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Under review as a conference paper at ICLR 2027

Proteina-Reforza: Reinforcement Learning Protein Binder Design

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Abstract

Flow- and diffusion-based generative models have transformed de novo protein binder design, but they are typically trained to reproduce molecular data distributions without explicit alignment to design objectives. Here, we introduce Proteina-Reforza, a reinforcement learning (RL) approach that post-trains Proteina-Complexa to improve protein binder design. We adapt the Advantage Weighted Matching RL framework to Proteina-Complexa’s partially latent representation for atomistic joint sequence–structure generation. Rewards include structure prediction confidence scores, physics-based Rosetta energies, affinity predictions, as well as a novel diversity reward, and we additionally train reward models on experimental binding data to enable RL guided by experimental outcomes. We apply Proteina-Reforza to both minibinder and cyclic peptide design, for both protein and ligand targets, and demonstrate general model alignment as well as target-specific adaptation for challenging design tasks. Proteina-Reforza achieves state-of-the-art performance on established in silico binder design benchmarks, substantially outperforming existing methods, and alleviating the need for extensive post-hoc filtering. Further analyses and ablations reveal how RL shapes the generated binders and support their structural and biophysical plausibility, without noticeable reward hacking. Experimental evaluation of generated minibinders and cyclic peptides confirms that these computational gains translate into improved binding success in the lab.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
protein design, reinforcement learning, post-training, binder design, flow matching, generative modeling, diffusion models

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_89DCOpenReview ↗
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3
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Informativeness
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Paper summary

The paper introduces Proteína-Reforza, which adapts Advantage Weighted Matching to post-train a joint sequence–structure protein binder generator. It explores structural, physical, and experimentally learned rewards for general and target-specific design, including cyclic peptides. Computational benchmarks show substantial improvements in successful binder generation. PD-L1 binding experiments and peptide display screens provide additional support, though the experimental evidence is narrower than the computational evaluation.

Critical strengths
  1. The improvement on the main protein-binder benchmark is substantial. Under the same sampling budget, successful designs increase from 22.05 to 91.14 per target, and structurally distinct successes from 14.18 to 61.82. Gains also transfer to alternative structure predictors, making the result more convincing than an improvement measured only by the training reward.

  2. The paper provides experimental evidence beyond computational scores. The PD-L1 study identifies seven binding-positive designs from the adapted RL model versus none from the base model, with the best showing an apparent affinity of 64.7 nM. Although limited to a target-adapted setting, this is meaningful evidence that the approach can improve practical binder discovery.

Critical weaknesses

The main protein-binder benchmark lacks a filtering-based supervised fine-tuning baseline under a matched reward-evaluation budget. Consequently, the results do not establish how much of the improvement comes from AWM rather than learning from reward-selected samples. Comparing AWM against iterative generation–scoring–filtering–SFT, with matched initialization, target distribution, and reward-evaluation budget, would help isolate the benefit of the proposed optimization approach.

Questions for authors

How does AWM compare with iterative generation–scoring–filtering–SFT on the main protein-binder benchmark, using the same initialization, target distribution, and reward-evaluation budget? This comparison would clarify whether AWM offers a meaningful advantage over simply training on reward-selected samples.

1 comment

Thank you for recognizing the benchmark gains, their transfer across structure predictors, and the value of the PD-L1 results. Our additional experiments are in Section K. To show the generality of our approach, we also include results on RFD4-Proteina (§K.4) that show RL can further improve a new generator with a different architecture.

W1 + Q1: AWM versus filtering-based SFT. How does AWM compare with iterative generation–scoring–filtering–SFT on the main protein-binder benchmark, with matched initialization, target distribution, and reward-evaluation budget? This would isolate the benefit of AWM beyond learning from reward-selected samples.

We carried out this suggested comparison and added the results in §K.2 and Figure 40, using the same Complexa initialization, target distribution, and reward-evaluation budget for iterative filtered SFT and RL. Reforza produces about 3.5× as many structurally unique successes as the stronger SFT round.

Filtered SFT improves over the base model, but another round slightly increases total successes while reducing structural diversity. This suggests that repeated training on a small, positive-only dataset concentrates generation around the retained examples rather than discovering new successful folds.

Unlike filtered SFT, which only imitates accepted designs and discards the training signal from rejected ones, AWM uses relative rewards to reinforce higher-reward designs and suppress lower-reward designs, with fresh on-policy samples throughout training. This helps explain why RL finds a broader range of successful structures.

