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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
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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.
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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.
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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
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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.
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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.
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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.
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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
- 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?
- 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?
- Is the 0.155–0.182 bond-length validity a model property or an artifact of the Kabsch placement step in Appendix P?
- 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
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.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.
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.