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Paper summary
This paper introduces SP-FMAG, a framework for antibody CDR sequence–structure co-design that replaces linear positional interpolation with frequency-dependent flow-matching paths. CDR deformation relative to the chord connecting its framework anchors is expressed in a fixed-end sine basis, and higher-frequency modes receive delayed interpolation clocks. The architecture, positional source distribution, and sequence and orientation paths remain unchanged. On the standard SAbDab benchmark, the method reduces CDR-H3 RMSD from 3.313 Å to 2.958 Å and increases Rosetta binding-energy improvement rate from 23.8% to 35.7% relative to a matched linear-flow model. Additional experiments examine spectral strength, reversed ordering, reduced sampling budgets, and local antibody optimization.
Critical strengths
1、The matched linear baseline, reversed-ordering experiment, and spectral-strength ablation provide useful evidence beyond comparisons against previously published methods. The appendix also reports mixed results across CDR types rather than presenting the improvement as universal.
2、The complex-level paired bootstrap is preferable to treating individual generated samples as independent observations. The reported H3 structural improvement is encouraging and warrants further investigation.
Critical weaknesses
1、The experiments do not isolate the contribution of the probability path from frequency-dependent loss reweighting.Changing β modifies both the interpolation clocks in Equation (13) and the modal regression weights in Equations (15)–(16). Consequently, the β ablation changes the training-state distribution and the allocation of regression error across spatial frequencies simultaneously. Reversing the clock ordering also changes this allocation, so the forward-versus-reverse comparison does not resolve the confound. This distinction is particularly relevant to Table 3. With T = 1, Equation (17) reduces to directly returning the predicted endpoint because every clock satisfies Aₖ(0) = 0 and Aₖ(1) = 1. There is therefore no intermediate coarse-to-fine traversal during one-step inference, yet the structural advantage remains. This supports a benefit from the training formulation, but does not establish whether that benefit comes from the proposed path, spectral loss weighting, or their interaction. The central attribution to coarse-to-fine transport is therefore stronger than the available controls justify.
2、The mechanistic illustrations do not faithfully establish smoother generation under the actual source distribution.Figure 1 starts from a deterministic chord, whereas the implemented model starts from independent Gaussian modal coefficients. Under Equation (13), conditioned on a fixed target, the source-noise covariance in mode k is proportional to (1 − Aₖ(t))²I. Delaying high-frequency clocks therefore retains more high-frequency source noise than linear interpolation at the same base time. Delayed introduction of target detail does not, by itself, imply smoother intermediate samples. The tracking diagnostic in Appendix B.3 is also sensitive to the prescribed clock. For example, a trajectory that remains at its source has normalized residual Aₖ(t)² for an individual mode, which can be small simply because that mode is delayed. Figure 5 therefore does not independently demonstrate that the learned dynamics establish meaningful coarse geometry before resolving fine structure. These issues do not invalidate the path construction, but weaken the proposed explanation for its effectiveness.
3、The robustness evidence is limited by a small, grouped test set and a single reported training seed.All main conclusions rely on 19 complexes drawn from five held-out clusters/groups. Appendix B.4 bootstraps complexes, which captures variation across the observed test cases, but does not account for possible dependence within those groups or variation across independently trained models. Appendix D reports seed 2022 without multi-seed results. The confidence interval should therefore not be interpreted as establishing robustness across training runs or independent antigen groups. The model-selection procedure is also unclear. Twenty complexes are reserved for validation, but the manuscript does not specify the criterion used to select β = 4 and the reported checkpoints. Since several β values are compared on the same small benchmark, distinguishing validation-based selection from retrospective test-set selection is important.
4、The comparisons do not adequately establish the advance over existing antibody flow-matching methods.The matched β = 0 model is useful for evaluating the proposed modification within this implementation. However, FlowDesign, which the paper identifies as a prior antibody sequence–structure flow-matching method, is absent from the benchmark comparison. The external comparison instead relies primarily on diffusion methods and RAbD, using numbers imported from MDMAD. As a result, the experiments establish an improvement over the authors’ linear-path implementation more clearly than an advance over existing antibody flow-matching approaches. A protocol-matched comparison with the closest prior method, or a concrete explanation of incompatibilities, is needed to contextualize the practical significance of the contribution.
