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Under review as a conference paper at ICLR 2027

BioCoLoop: Collaborative Agentic Research for Biological Model Improvement

Abstract

Artificial intelligence is increasingly used to automate biological model development. Recent self-improving agents extend this process by iteratively proposing model changes, training and evaluating them, and using the observed results to guide subsequent proposals. However, biological data are often distributed across laboratories and cannot be centrally pooled, making this iterative process difficult to apply. We introduce BioCoLoop, a collaborative research framework that extends collaboration from parameter fitting to model development itself. BioCoLoop collaboratively trains and evaluates proposed model structures and training hyperparameters across laboratories, and uses the resulting evaluation results to determine what should be tested next and which models should receive further training. Across drug-target interaction prediction, proteomic efficacy prediction, and cell perturbation identification, BioCoLoop consistently improves predictive performance. We further show that early evaluation results can guide which models continue training, improving performance under the same training and evaluation budget.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
AI for Science, Research Agents, Automated Research, Single-Cell Genomics

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_cR5gOpenReview ↗
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Paper summary

The paper proposes a framework to improve the training configuration of a federated model trained across several labs, with an LLM choosing a value for 4 hyperparameters such as the learning rate. The results of earlier trials are used as feedback.

Critical strengths

The paper sets out to address an important problem in the medical setting: distributed training where different laboratories can not share their data.

Critical weaknesses

The evaluation has flaws:

  • no comparison to traditional hyperparameter tuning, not even to random search
  • the laboratories are not real independent entities with a domain shift and batch effects, but random splits of a single dataset. The evaluation therefore never tests the hard part of combining multiple datasets across labs, but only addresses the distribution of the training.
  • the authors' own pipeline, when training a single model ("direct"), performs worse than a fixed model
  • similarly, other baselines also use 1 model, while BioCoLoop uses 10 labs
Questions for authors

The novelty of the work is not very clear to me, since the main approach appears to be asking an LLM to turn 4 knobs in the training hyperparameter space. Perhaps a better explanation of the novelty could make the reader appreciate the contribution better.

2 comments

Thank you for the review and for highlighting the setting we target: distributed training in biology and medicine when laboratories cannot share data. The revision adds single-laboratory random, Bayesian and exhaustive search, matched-access controls, a ten-laboratory fixed model, and laboratories built from distinct released studies. These separate two questions: whether collaborative training helps on real sources, and whether the research loop adds gain beyond that.

1. Traditional tuning and random search

On laboratory 0, random search, GP-EI Bayesian optimization and exhaustive enumeration all stay below collaborative BioCoLoop (Appendix D): DTI AUROC 90.10 vs 93.76, and random-search proteomics AP 20.13 vs 36.99.

At matched ten-laboratory access (Appendix E.1-E.2), all policies share laboratories, panels, configuration library and budget, and failed requests are charged. Language-model search and GP-EI reach 31.50 VCC Top-1 against 27.53 for random search. In eight-seed extensions registered before the new fits:

  • Luna beats random search by +0.053 AUROC percentage points on DTI (CI [0.050, 0.055]) and beats GP-EI in all eight seeds (E.6).
  • History beats direct search by +0.41 Top-1 on gene-disjoint cells (95% CI [0.09, 0.84]; E.5).
  • After canonicalizing request metadata (invalid requests fall from 102 to 5 of 288), Qwen also beats random and GP-EI on DTI in all eight seeds (Table E.7).

The research loop's extra gain over random search is small, and GP-EI performs better on protein (39.02 AP) and on the gene-disjoint cells (23.28 Top-1).

2. Simulated laboratories and domain shift: collaborative training on real sources

The main laboratories are grouped by canonical compounds (DTI), compound groups (proteomics) and disjoint training interventions (cells); none is shared between laboratories. The source-defined experiments assign a different released study to each laboratory (Section 4.5, Appendix B.2):

  • Proteomics (PTPC, Lin, Ruprecht and decryptE, eight seeds): target AUROC rises from 72.06 to 74.13 (+2.07, CI [0.65, 3.38]), and AP from 34.60 to 36.82.
  • DTI: adding Davis or Human raises target AUROC from 85.47 to 87.86 and 87.95.
  • Cells: adding Jiang raises VCC Top-1 from 29.49 to 33.07.

