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Under review as a conference paper at ICLR 2027

ReproBAIT: Can coding agents build their own biological AI tools?

Abstract

Large language models are increasingly competent at leveraging their scientific knowledge and existing computational tools to execute complex workflows. However, little information exists on their ability to build tools which are not readily available. We introduce an evaluation titled ReproBAIT (Reproducing Biological AI Tools) which focuses on measuring the ability of coding agents to design, implement and train biological AI tools from published research, across a range of information access conditions. The coding agent is securely sandboxed without internet access, then receives training data, a fixed time and compute budget, and limited information about the tool to replicate. We score the produced biological AI tool on tool-specific metrics over held-out data. We evaluate across a set of biological AI tools of varying complexities: ProteinMPNN, an inverse protein folding tool, RFdiffusion3, an all-atom generative diffusion tool, and a closed-source molecular design tool. We institute a methodology to check for memorisation, as the open source tools are likely to be included in the pretraining corpus. Across a range of leading closed- and open-source coding agents, we find promising reproduction capability for our selected tools. We find moderate evidence consistent with memorisation, varying across coding agents. These results suggest that tool developers may need to be increasingly vigilant about the information that they release publicly. Public information could undermine a tool’s commercial value or invalidate dual-use managed access strategies.

Primary area:
datasets and benchmarks
Keywords:
large language models, coding agents, capability evaluation, scientific tool reproduction, AI for biology, memorisation, AI safety

Reviews

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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_KpX3OpenReview ↗
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2(+1)
Confidence
3
Informativeness
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Paper summary

This paper introduces ReproBAIT, a benchmark for evaluating whether coding agents can reproduce biological AI tools from limited descriptions. The benchmark covers three tools with different levels of complexity and compares several coding agents under different information conditions. The results show that agents can reproduce some functions of simpler tools, while struggling with more complex ones. The paper also examines the possible effects of memorization and agent harnesses.

Critical strengths
  1. The benchmark includes both open-source and closed-source tools, providing different evaluation settings.
  2. The experiments consider information access, model complexity, and memorization, which helps explain the observed results.
  3. The evaluation environment is reasonably controlled, with fixed compute budgets and held-out test data.
Critical weaknesses
  1. Only three biological AI tools are evaluated. This is too small to support broad conclusions about the reproduction capabilities of coding agents.
  2. Each tool is mainly evaluated using one specific metric. Achieving a similar score does not necessarily mean that the original tool has been successfully reproduced.
  3. Some target tools may have appeared in the training data of the evaluated LLMs. Although the authors investigate this issue, the experiments cannot clearly separate memorization from actual reproduction ability.
  4. Different models use different agent harnesses, and the main results report the best of three attempts. This makes it difficult to compare the agents fairly and assess the stability of their performance.
  5. The main contribution is an evaluation framework based on existing coding agents and biological tools. The paper does not introduce a new agent method or learning algorithm.
Questions for authors
  1. Can the authors explain why only three tools were selected and whether the findings would hold for a larger set of biological AI tools?
  2. How can the benchmark distinguish genuine tool reproduction from achieving a high score on a limited evaluation metric?
  3. Can the authors provide stronger evidence that the results are not mainly influenced by memorization?
  4. Why are the best results from three attempts used instead of reporting mean performance with standard deviations?
  5. Can the authors provide more controlled comparisons using the same agent harness across different models?
1 comment

Thank you for the helpful feedback. We address each of your questions below:

1. Three tools and the benchmark contribution

We agree that only three tools cannot support conclusive statements about general BAIT reproducibility. We selected three illustrative use cases to gain initial insights into what is feasible and to guide future research. We revised the abstract (lines 20–23) and introduction (lines 97–99) to narrow the claims accordingly. We also expect this framework to be most interesting when applied to closed source tools.

We view a primary contribution of our paper as the framework itself, allowing a scalable approach to evaluate agentic capabilities for replicating biological AI tools—a task that has not, to our knowledge, been reported elsewhere in the literature. We note that the paper was submitted in the datasets and benchmarks track. We believe benchmark infrastructure for assessing emerging capabilities is a valuable contribution, consistent with other papers in this track, and will catalyze further investigation of these capabilities. Based on the results of the paper and our limited experimentation on further BAITs, we expect future runs will find further evidence of BAIT reproducibility across a range of biological functions.

2. Task scope and metrics

We acknowledge that a high score on a single metric does not establish that the original BAIT has been reproduced. Our primary metrics are deliberately narrow so that scoring can be automated and repeated.

We have revised the text to state each task's scope explicitly and have now added all calculated metrics per attempt in Appendix B. These provide additional context for any discrepancy between reproducing a specific functionality and reproducing the broader tool. For example, on RFdiffusion3 the highest designability scores come from attempts whose backbones are near-duplicates of known PDB entries, so the primary score alone would have been misleading. We highlight this in the results.