We hope the matched-budget filtered-SFT comparison addresses your main concern and clarifies the benefit of AWM beyond learning from reward-selected samples. If you feel that this concern has been addressed, we would be grateful if you would kindly consider raising your score in light of the new evidence.

Reviewer_4hd7OpenReview ↗
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3
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3
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3
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Paper summary

The paper addresses a mismatch in structure-based de novo binder design: flow/diffusion generators such as Proteína-Complexa are pretrained to reproduce a data distribution and are not aligned with any design objective, so usable candidates are obtained by sampling in bulk and filtering post hoc, while inference-time search spends additional compute without updating the model. The authors adapt Advantage Weighted Matching (AWM) to the partially latent representation of an atomistic binder generator, where explicit Cα coordinates and per-residue latents are generated on separate time axes, keeping the RL update in the same L2 form as the pretraining flow-matching objective with a KL term. Rewards combine folding confidence (AF2-Multimer based), physics (TMol ΔΔG), predicted affinity (Nesso-1), a fold-cluster diversity bonus, and a reward model trained on experimental phage-display data; both general and target-specific post-training are reported. The method is extended to a modality absent from the base model, 12–18 residue terminal-disulfide cyclic peptides. Reported results include in-silico folding success rising from 22.05 to 91.14 (200 designs/target, 22 targets), gains over seven recent baselines under both design-count and GPU-hour matching, transfer to held-out AF2 weights and to Boltz2/ESMFold2 as independent evaluators, and wet-lab evaluation: SPR on PD-L1 and mRNA-display enrichment for cyclic peptides against three targets.

Critical strengths
  • The reward-hacking falsification suite is the paper's most reusable contribution. Four distinct failure hypotheses each get a dedicated experiment: oracle overfitting (G.2 — a held-out AF2 weight set plus two independent evaluators, Boltz2 485→2,005 and ESMFold2 216→467/109→326 in the reported counts, plus an entirely separate RL run with Boltz2 swapped in as the reward oracle); mode collapse (G.7 — Foldseek-unique cluster counts measured along a compute axis, still rising at the maximum budget, which total success counts would have hidden); memorization of training targets (G.4 — per-target gain vs. TM-score to the training pool, r = −0.066, with all three targets below TM 0.5 improving, including SpCas9 8→45 at TM 0.259 and Claudin1 3→67 at TM 0.421); and condition-ignoring (G.8 — hotspot commitment 51.95%→80.75%, improved on 19 of 20 targets). The second RL run with a swapped reward oracle is a stronger control than the usual "re-score with another model."
  • Interface biophysics is reported over the full design distribution, not the success set. G.6 gives median dSASA 1,397→2,544 Ų, shape complementarity 0.33→0.53, H-bonds 3→8 across all ~4,400 designs, with amino-acid composition shifts of only a few percentage points. Reporting over the whole distribution closes the selection-effect alternative that a success-set-only analysis cannot distinguish.
  • The PD-L1 SPR result is real and I accept it without reservation at its stated scope. 7/60 binding-positive for the RL pipeline vs. 0/60 for the base pipeline (best apparent K_D ≈ 65 nM) is not plausibly chance (Fisher exact, one-sided p ≈ 0.0065; reviewer-computed — the paper reports no test).
Critical weaknesses

The cyclic-peptide wet-lab claim is not distinguishable from the null, yet the abstract says "confirms." The abstract states that "Experimental evaluation of generated minibinders and cyclic peptides confirms that these computational gains translate into improved binding success in the lab," and §5 repeats it. The entire supporting statistic (J.2, Fig. 37–39, Tab. 22) is the RL/SFT split of the pooled top-50 by read count: 28/22 (GABARAP), 27/23 (PD-L1), 29/21 (TROP2). Against the 25/25 null these are indistinguishable from chance (two-sided binomial p ≈ 0.48, 0.67, 0.32; pooled 84/150 p ≈ 0.17 — all reviewer-computed; the paper reports no statistical test anywhere). Three further problems compound this: the readout is mRNA-display read count, which confounds binding with display efficiency and PCR bias, and which the authors themselves scope as "within-target assay enrichment"; the paper states that "direct binding-affinity measurements are planned," so zero cyclic peptides have confirmed binding; and the two libraries are not matched — tier composition differs (Fig. 38, e.g. TROP2 strict RL 6,219 vs. SFT 4,142) as do per-hotspot-set design counts (Tab. 22, e.g. GABARAP H2 RL 3,236 vs. SFT 4,474). This matters because "experimentally validated in both modalities" is what separates this from an in-silico paper, and half of it is statistically empty. Minimal fix (no new experiment): remove cyclic peptides from the scope of "confirms" in the abstract/§5/§6 and describe them as preliminary enrichment results with affinity measurements pending; report the test or CI for the splits in §5 and J.2; state the library asymmetry in the main text. Alternatively, run the already-planned affinity measurements. I classify this as Critical not because more experiments would be nice, but because the presented evidence cannot separate the stated conclusion from the null — and as demonstrated-flaw-in-claim rather than in science, since narrowing the claim resolves it completely.

