76 & 1.576 & 1.941 \\\\ \end{array}$$ *The Full row combines the paper-reported AAR/local RMSD with refolding scRMSD. It is a descriptive summary across protocols. The matched full-model baseline is 39.85% AAR, 1.857 Angstrom local RMSD and 2.032 Angstrom refolding scRMSD; this baseline is retained in the appendix and used for all within-study effects and confidence intervals. Our design addresses several distinct properties: native-referenced loop shape, agreement of a designed sequence with its generated structure, and placement in the antigen context. Local RMSD measures the first; framework-fitted refolding scRMSD directly tests the second. The rotational-supervision comparison below supports a specific consistency benefit, while within the matched study, full-minus-EGNN refolding scRMSD is +0.091 Angstrom, CI [-0.112,+0.299], so we do not infer overall structural superiority. The revised manuscript separates these properties and conditioning assumptions. Grafting baselines retain native framework coordinates, whereas our pipeline predicts output antibody geometry and placement. This matters for whole-complex metrics, but does not remove our local loop-shape limitations. Native refolding controls give 2.434 Angstrom against crystal coordinates; that different reference calibrates folding-model error and does not establish designs better than native. Refolding does not validate affinity or antigen placement. **Action:** **Completed:** We added the independent refolding protocol, fixed-sample coverage, control table, fitting definitions and uncertainty to the appendix, "Independent Consistency and Matched Component Controls." The main Metrics and Results sections now distinguish shape, consistency and placement, and the evaluation attachment supplies the records and analysis code.
AuthorsOpenReview ↗

Response to reviewer cnEL(Q2)

Question 2: Why does adding rotamer loss improve reported AAR while slightly worsening CDR RMSD, and does it improve compatibility consistently?

Response:

We appreciate this question. Our χ1\chi_1 loss couples sequence probabilities to local sidechain geometry; its intended benefit is more specific than minimizing native-referenced backbone RMSD. The reported AAR change 0.494 to 0.535 with RMSD 1.731 to 1.762 Angstrom is a recovery/backbone trade-off. Cα\mathrm{C}_{\alpha} RMSD alone cannot determine whether sidechains are more compatible with the predicted sequence.

The existing PLM-augmented sidechain ablation directly addresses that intended role: adding rotamer loss reduces χ1\chi_1 MAE from 76.4 to 63.9 degrees and CDR-antigen all-atom clashes from 19.00 to 8.89. This is evidence for local sidechain regularization within that input setting; it does not establish the same effect in every regime.

The matched PLM-free loss-on/off experiment provides a complementary check. Adding the loss improves the corrected broad Rama proxy from 0.49891 to 0.63505: +13.61 percentage points, 95% CI [+10.04,+17.03]. This is a backbone angular proxy, not direct χ1\chi_1 accuracy. Bond validity worsens, and no refolding benefit is established. We therefore confirm the component as a targeted local regularizer, while making its measured trade-offs explicit. The torsion convention was checked against Bio.PDB.

Action:

Completed: We added the matched rotamer-loss results and confidence interval to the appendix, "Rotamer-loss scope," and revised the main Results and ablation interpretation. The paper now separates sidechain evidence, broad angular plausibility, backbone fidelity, and refolding consistency, rather than claiming that the loss uniformly improves them.

AuthorsOpenReview ↗

Response to reviewer cnEL(Q3)

Question 3: Why supervise rotational velocities when refinement uses only translation corrections, and how does our design compare with simple residual correction?

Response:

Thank you for this question. Rotational supervision and translation refinement serve complementary purposes. Although rotational velocities are not integrated during inference, their supervision provides geometric learning signals through the shared EGNN representations. Since hidden states are not detached, rotational-loss gradients also influence representations used for translation and sequence prediction. During inference, iterative translation feedback performs coordinate refinement, with optional ODE integration disabled.

Unlike simple residual correction, which directly learns coordinate updates, our method combines iterative refinement with flow-based geometric supervision. Thus, the evaluated approach is more accurately described as flow-supervised iterative refinement, rather than explicit rotational flow integration.