Not every source helps: BioSNAP lowers target DTI AUROC by 3.03, and Replogle and Nadig lower VCC Top-1 by 2.37 and 2.55, so compatibility between studies matters. These experiments measure the value of collaborative training, not the research loop's extra gain, which the matched-access controls above evaluate. All laboratories run on shared compute; real-site deployment is next.

3. Direct search versus the fixed model

Section 4.2 now defines both. Direct search trains several candidates without feedback from earlier evaluations and keeps one by development score; the fixed model is the single default configuration. The single-laboratory gap comes from selecting on laboratory 0's small development panel.

4. Ten laboratories versus one model

The ten laboratories hold data; they are not an ensemble. BioCoLoop, like every baseline, returns one predictor evaluated on the same test set. Table 1 makes the standard federated comparison, developing with collaborators against developing alone, and its caption now says so. It cannot separate the contribution of collaboration from that of search on its own, so two controls hold access fixed. Against a ten-laboratory fixed model (Table D.1), BioCoLoop adds 1.96 DTI AUROC and 6.77 Norman Top-1. On proteomics and VCC the fixed model already matches BioCoLoop (37.07 vs 36.99 AP; 31.54 Top-1 for both), and on Tahoe it is 3.48 points higher, so there the gain is carried by collaboration itself.

5. "Asking an LLM to turn 4 knobs"

The contribution is a protocol and interface through which laboratories that cannot pool data jointly decide which design to keep, what to try next and how to allocate further training, exchanging only model updates and bounded per-laboratory development evidence. It serves three task families and several research agents. The four-factor library keeps the comparisons interpretable, and Appendix E.6 widens it to 36 recipes.

The clearest gain from the loop itself is the two-stage budget allocation. At matched training and evaluation budgets, screening on early collaborative evidence and training the promising candidates longer raises Norman Top-1 from 11.48 to 22.32 over uniform allocation (+10.84, CI [4.54, 17.73]), and across 12 task-seed pairs it never loses to uniform (E.4). Random promotion after the same screen is competitive with trajectory promotion (six wins, six losses), so the gain comes mainly from screening followed by longer training, not from trajectory guidance alone.

Thank you again; these points led to the controls added in this revision.

I thank the authors for the revisions they made. I'm still not convinced that the novelty and demonstrated gains are at a high enough level, so I will not raise my score, but I wish them all the best with continuing this work.

Reviewer_AfJBOpenReview ↗
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Paper summary

The authors introduce BioCoLoop, a framework for sharing model-development information across laboratories with siloed biological data. The central idea is that collaboration can extend beyond sharing model parameters to sharing development evidence to guide subsequent model improvement. The framework uses an LLM to propose model configurations, which are collaboratively trained and evaluated across laboratories using federated learning. The aggregated results are returned to the LLM to inform subsequent proposals. The search space primarily consists of hyperparameters with a small architectural modification. The authors evaluate BioCoLoop across three biological prediction applications and compare it against fixed models, direct optimization, and existing AI-scientist systems. BioCoLoop generally achieves improved performance in the main comparisons.

Critical strengths

I appreciate the matched-training-budget experiment evaluating evidence-guided allocation.

Critical weaknesses
  1. The primary concern is the novelty of the proposed framework relative to the existing literature.

Several existing works have already explored collaboration among AI agents for scientific discovery. For example, The Virtual Biotech (James Zou and colleagues) investigates the coordination of specialized AI agents for therapeutic discovery, while AutoScientists (Gao, Fang, and Zitnik) explicitly investigates collaborative scientific experimentation, shared experimental histories, and the advantages of coordination over independent agents. More directly relevant is Helmsman: Autonomous Synthesis of Federated Learning Systems via Collaborative LLM Agents (ICLR 2026), which already introduces a framework in which LLM agents iteratively design, implement, evaluate, and refine federated learning systems.

Although these works do not investigate exactly the same thing, they establish much of the conceptual foundation of collaborative agentic research and automated improvement of federated learning systems. Given these existing contributions, it is difficult to discern what methodological novelty BioCoLoop introduces.