"State-of-the-art by a large margin" is measured only on the objective this model was trained to optimize. Table 1 success is defined by AF2-Multimer criteria (ipAE ≤ 7, pLDDT ≥ 0.90, scRMSD < 1.5; §D) and reward Eq. (3) penalizes violations of exactly those three thresholds. G.2 re-scores only the base and RL models under Boltz2/ESMFold2; the seven baselines were never re-scored under an independent evaluator, so it is unknown whether "BindCraft 45.73 vs. 91.14" survives an evaluator switch. The held-out AF2 weight set is a within-family control only. The authors' own Fig. 19 shows RL AF2 success of 45.6% falling to 10.6% under Boltz2, so absolute levels under an independent evaluator are very different from the impression Table 1 gives. The bias is also not uniform across baselines — BindCraft is a hallucination method that optimizes AF2 directly and is therefore partly aligned, while RFDiffusion3/PXDesign/ODesign/Genie3 are not — so the ranking itself may be evaluator-dependent. Compounding this, the Proteína-Complexa row is run with its published core component disabled (H.5: "no reward-based rejection or additional guidance model"). That is the correct control for isolating the RL delta, but it is the wrong basis for a "beats all existing methods by a large margin" claim, and since §1 positions RL as the alternative to inference-time search, guidance-on Complexa is the most important competitor and is absent. Minimal fix (no retraining, no new generation): re-score the already-generated baseline designs (200 × 22 each) with Boltz2 or ESMFold2 and report an independent-evaluator version of Table 1; state the guidance-off configuration in §4.1; ideally add one guidance-on Complexa column at matched GPU-hours.

Questions for authors

Will you either (a) narrow the abstract/§5/§6 so that "confirms" covers minibinders only and cyclic peptides are described as preliminary enrichment with affinity measurements pending, or (b) report the planned direct binding-affinity measurements? If (b) yields confirmed cyclic-peptide binders, I would move to accept. If (a), please also report a test or CI on the 28/22, 27/23, 29/21 splits — do you agree with my computation (two-sided binomial p ≈ 0.48/0.67/0.32; pooled 84/150 p ≈ 0.17), and if not, what test do you propose?

Can you re-score the already-generated baseline designs with Boltz2 or ESMFold2 and report an independent-evaluator version of Table 1? No new generation or training is needed. If the ranking holds, C2 becomes substantially stronger than it currently is; if it changes, that is itself an important result for the field. What is the ranking under at least one independent evaluator?

2 comments

Thank you for recognizing the value of our reward-hacking controls, interface analysis, and PD-L1 results. Our additional experiments are in Section K. To show the generality of our approach, we also apply the method on RFD4-Proteina (§K.4), which shows the gains to a new generator with a different architecture. We also highlight our modifications to the writing related to the cyclic peptide experiments in red.

W1 + Q1: Cyclic-peptide experimental evidence. Do the enrichment results support improved binding, given the reported non-significant top-50 splits, possible display/PCR biases, and unmatched library composition? Please provide direct affinity measurements, or narrow the claims to preliminary enrichment, report statistical tests or confidence intervals, and disclose the library asymmetry.

We agree that screening enrichment is preliminary evidence and does not confirm binding of the designed cyclic peptides. We have described these results as preliminary within-target assay enrichment and narrowed the corresponding claims in the updated abstract and main text.

To assess assay performance, we included positive controls for GABARAP, PD-L1, and TROP2 with SPR-confirmed binding affinities below 100 nM. These controls were enriched in the respective screens, supporting assay performance. After identifying PCR bias, particularly in the PD-L1 and TROP2 screens, we repeated the experiments for these two targets with an additional protocol step intended to improve cDNA amplification efficiency and reduce amplification bias. All PD-L1 and TROP2 screening results reported here correspond to these repeated experiments, while GABARAP results are from the original screen. Average post-selection read counts per detected unique peptide were 812, 1,000, and 998 for GABARAP, PD-L1, and TROP2, respectively, describing sequencing coverage among detected candidates. We also optimized display efficiency to approximately 90%. These measures improve assay quality but do not eliminate potential display or amplification biases or establish binding affinities for the designed candidates.