3. Memorisation evidence

We agree that our experiments cannot definitively separate memorisation from reproduction ability. Our transcript diagnostics detect evidence consistent with prior recall but cannot fully quantify its contribution. Our code similarity check can detect verbatim code regurgitation, but cannot detect rephrased implementations. However, we argue that the combination of the two checks provides a useful diagnostic signal for the overall memorisation of the given BAIT. Given the secrecy around training datasets for frontier models, we hope that future research will help shed light onto the effects of memorisation.

That said, we would like to emphasise that CMD’s training pipeline is closed-source, so there is no code for an agent to have memorised. Agents still match the published validity score. Further evidence to rule out memorization would involve the addition of further closed-source tools or those past the training-data cutoff of the evaluated model; but this is beyond the scope of the paper’s initial exploration.

4. Best-of-three

The best-of-three framing was intended to represent a motivated user who can retry several times and use a successful result (where success criteria are known in advance as they are here). However, we agree that this limited a full reading of the results distribution. We have updated the manuscript to report all three replicates with means and standard deviations for each task.

5. Harness comparisons

The original harnesses were included to correspond to practical usage for the evaluated models, but we agree this may have confounded the comparison between models. We now use the same ReAct harness across all four models and all three tasks.

The paper-only results under the common ReAct harness are shown below. Each cell gives mean fidelity (% of the task reference) ± sample SD over three attempts, each with a 12-hour allowance.

ModelProteinMPNNCMDRFdiffusion3
Claude Opus 5109.5 ± 2.9100.7 ± 0.722.8 ± 32.4
GPT-5.6 Sol90.5 ± 5.599.5 ± 0.199.6 ± 8.8†
Kimi K392.0 ± 9.699.2 ± 0.80.0 ± 0.0
Qwen3.8-2.4T76.7 ± 7.099.9 ± 0.218.2 ± 31.6
†All three runs were flagged for structure lookup.

We include a harness comparison in § 3.3 as evidence that ReAct does not appear to disadvantage the agents we tested on ProteinMPNN compared to the proprietary harnesses.

Reviewer_zeaROpenReview ↗
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2
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2
Informativeness
2
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2
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Paper summary

ReproBAIT tests whether coding agents can implement selected functionalities of biological AI tools under fixed resource budgets. Agents receive an abstract or full paper, training data, and task-specific infrastructure. Four agents attempt three tools three times in each information condition, giving 72 attempts. A separate scorer evaluates the submissions on held-out tests and reports performance relative to the reference tool's selected metric. Agents recover some functionalities well and perform much worse on the most demanding task. This paper also examines possible memorization, effects of the agent harness, and evaluation security.

Critical strengths

The benchmark evaluates submitted implementations on held-out tests, isolates the scorer from the agent, and checks the reference scoring pipeline. These are useful safeguards for measuring whether an agent has produced something that works. The reporting of failures, restricted functionality, and possible memorization also helps interpret the successes. The resulting scores also measure the submitted implementation's actual behavior.

Critical weaknesses
  1. A high fidelity score has a different meaning for each task. For example, CMD's primary metric is narrow and nearly saturated, ProteinMPNN uses relative sequence recovery, and RFD3 covers only restricted functionality. The paper discloses these limits, but the percentages are still easy to read as a common measure of how much of each tool has been reproduced. The primary metrics cover too little of each tool's capability to support that interpretation. The secondary outcomes matter here because they can show whether a high-scoring submission also retains meaningful quality within the stated task scope.
  2. CMD's complexity score is 25.7 in the main presentation and 51.9 in Appendix Table 8. This changes its ordering relative to ProteinMPNN and affects the complexity argument. The tasks also differ in their metrics, budgets, prior familiarity, and supporting components. With these factors varying together, the results can describe which tasks were harder for the agents, but do not isolate implementation complexity as the explanation.
Questions for authors
  1. Do the secondary outcomes from the existing runs agree with the conclusions drawn from primary fidelity, especially for the highest-scoring submissions? Which aspects of the original tool's quality are preserved or lost when an implementation matches the primary score?
  2. Section 2 allows unrestricted choices of model architecture and implementation. Section 3.1 partly explains some RFD3 failures by saying that the submissions did not train a full diffusion model. Were those submissions rejected because of output quality, because a particular model family was required, or both? What eligibility rule was specified before evaluation, and was it applied consistently?
  3. Appendix B gives CMD a complexity score of 25.7, whereas Tables 8 gives 51.9. Are these scores for different task scopes or different versions of the same assessment? Which score applies to the evaluated task, and how does it affect the complexity–performance conclusion?
  4. How sensitive are the reported costs per reproduction to the 75% fidelity cutoff? Do the cost rankings and the number of successful attempts change substantially with that cutoff, given that fidelity measures a different capability for each tool?
1 comment

Thank you for the specific questions, which we address below:

1. Secondary metrics

We agree that percentages should not be read as a complete measure of reproduction completeness. We additionally provide all secondary metrics in Appendix B. CMD uniqueness is 96.9-99.6% and novelty is 80.7-96.3%, which addresses repetition and overfitting to the training distribution. ProteinMPNN perplexity improves alongside recovery, with comparable scores to the open-weights checkpoint. These metrics support that high-scoring submissions generate diverse, novel outputs rather than trivial solutions.