The reported results and newly evaluated no-flow runs show:

\text{Model / seed} & \text{AAR (\\%)} & \text{CAAR (\\%)} & \text{H3 RMSD (A)} \\\\ \hline \text{Reported full model} & 53.50 & 33.40 & 1.762 \\\\ \text{New no-flow / 1} & 38.65 & 24.22 & 1.824 \\\\ \text{New no-flow / 2} & 39.64 & 25.29 & 1.818 \\\\ \end{array}$$ The reported full model has higher AAR and CAAR and lower H3 RMSD than both new no-flow runs. This is a descriptive comparison across different input/checkpoint-selection protocols; it does not isolate flow's contribution. The separate matched two-seed comparison is reported in the appendix, while the dedicated rotational-loss control below tests the auxiliary-supervision mechanism directly. To address the reviewer's proposed alternative directly, we implemented a residual-displacement baseline matching the invariant inputs, head capacity, correction locations and refinement rounds. The evidence for rotational supervision comes from its dedicated ablation: removing the rotational-velocity loss worsens framework-fitted refolding scRMSD from 2.032 to 2.256 Angstrom, a +0.224 Angstrom difference, 95% CI [+0.036,+0.412], across 300 designs per condition on 60 targets. Local native-referenced RMSD and bond validity favor removal. Thus, our evidence supports a specific benefit to sequence-structure consistency from auxiliary rotational supervision, without requiring rotational integration or claiming uniform geometric improvement. **Action:** **Completed:** We added the matched two-seed comparison, direct residual baseline, rotational-supervision ablation and feedback control to the manuscript. The Method and appendix now distinguish training supervision from inference correction and report the configurations, uncertainty and structural trade-offs explicitly.
Reviewer_c3nSOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This work introduces RiMES, an iterative full‑atom co‑design model for antibody CDR co‑design built upon Riemannian flow matching over residue‑level SE(3) local frames, targeting joint sequence‑structure prediction of CDRs given fixed antibody frameworks, antigen context and CDR lengths.

RiMES couples multi‑channel equivariant EGNN message‑passing with an SE(3)‑velocity head for Riemannian flow matching. It uses mixed starting distributions (half perturbed EGNN prediction‑based starts, half Haar‑noise starts), detached flow targets, differentiable Dunbrack‑rotamer‑based χ₁ stereochemical regularization and soft Cα clash penalties to link sequence predictions and 3D geometry

Critical strengths
  1. The work unifies iterative equivariant full‑atom refinement, SE(3) Riemannian flow‑matching on residue local frames, and differentiable stereochemical regularizers (rotamer compatibility, steric clash penalty) inside one end‑to‑end model.

  2. The authors clearly distinguish PLM‑free de‑novo‑like CDR co‑design versus parent‑conditioned variant redesign, supported by a key control retraining where CDR tokens are masked before PLM encoding to isolate parent‑sequence information contribution.

Critical weaknesses
  1. While sequence‑recovery metrics improve, the model exhibits meaningful antigen‑frame placement error; CDR‑self‑fitted RMSD only evaluates local loop shape and hides mis‑placement relative to antigen. Computational interface‑energy proxies show zero correlation with measured experimental affinity in their small assay panel, meaning in‑silico scoring cannot reliably select high‑affinity candidates.

2.For multi‑CDR joint design the aggregation procedure for headline aggregate AAR is unresolved; baseline per‑loop averages diverge from reported summary numbers, which complicates direct comparison against prior work. The “no‑flow” ablation cannot fully isolate flow‑matching’s unique contribution, as multiple components change simultaneously.

Questions for authors

In the multi‑CDR setting, can you explicitly clarify the exact aggregation rule used to compute the headline aggregate AAR? Why do per‑loop unweighted means for several baselines diverge from the main‑table multi‑CDR results, and does this alter comparative conclusions against competing methods?

4 comments
AuthorsOpenReview ↗

Response to reviewer c3nS (Q3)

Question 3: Does the no-flow ablation isolate the contribution of flow matching?

Response:

Thank you for raising the attribution question. Our flow module is intended to provide residue-frame geometric supervision and guide iterative refinement. Its rotational targets train the shared representations, while intermediate translation feedback updates coordinates. This auxiliary role is a deliberate part of our design and does not require a separate ODE sampler at inference.

We agree that Appendix G alone cannot isolate the contribution of flow: its historical control removes the equivariant adapter, flow supervision and flow feedback together, while retaining PLM inputs. We therefore added a strict matched PLM-free control. Both conditions retain the same backbone and head architecture, data, optimizer, training seed, 200-epoch budget, checkpoint criterion, and rotamer/clash regularization. The control sets λf=λc=0\lambda_f=\lambda_c=0 and disables flow feedback. This removes the adapter and physical-regularizer confounds when testing flow supervision and feedback.