  1. The second major concern is whether the experiments demonstrate the value of the proposed research loop itself.

Table A.1 is concerning. When the number of laboratories is held at one, BioCoLoop performs essentially identically to direct optimization across all five evaluated endpoints, with a slight decrease on VCC. Tables A.2 and A.3 show the same general pattern. Also, the main comparison in Table 1 provides BioCoLoop access to ten laboratories, while the existing AI-scientist baselines operate on a single laboratory. So it is difficult to attribute the improvements to the proposed agentic research mechanism rather than access to additional training data through collaborative learning. This concern is reinforced by Section 4.7, where the authors directly compare history-guided and feedback-free proposal generation with matched laboratory access. Across ten comparisons, eight show identical final performance.

Questions for authors

My weaknesses cover my questions for the authors.

1 comment

Thank you for the expert review, for pointing us to The Virtual Biotech, AutoScientists and Helmsman, and for your note on the matched-budget allocation experiment. The revision states the method's purpose directly: laboratories that cannot pool data develop one predictor together, and we measure what that gives them over developing it alone.

1. Novelty relative to The Virtual Biotech, AutoScientists and Helmsman

Section 2 now discusses all three. In The Virtual Biotech and AutoScientists, the collaborators are AI agents sharing evidence, programs and logs over data they can access. In BioCoLoop, the collaborators are data-holding laboratories: each trains and scores candidates on its own data, and only model updates and bounded per-laboratory evidence leave the site. Helmsman's agents synthesize and debug federated-learning code; BioCoLoop keeps the federated protocol fixed and uses the laboratories' evidence to decide which design to keep, what to try next and which candidates to train longer. We also position the work against FedEx, FedNAS and FedHPO-Bench, which optimize a predefined numerical space with a fixed algorithm.

Our contributions are:

  • a cross-laboratory model-development interface, instantiated on three biological task families;
  • controlled experiments that separate laboratory participation, proposal policy and training allocation;
  • a two-stage budget allocation (screen on early collaborative evidence, then train a few candidates longer) that improves Norman Top-1 over uniform allocation by 10.84 points (95% CI [4.54, 17.73]) at matched budgets.

The interface is portable: with AI-Scientist-v2 driving it, the ten-laboratory pilot reaches 95.07 DTI AUROC and matches BioCoLoop on the other four endpoints (Appendix C.4).

2. Single-laboratory runs (Tables A.1-A.3)

Your reading is correct, and Appendix D.1 now explains it. With one laboratory, every strategy selects designs on laboratory 0's small development panel, so the strategies land on similar scores. Changing only participation from one laboratory to ten, the same workflow improves all five endpoints (Table D.1):

  • DTI AUROC from 89.89 to 93.76;
  • proteomics AP from 20.13 to 36.99;
  • VCC, Norman and Tahoe Top-1 from 20.22, 14.15 and 15.42 to 31.54, 22.25 and 22.39.

3. Ten laboratories versus one in Table 1

The main table cannot separate the contribution of collaboration from that of search on its own. It makes the standard federated comparison, collaborative development against a laboratory working alone, and its caption now says that rows at the two access levels compare complete scenarios. Two controls hold access fixed. The ten-laboratory fixed model (Table D.1) isolates shared data; on top of it design search adds 1.96 DTI AUROC and 6.77 Norman Top-1, where the default design falls from 25.56 to 15.48 as laboratories join. On proteomics and VCC the ten-laboratory fixed model already matches BioCoLoop (37.07 vs 36.99 AP; 31.54 Top-1 for both), and on Tahoe it is 3.48 points higher, so there the gain is carried by collaboration itself. In the seed-42 pilot with the same ten laboratories, AI-Scientist-v2 matches BioCoLoop on four endpoints.

4. Section 4.7 and the role of history

We agree, and Section 4.7 now opens by saying so: the main gain comes from collaboration, and history is one task-dependent component. We tested history where it has room to matter, with eight seeds and the analysis registered before the new fits:

  • Gene-disjoint cells (E.5): structured history beats feedback-free direct search by +0.41 Top-1 (seed-block 95% CI [0.09, 0.84]; no losses) and beats the fitted default in all eight seeds.
  • 36 wider recipes (E.6, Luna): language-model search beats random by +0.053 AUROC percentage points on DTI (CI [0.050, 0.055]) and beats GP-EI in all eight seeds. On protein, history beats random in six of eight seeds (+0.21 AP).
  • Canonicalizing Qwen's request metadata cuts invalid requests from 102 to 5 of 288, after which Qwen selects the same DTI predictors as Luna and beats random and GP-EI in all eight seeds (Table E.7).