Questions for authors
1、Can the effects of interpolation clocks and modal loss weights be separated? Were any existing runs performed with spectral clocks and uniform endpoint weights, or with linear clocks and spectral weights? If not, please clarify that the reported ablations evaluate their combined effect rather than the probability path alone.
2、How were β and checkpoints selected? Please state the validation criterion, whether the same criterion was used for every model, and whether any test-set result influenced the choice of β = 4.
3、Why is FlowDesign absent from the comparison?
4、How sensitive are the results to test-group composition and training randomness?
5、Does Figure 1 represent the implemented Gaussian-source process? Please explain how the claim of smoother intermediate states applies when delayed high-frequency modes retain source noise.
We thank the reviewer for their thorough and careful analysis of the ablations and intermediate states. We added crossed path and weighting controls, evaluated variability across training runs and antigen groups, and clarified how to interpret intermediate states.
Q1. Separating the path and loss weighting
We ran both requested controls with seed 2022 (Appendix B.8, Table 10, p. 21).
Each change alone yielded a small RMSD reduction. Spectral weighting with a linear path increased IMP from 23.8% to 31.9%. The combined configuration gave the lowest RMSD and highest IMP in this single-run comparison. The β sweep and reversal comparisons change both the path and its associated loss weights.
At T = 1, Eq. (17) returns the predicted positional endpoint directly. The one-step RMSD gain reflects differences between the trained models, since there are no intermediate states. We clarified this in Section 5.3 (p. 9).
Q2. Selection of β and checkpoints
Checkpoints. We trained each model for 200,000 steps at an effective batch size of 16 and used the final checkpoint for all models. Validation loss was used only for the learning-rate plateau scheduler. We did not use early stopping or validation-based checkpoint selection (Appendix D.2, p. 24). The fixed budget follows MDMAD's baseline reproduction protocol. The external baseline numbers are from MDMAD, and we follow its OpenMM/Rosetta relaxation protocol.
β selection. We ran the H3 sweep with seed 2022 (Table 2, p. 9).
We chose β = 4 because it gave the lowest H3 RMSD on the benchmark test split in this sweep (Appendix D.2, p. 25). We used this value for all six CDRs. The additional runs kept β fixed on the same split to assess variability across seeds. MDMAD also reports a mixture-size sweep and uses four mixture components each for position and orientation in its main configuration (Durvasula et al., 2026, Tables 1 and 6).
Q3. FlowDesign comparison
FlowDesign's published results use a different data split, with initial CDR structures generated by dyMEAN retrained on that split. A matched comparison would require priors prepared for our split. We attempted this adaptation. The available templates covered 9 of our 19 complexes. The KIC templates we generated for the remaining 10 used a different initialization procedure, so we did not report the preliminary results as a matched baseline.
Q4. Training seeds and antigen groups
Training and sampling seeds. We evaluated four independent training runs per model on the same split. Each run used the same seed for training and sampling, and seeds were matched across models. Mean H3 RMSD decreased from 3.331 ± 0.106 Å to 3.053 ± 0.135 Å (mean ± sample SD), an 8.4% reduction, and was lower in every matched run. Mean IMP increased from 25.72% to 28.22%, with gains in three of four runs (Appendix B.5, Table 8, p. 19). The paired bootstrap in Appendix B.4 quantifies uncertainty across complexes for the seed-2022 comparison.
Antigen groups. The 19 evaluated complexes represent four antigen groups. Mean H3 RMSD was lower within each group. Using existing predictions, we excluded each group in turn and recomputed the mean on the remaining complexes. The reduction ranged from 0.211 to 0.410 Å, with lower RMSD in all four runs for every exclusion (Appendix B.10, p. 22).
Q5. Gaussian source and intermediate states
We agree that delayed high-frequency clocks retain more Gaussian source noise in those modes at the same time. The coarse-to-fine ordering refers to the rate at which target contributions grow. We removed the claim that this makes intermediate samples smoother. Figure 1 (p. 1) now shows the Gaussian source, and the caption states:
We also revised Appendix B.3 (p. 19) to explain that a trajectory remaining at its source has a normalized single-mode residual of Aₖ(t)². A delayed clock can make this residual small even without progress toward the target. The diagnostic measures proximity to the prescribed path and does not establish that useful coarse geometry is learned first.