To test this role beyond sequence recovery, we also examine refolding consistency. In the single-seed rotational-loss control, removing rotational-velocity supervision worsens framework-fitted refolding scRMSD from 2.032 to 2.256 Angstrom: removal-minus-full +0.224 Angstrom, paired target-bootstrap 95% CI [+0.036,+0.412], using 300 refolded designs per condition across 60 targets. This provides specific support for the intended auxiliary-supervision role of our design. Local native-referenced RMSD and bond validity favor the ablation, so we interpret the benefit specifically as improved refolding consistency in this control.

We also included a parameter-matched direct residual-correction baseline. The full model's AAR difference is +1.05 percentage points, CI [-0.67,+2.74]. Together, these controls allow a more precise assessment than the original combined ablation and help identify which aspects of our design contribute to recovery and sequence-structure consistency.

Matched two-seed results:

For the strict matched comparison of flow supervision and feedback, full-minus-no-flow AAR is +1.19 and +0.66 percentage points for Seeds 1 and 2; mean +0.93 points (sample SD across the two differences 0.38), paired target-bootstrap 95% CI [-0.27,+2.13]. Recovery is higher for the full model in both runs, while the interval includes zero. The new comparison addresses the original adapter/regularizer confound. Structural outcomes remain mixed: refolding and DockQ differences are inconclusive, and no-flow has better Rama and bond validity. We therefore support a specific auxiliary-supervision role without claiming necessity or uniform improvement. Intervals resample paired targets conditional on these two trained seeds. Other component controls remain single-seed. This study has a separate input/selection protocol from the saved ESM-enabled runs.

Action:

Completed: We added the strict full/no-flow comparison with two matched seeds, the residual-correction baseline, and the rotational-supervision and feedback controls, with configurations and evaluation records supplied.

For revision: We state exactly what each ablation removes and foreground the component-specific evidence. We describe the supported role of flow as auxiliary geometric supervision coupled to refinement, with the limits of the recovery and structural comparisons made explicit.

AuthorsOpenReview ↗

Response to reviewer c3nS(Q4)

Question 4: Can the interface-energy proxy reliably select high-affinity candidates, and what does the wet-lab panel establish?

Response:

Thank you for highlighting the distinction between computational scoring and measured affinity. We agree that the current panel does not establish the interface-energy proxy as a reliable affinity ranker. We would, however, like to clarify the scope of our contribution: our model jointly designs sequence and structure, and the energy proxy is one computational assessment of the resulting candidates. Its ranking performance should be considered alongside the separate evidence for generated-design function.

Our experimental application is deliberately parent-conditioned hit-to-lead redesign around a characterized binder, where preserving binding while exploring CDR variants is a relevant objective. In the reported HER2 panel, all 10 selected designs expressed and retained binding. The strongest tested design has affinity 1.46 nM compared with 0.98 nM for the parent. We interpret this as retained nanomolar binding for that design, without claiming improved affinity. These measurements provide application-specific evidence that our workflow can propose functional variants; this conclusion does not depend on the energy proxy ranking their affinities correctly.

The use of parent-sequence context is consistent with this stated redesign setting. This is why we distinguish parent-conditioned evaluation from PLM-free co-design and include the masked-input control to quantify the contribution of native context. The wet-lab results support the parent-conditioned application; they do not experimentally validate the PLM-free architecture or establish a general success rate beyond the selected panel.

We therefore believe that the useful experimental outcome is the expression and retained binding of the tested redesigns, while the observed lack of affinity-ranking correlation is an important limitation of the proxy. We present both points more clearly so that computational plausibility, functional retention and affinity improvement are not conflated.

Action:

Completed: We clarified the distinct roles of joint co-design, the computational energy proxy and the reported binding assays, and identified the parent-conditioned scope of the panel.

For revision: We report the proxy as an interface-energy assessment, present the expression/binding outcomes with the parent comparison, and state the panel-selection and PLM-setting limits explicitly. We keep affinity-ranking and affinity-improvement claims within the experimental evidence.

Thanks for the detailed reponse.

We sincerely thank the reviewer for carefully considering our rebuttal and for their willingness to raise the score. We greatly appreciate your constructive feedback and thoughtful reassessment of our work.

We remain open to further discussion and would be happy to provide additional clarifications or evidence to address any remaining concerns that may help inform your final assessment. Thank you again for your time and consideration.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.