GP-EI performs better on protein (39.02 AP) and on the gene-disjoint cells (23.28 Top-1).

5. Allocation

The gain is that of the two-stage budget arrangement over uniform allocation. In a fresh 360-fit study (Appendix E.4), trajectory promotion beats uniform allocation in four task-seed pairs and loses none, and beats score-only promotion four times to one. Random promotion after the same screen is competitive with it (six wins, six losses), so we do not attribute the gain to trajectory guidance alone: the key ingredient is screening followed by longer training, and the abstract and Section 4.4 now describe the method that way.

Thank you again; your comments made the paper's claims clearer.

Reviewer_FBhKOpenReview ↗
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Paper summary

BioCoLoop combines collaborative model training with LLM-guided configuration search. Laboratories keep their data locally and return model updates and development measurements. An LLM with fixed weights uses the accumulated experiment history to select configurations that vary learning rate, weight decay, coordinator momentum, and an optional residual module. A separate allocation policy uses early scores and improvement trajectories to select candidates for longer training. The evaluation covers drug–target interaction prediction, observed-response proteomic efficacy prediction, and cell perturbation identification. The experiments include comparisons with adapted research agents, controls for laboratory participation and proposal history, and a training-allocation study with matched budgets.

Critical strengths
  1. The paper addresses a practical problem: how to use data held by different laboratories to inform model development as well as model fitting. I found the common training and proposal interface across the three biological task families useful. The appendices specify the configuration libraries, checkpoint selection, decoding settings, and handling of failed proposals in considerable detail. This makes the procedure relatively easy to understand and provides a concrete starting point for further work on collaborative model development.

  2. The allocation experiment provides a positive result under a carefully accounted budget. Both methods use 800 aggregation rounds and 160 aggregate development evaluations, including the cost of screening and restarting candidates. On Norman, the proposed allocation improves Top-1 by 10.84 percentage points, with a reported 95% confidence interval of [4.54, 17.73] (Table 2). Although the benefit is concentrated in this task, it provides evidence that early training measurements can help allocate a fixed budget. The reported ties and negative results elsewhere also help establish the limits of this finding.

Critical weaknesses
  1. The experiments do not establish the added value of the history-guided research loop. In Table 1, BioCoLoop uses ten laboratories while the baselines use laboratory 0. Training data, development data, and total local computation therefore change alongside the search method. The controls with equal laboratory access are more informative, but provide little evidence for an improvement from history: Table B.10 contains eight ties, one improvement, and one decrease; Table B.12 contains seven ties and one decrease. The efficiency result is also mixed: history reaches the Norman/Luna target in four proposals rather than 22, but takes 13 rather than five on Tahoe/Luna (Table B.13). These targets are defined retrospectively. Given that the search covers only 12 or 36 predefined configurations, a random-search baseline under the same laboratory access and budget is particularly important. Without this comparison, I am not convinced that the LLM history mechanism contributes enough beyond collaborative fitting and conventional configuration search.

  2. The development-selection procedure does not reliably translate search progress into held-out improvement. In the extended experiment, VCC/Qwen falls from 31.50 at initialization to 19.61 after 24 proposals, while both Tahoe proposers fall from 25.37 to 13.43 (Table B.12). Development scores improve during these searches. The paper reports this behavior, but does not explain whether it is mainly due to small development panels, differences between development and test aggregation, or overfitting through repeated selection. This matters because the same development evidence drives both the next proposal and the final model choice. The framework’s effectiveness remains uncertain when additional search can produce such large decreases in held-out performance.

Questions for authors
  1. Additional evidence on the central contribution: Can you compare BioCoLoop with random search without replacement and direct LLM search using the same ten laboratories, development panels, configuration library, and training budget? This would help determine whether the history mechanism provides an advantage over simpler search procedures.

  2. Clarification of the validation procedure: What explains the development–test divergence in the extended VCC and Tahoe searches? In particular, how are the development panels constructed, and how does equal weighting of laboratory-level metrics affect selection relative to the common held-out metric? Any existing results across different grouped partitions would help assess whether these failures are specific to the chosen split.