We reanalyzed the results to account for sequences generated by both methods, this is, the SFT model and the RL model. Each method selected 10,000 unique candidates per target, with 165 shared sequences for GABARAP, 764 for PD-L1, and 472 for TROP2. Shared sequences were ranked once and counted toward both methods. The GABARAP top 50 contained 28 RL-only and 22 SFT-only candidates. The updated PD-L1 top 50 contained 24 RL-only, 24 SFT-only, and two shared candidates, giving 26 candidates per method. The updated TROP2 top 50 contained 36 RL-only and 14 SFT-only candidates. The corresponding RL/SFT candidate-count ratios were 1.27, 1.00, and 2.57. These ratios describe top-50 counts rather than binding success rates.

Following the reviewer’s analysis, we added two-sided exact binomial tests comparing RL-only and SFT-only counts under an equal-probability null hypothesis, excluding shared candidates. The nominal p-values were 0.4799, 1.0000, and 0.00260 for GABARAP, PD-L1, and TROP2, respectively. TROP2 showed a significant difference favoring RL, whereas GABARAP showed a smaller, nonsignificant difference and PD-L1 had equal counts. Some GABARAP candidates also had read counts comparable to those of validated positive controls. These exploratory tests assume independent candidates and equal selection opportunities; the reported p-values are unadjusted for multiple comparisons.

RL and SFT had equal generation budgets within each hotspot configuration. Candidates were pooled across hotspot configurations, deduplicated, and selected by tier priority and within-tier ranking to obtain 10,000 unique sequences per method and target. Table 22 reports the hotspot composition of these selected candidates across all six tiers, while Figure 38 shows their tier composition across all hotspot configurations. We updated Table 22 to report the number of designs generated per model within each hotspot configuration, alongside the selected counts.

Overall, the results indicate that improved in-silico RL performance for cyclic peptide binders can also translate to the wet lab, although the effect is target-dependent in our experiments and based on preliminary enrichment analyses. SPR measurements for designed GABARAP and PD-L1 candidates are in progress. As these results are not yet available, we do not claim confirmed binding for the designed cyclic peptides. Our revised manuscript text distinguishes preliminary cyclic-peptide screening enrichment from experimentally confirmed minibinder binding.

We added these additional analyses and discussions in the §J.2 of the paper, with all additional content denoted in red color. The relevant modifications in the main paper text are highlighted similarly.

W2 + Q2: Independent evaluation and inference-time search. Does the baseline ranking hold when all methods are re-scored with Boltz2 or ESMFold2? Please report an independent-evaluator version of Table 1, disclose that Complexa guidance was disabled, and ideally compare with guidance-on Complexa at matched GPU-hours.

Thank you for these concrete suggestions. We have added both requested comparisons.

Independent evaluators (§K.1, Table 23). We re-scored all baselines with Boltz2 and ESMFold2. Reforza achieves the most structurally unique successes across AF2, Boltz2, and ESMFold2, although baseline rankings vary across evaluators. ESMFold2 hallucination slightly exceeds Reforza in total and sequence-unique successes when evaluated with ESMFold2 itself, which it directly optimizes against (§I.2), but its performance transfers less well to AF2 and Boltz2, both held out from both methods. Reforza outperforms it under these shared, independent evaluations while generating designs roughly 1,300× faster, a difference of over three orders of magnitude in compute per design. These results show that Reforza’s gains transfer across folding models while retaining efficient generation.

We also observe transfer with RFD4-Proteina (§K.4, Table 24 and Figure 44): RL trained with AF2 rewards improves performance under independent OpenFold3 evaluation as well, yielding about 2.1× as many structurally unique successes as the high-thinking base model.

Guidance-enabled Complexa (§K.3, Figures 41–43). Table 1 compares methods under the same sample budget. Inference-time search generates and evaluates additional candidates and takes substantially more time, so we report this comparison separately under matched GPU-time budgets for a fair and meaningful evaluation. Following the original Complexa inference-time scaling setup, we compare Reforza with Complexa best-of-N sampling and guidance-enabled beam search. Across the evaluated targets, Reforza consistently produces more structurally unique successes than both Complexa approaches at matched GPU budgets.