4 comments

Thank you for highlighting the matched-budget allocation result. Your two questions shaped the main additions: a ten-laboratory fixed-model control, random and Bayesian baselines at matched access, eight-seed extensions of two search studies, and an audit of the VCC and Tahoe selections.

1. What the loop adds beyond collaborative fitting, and how it compares with random and direct search at the same access

The main table cannot separate the contribution of collaboration from that of search on its own: single-site baselines are not federated methods and can only develop on their own data. The controls below hold access fixed.

Against the fixed default design trained by all ten laboratories (Table D.1), the loop adds 1.96 DTI AUROC (93.76 vs 91.80) and 6.77 Norman Top-1 points (22.25 vs 15.48); on Norman the default design degrades as laboratories join, and design search lifts it. On proteomics and VCC the ten-laboratory fixed model already matches BioCoLoop (37.07 vs 36.99 AP; 31.54 Top-1 for both), and on Tahoe it is 3.48 points higher, so there the gain is carried by collaboration itself.

At matched access (Appendix E.1-E.2), every policy uses the same ten laboratories, development panels, 12-design library, six proposal slots and 100-round fits, and invalid requests consume slots. Random search is the exact expectation over all 462 six-design subsets. Language-model search reaches 31.50 VCC Top-1 against 27.53 for random, and Luna history reaches 23.11 on Norman against 22.66 for random and 22.30 for direct search.

We extended two 20-round studies from three to eight seeds, with the analysis registered before the new fits and no seeds excluded. History is a task-dependent component with small gains:

  • Gene-disjoint cells (E.5): structured history beats direct search by +0.41 Top-1 (seed-block 95% CI [0.09, 0.84]; four wins, four ties, no losses).
  • 36 wider recipes (E.6): on DTI, Luna beats random search by +0.053 AUROC percentage points (CI [0.050, 0.055]) and beats GP-EI in all eight seeds. On protein, history is +0.21 AP above random and wins six of eight seeds.
  • Canonicalizing metadata errors in Qwen's otherwise valid requests cuts invalid requests from 102 to 5 of 288. Repaired Qwen then selects the same DTI predictors as Luna, beats random and GP-EI in all eight seeds, and its direct search reaches 38.98 protein AP (+0.40 above random; six wins in eight seeds; Table E.7).

GP-EI performs better on protein (39.02 AP) and on the gene-disjoint cells (23.28 Top-1).

The clearest efficiency result is the two-stage budget allocation. At a fixed 800 aggregation rounds and 160 development evaluations, screening candidates on early collaborative evidence and training the promising ones longer raises Norman Top-1 from 11.48 to 22.32 over uniform allocation (+10.84, CI [4.54, 17.73]). In a new 360-fit study (E.4), trajectory promotion beats uniform allocation in four task-seed pairs and loses none, and beats score-only promotion four times to one. Random promotion after the same screen is competitive with it (six wins, six losses), so the gain comes mainly from screening followed by longer training, not from trajectory guidance alone.

2. Development-test divergence on VCC and Tahoe

The audit explains why selection was sensitive on VCC and Tahoe; it does not show that the original failure is fixed.

Panel weighting is not the cause: development and test interventions are disjoint (VCC 60/20/20, Tahoe 180/60/67 training/development/test), the development sets form ten equal panels, and Top-1 is intervention-macro-averaged, so equal panel weighting equals the pooled score exactly.

We reconstructed all 14 selected checkpoints and their 140 development panels, and reproduced all 80 archived held-out prefix scores (E.3). The audit points to selection on a very small development population: Tahoe's +5.00 development gain corresponds to three extra correct compounds. Re-scoring the same checkpoints on 20 redrawn distractor rosters, without retraining, turns Qwen/VCC's +1.17 into -1.34 +/- 7.37 and Tahoe's +5.00 into -1.33 +/- 4.82. It does not single out one cause, and biological differences between development and test interventions may also contribute.

Larger, better-grouped development populations kept selection aligned with held-out performance where we tested them: with gene-disjoint contexts (E.5; 1,208/414/406 training/development/test genes), structured history exceeds the fitted default in all eight seeds. Pooling evidence matters too: laboratory-level rules (a dispersion penalty, a 6-of-10 majority) lower protein AP in all eight seeds relative to the pooled score (Table E.7). VCC and Tahoe were not re-run under these settings, and we report them as an unresolved limitation.

Thank you again; both questions changed what the paper reports.

Thank you for the comprehensive response and the additional experiments. Incorporating the matched-access comparisons, random and Bayesian optimization baselines, and extended multi-seed evaluations substantially strengthens the empirical evaluation and addresses many of my initial concerns.

Specifically, the ten-laboratory fixed-model control effectively separates the benefits of collaborative training from those of configuration search. I also welcome the expanded analysis of the VCC and Tahoe results—pointing to the small development population and distractor-roster sensitivity provides a reasonable explanation, even if the generalization issue persists as a limitation.

Regarding the newly provided results, I have two follow-up questions:

  1. Contribution of history feedback. Outperforming random search and GP-EI is encouraging, yet it does not fully isolate the impact of history feedback. Which specific comparisons within the new multi-seed results best isolate the benefit of history-guided search over direct LLM search under the same setting?

  2. Interpretation of the extended experiments. Given that the new eight-seed studies operate under shorter training budgets than the original main experiments, how should these outcomes be weighed relative to the original 100-round search protocol?

Taken together, the rebuttal satisfactorily addresses several core concerns and makes the experimental case stronger. What remains open in my view is not the utility of the collaborative framework itself, but rather the magnitude and consistency of the added gains brought by history-guided search.

Thank you for recognizing the additional experiments and improvements to the paper. Your distinction between the benefits of collaborative training and the contribution of history feedback has also helped us present the evidence more clearly. We address your two follow-up questions below.

1. Which comparisons most directly show the contribution of history feedback?

The most direct evidence comes from the comparison of Direct, Raw history, and Structured history in Appendix E.5. These three arms use the same LLM, the same 16-design candidate library, a shared cache of trained candidate outcomes, and the same six proposal slots. They also share the first proposal. Direct receives no previous trial outcomes when generating subsequent proposals; the two history arms receive development feedback and differ in how that information is organized.

Across eight seeds (Table E.4):

  • Structured outperforms Direct by 0.41 percentage points in held-out Top-1, with a 95% CI of [0.09, 0.84]: four wins, four ties, and no losses.
  • Structured outperforms Raw by 0.105 percentage points, with a 95% CI of [0.006, 0.28].

The first comparison measures the additional benefit of incorporating structured history into the same LLM search. The second measures the further benefit of organizing the feedback. Together, they provide direct evidence of history’s contribution under matched conditions, beyond what comparisons with random search or GP-EI alone can establish.

Appendix E.6 further clarifies where this benefit occurs: Luna’s three modes select the same predictor on DTI, while Direct performs slightly better on the protein task. We therefore present history feedback as a component that can improve search on particular tasks, with gains that depend on the setting.

2. How should the 20-round, eight-seed results be weighed against the original 100-round protocol?

The two sets of experiments provide complementary evidence. The original 100-round experiments retain the main evaluation’s training conditions. The additional 20-round experiments allow us to run eight seeds and a more complete set of search controls, providing a fuller picture of the gains from history feedback and their variation across runs.

Using 20 rounds made it feasible to cover Direct, both history representations, random search, and GP-EI within the available computational budget. Within each experiment, all arms share the same proposal allowance, training schedule per valid candidate, and failure-accounting rules, supporting direct comparisons between search strategies. The follow-up studies also expand the benchmark or candidate library, so we use them to complement the original evaluation and interpret effect sizes within their respective protocols.

History and direct search are also compared at the original training budget (Table E.1). On Norman, Luna improves from 22.30% with Direct to 23.11% with history, a gain of 0.81 percentage points; other tasks include ties and a regression. The original comparison uses one frozen training seed per task, while the new eight-seed studies add evidence from repeated runs under their respective settings.

Together, these experiments clarify the value of collaborative training and provide paired evidence for the additional contribution of history feedback in specific settings. Thank you for encouraging these more targeted analyses. We hope the additions further strengthen your confidence in the paper’s contribution, and we would be grateful if you would reconsider your score in light of the strengthened evaluation and the direct evidence above.

Thank you to the authors for the detailed response and the effort put into the rebuttal. While the clarifications are helpful, my overall assessment of the paper remains largely unchanged. Therefore, I will maintain my original score.

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

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