We hope the revised cyclic-peptide claims and analysis, together with the new independent-evaluator and guidance-enabled comparisons, address your concerns. If you feel that these revisions have resolved your concerns, we would be grateful if you would kindly consider raising your score in light of the strengthened evidence.

Reviewer_4j92OpenReview ↗
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4
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4
Informativeness
3
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Paper summary

Proteína-Reforza post-trains the atomistic binder generator Proteína-Complexa with Advantage Weighted Matching on a partially latent sequence–structure representation. Rewards combine AlphaFold2 or RosettaFold-3 success, Rosetta interface energy, a Nesso-1 affinity score, a Foldseek diversity bonus, a hydrophobic-burial stability penalty, and a classifier fit to phage-display outcomes. The same recipe is applied to minibinders, small-molecule targets, and disulfide cyclic peptides, in both a general target mixture and target-specific runs, with SPR and mRNA-display follow-up.

Critical strengths
  1. The empirical jump on the 22-target protein benchmark is large. With 200 samples per target, folding-success RL reports 91.14 total and 61.82 Foldseek-unique successes, against 22.05 / 14.18 for the base model and 45.73 / 27.82 for BindCraft, at the same 0.45 s/sample as the base model.

  2. Held-out AlphaFold2 weights, transfer checks across folding models, Rosetta and hydrogen-bond gains, and a stability filter make a pure reward-fitting story harder to dismiss. Joint folding plus TMol training further improves interface energy (−128.5 versus −110.5 for folding-only).

  3. Target-specific RL recovers successes where the base model has none (TNFα 0 to 3, H1 2 to 23 unique successes). The diversity reward and the stability penalty are sensible responses to mode collapse and extended decoys.

  4. Wet-lab results exist. On PD-L1, a preliminary RL model yielded 7 SPR binders out of 60 tested designs, including a 64.7 nM hit, against 0/60 for the base model. Disulfide peptides are enriched in mRNA-display read counts (29/50 versus 21/50 of the combined top 50 on TROP2; similar margins on GABARAP, 28 versus 22, and PD-L1, 27 versus 23).

Critical weaknesses

No critical weakness.

Questions for authors
  1. What is the strict-filter pass rate per 2,000 designs for the base model versus RL on PD-L1, and what is the hit rate if both arms are tested only on strict-filter designs, or on a random sample before filtering?

  2. For the 22-target table, how many successes remain if evaluation uses a folding-model family that was never in the reward, with thresholds fixed before looking at the RL outputs?

  3. On the classifier holdout, what is the target-level AUROC of the reward model, and do gains survive if entire targets, not crops, are held out of classifier training?

1 comment

Thank you for recognizing the benchmark gains, the controls against reward overfitting, and the PD-L1 results. Our additional experiments are in Section K. This includes results on RFD4-Proteina (§K.4) that show the gains extend to a new generator for testing the generality of our approach.

Q1: What is the strict-filter pass rate per 2,000 designs for the base model versus RL on PD-L1, and what is the hit rate if both arms are tested only on strict-filter designs, or on a random sample before filtering?

Thank you for asking us to separate candidate yield from experimental hit rate. As detailed in §J.1 (Table 20 and Figures 34–35), the strict filters retain 9/2,000 designs for Complexa (0.45%) and 93/2,000 for the preliminary RL model (4.65%). We apply the same selection rule to both models, prioritizing strict candidates and filling any shortfall with relaxed candidates. This yields 9 strict and 51 relaxed-only designs for Complexa, and 60 strict designs for RL. All 9 strict Complexa designs were tested and none bound; the strict RL panel yielded 7/60 binding-positive designs (11.7%).

We have not experimentally tested random unfiltered samples, and we do not have enough time to complete such additional wet lab comparisons within the rebuttal period. We are, however, actively testing new targets using our RL models and will update the final version with the results.

Q2: For the 22-target table, how many successes remain if evaluation uses a folding-model family that was never in the reward, with thresholds fixed before looking at the RL outputs?

We agree and have evaluated the designs with Boltz2 and ESMFold2, neither of which was used in the AF2-based training reward. As reported in §G.2, Reforza outperforms Complexa under both evaluators: 21.23 versus 9.82 successes per target under Boltz2 and 14.82 versus 4.95 under ESMFold2, with about 2.6× and 2.9× as many structurally unique successes, respectively. These results show that the gains transfer across different folding models.

We also added a comparison with all baselines under both independent evaluators (§K.1, Table 23). Reforza produces the most structurally unique successes under both Boltz2 and ESMFold2, showing that its advantage extends beyond the comparison with Complexa.

We observe the same transfer when applying RL to RFD4-Proteina (§K.4, Table 24 and Figure 44): although training uses AF2 rewards, the gains also hold under independent OpenFold3 evaluation, with about 2.1× as many structurally unique successes as the high-thinking base model.

Q3: On the classifier holdout, what is the target-level AUROC of the reward model, and do gains survive if entire targets, not crops, are held out of classifier training?

Thank you for highlighting the distinction between binder holdout and target holdout. Table 13 in §E.3 reports a per-target AUROC of 0.698 for the selected classifier, compared with 0.682 for AF2 ipTM; pooled AUROC is 0.806 versus 0.779, and AUPRC is 0.134 versus 0.103. As described in §B.5.2, binder structural families are kept in separate splits within each target; 22 targets with at least 30 positive examples are eligible for holdout.

The classifier deliberately sees all target crops, including those held out from RL training, so that this proof-of-concept studies post-training with a reliable, in-distribution experimental surrogate. We have not evaluated the full pipeline with entire targets held out of classifier training and therefore cannot claim that the gains survive that stricter split. Table 4 (§4.4) shows that the combined classifier-and-folding reward can improve computational design metrics on crops held out from RL, but its classifier scores use the training reward model and are not an independent experimental validation. Note that training a classifier reliably also for the target-holdout setting can be expected to be more challenging and will likely require more diverse training targets for generalization. Therefore, this is beyond the score of the rebuttal and left for future research. We view target-held-out evaluation as an important next step.

We hope we have addressed all of your questions. Thank you again for your thoughtful feedback, and please let us know if you have any further questions.

Comments on the paper

1 comment

We thank all three reviewers for their careful reading and constructive suggestions. We are encouraged that the reviewers found the computational improvements substantial and the PD-L1 results meaningful. Their feedback helped us strengthen the comparisons and clarify what the experiments establish. We gather all additional results for the Rebuttal in Appendix K for convenience and we will reorganize the content for the final version. Modifications elsewhere in the paper are highlighted in red.

In response to the reviewers’ requests, we added the following three experiments:

  1. Independent evaluation of all protein-binder baselines (§K.1, Table 23). Re-scoring all methods with Boltz2 and ESMFold2 confirms that Reforza produces the most structurally unique successes under both independent evaluators.
  2. Filtered SFT at a matched reward-evaluation budget (§K.2, Figure 40). Reforza produces about 3.5× as many structurally unique successes as the stronger filtered-SFT round under the same reward-evaluation budget, while another SFT round slightly improves total successes but reduces structural diversity.
  3. Comparison with guidance-enabled Complexa (§K.3, Figures 41–43). Reforza retains its advantage in structurally unique successes over guidance-enabled Complexa at matched GPU-time budgets, showing that the gains extend beyond comparison with an unguided base model.
  4. Cyclic peptide experiments and interpretation (§5, Figure 8, §J.2). We repeated the PD-L1 and TROP2 screens with a revised protocol to reduce PCR bias. RL contributed 36 of the top 50 TROP2 candidates versus 14 for SFT, a significant difference after Bonferroni correction across three targets (p=0.0077), while GABARAP showed slight enrichment and PD-L1 showed no significant difference. We added statistical tests and confidence intervals, accounted for shared sequences, and clarified differences in library composition.

To further strengthen the paper, we also added the following two experiments:

  1. Transfer to RFD4-Proteina (§K.4, Table 24 and Figure 44). We extended Reforza to the recently released RFD4-Proteina model [1] to test whether RL can further raise the performance ceiling of protein binder design across different architectures. At high thinking, RL yields 2.4–2.7× as many successful designs and about 2.1× as many structurally unique successes under held-out AF2 and independent OpenFold3 evaluation, establishing a new state of the art on this in silico benchmark; even the low-thinking RL model produces 1.5–1.7× as many structurally unique successes as the high-thinking base model.
  2. Physics-based rewards for ligand targets (§K.5, Table 25). Adding TMol to the folding reward improves successful-design yield, structural diversity, interface energies, and hydrogen bonding together, supporting physics-based feedback as a complementary signal for ligand binder design.

[1] Corley, N. et al. “Biomolecular design through latent reasoning with RFD4-Proteina.” preprint (2026).

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