However, for RFdiffusion3, we note that the highest designability scores were associated with high rates of known PDB structures, which is more aligned with look-ups rather than genuine function reproduction. We clearly flag this in Table 9 and Figure 3e. They also reveal a more subtle failure mode, as Opus 5 and Qwen3.8-2.4T produce tools where the secondary structure distributions are far from those of the original tool and natural proteins. For these, we report the scores as given and comment in § 3.1.

2. Architecture and eligibility criteria

The coding agent’s architecture choice is unrestricted, and we have removed any wording that implied otherwise. No attempts are excluded based on architecture.

For RFdiffusion3, we set a predetermined threshold of TM-score ≥ 0.95 on produced protein backbones to identify lookups of known PDB structures. This was triggered by all GPT-5.6 Sol attempts but did not affect reporting: we report all raw scores in appendix B, with corresponding lookups appropriately flagged as context.

3. CMD complexity

Thanks for spotting this inconsistency. The revised CMD score is 25.7 throughout, scoped specifically to the initial LSTM/SMILES generator rather than the entire tool. Appendix D documents the complexity grading approach and we have corrected the inconsistent 51.9 presentation. There is no change to the complexity–performance relationship put forward in the initial presentation.

4. Cost reporting

The cost-per-replication metric was not particularly sensitive to changes in the threshold across a range of cutoffs, and was intended only as a directional approach to anchor costs on a simple basis. We agree that the choice of a 75% fidelity cutoff can affect the estimated cost per successful replication. We therefore replaced this measure with mean cost per attempt in Figure 3b and Appendix C. This reports the cost of running an agent without requiring a success threshold.

Reviewer_wQjROpenReview ↗
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2
Confidence
2
Informativeness
2
Presentation
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2
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Paper summary

ReproBAIT evaluates whether coding agents can implement and train biological AI tools under restricted information access and fixed computational budgets. The benchmark includes three tasks derived from ProteinMPNN, RFdiffusion3, and an anonymized closed-source molecular design tool. Agents receive training resources and either an abstract or the full paper, while submissions are evaluated in a separate environment using task-specific functional metrics. The study also includes exploratory source-code and agent-harness comparisons, together with transcript-based and code-overlap diagnostics for memorization.

The strongest agents approach the released ProteinMPNN model’s sequence recovery and match the published molecular-validity score for the closed-source task. RFdiffusion3-derived backbone generation is substantially harder under the tested budget. These results provide an interesting snapshot of agents’ ability to reconstruct selected scientific functionalities, although the definition of successful reproduction and the interpretation of information-access effects need strengthening.

Critical strengths

A relevant evaluation of executable scientific-tool construction. The benchmark asks agents to deliver working code and trained models, rather than merely describe a method or reproduce textual answers. Fixed resource budgets, held-out evaluation data, and separation of agent and scorer environments provide a useful foundation for assessing this capability. Running the released ProteinMPNN and RFdiffusion3 checkpoints through the same scoring pipeline also helps anchor the results.

The analysis explicitly examines several important failure modes. The paper investigates prior memorization through complementary transcript and source-overlap diagnostics, identifies submissions that return near-duplicates of known structures, and reports substantial variation across attempts. It also acknowledges that matching one metric does not establish complete tool equivalence and that memorization diagnostics cannot determine the causal contribution of prior exposure. These qualifications make the study more informative than a simple leaderboard.

Critical weaknesses

The benchmark’s success criteria do not consistently capture the capability being claimed. For CMD, the primary metric is RDKit validity, which is necessary but insufficient to establish reproduction of the broader molecular-design tool. The manuscript defines uniqueness and novelty as secondary checks but does not provide the corresponding per-agent results needed to assess the quality of the purported reproductions. For RFdiffusion3, evaluation covers only unconditional monomer backbone designability, excluding its conditional and all-atom capabilities. More importantly, Section 2 explicitly permits alternative architectures, yet the high-scoring Claude submission is classified as only partially successful partly because it implements a simpler diffusion model rather than attempting to recreate RFdiffusion3 “in earnest.” Rejecting retrieval-based submissions can be justified by explicit novelty requirements, but simplicity of architecture alone conflicts with the stated functional evaluation principle. The benchmark needs predefined, uniformly applied criteria separating valid alternative implementations, restricted-distribution generators, and degenerate solutions. Otherwise, the headline conclusion that no RFdiffusion3 reproduction succeeds depends partly on discretionary adjudication.

The design does not isolate the effects of information disclosure or implementation complexity. Only three tools are evaluated, with task domain, prior exposure, training requirements, and available resources varying together. The open-source tools may have been encountered during pretraining, while the sole closed-source example is evaluated using a saturated validity metric and cannot be rerun through the same scorer. Transcript and code-overlap diagnostics are useful observations, but cannot establish how much performance depends on supplied information rather than previously learned implementation details. Similarly, RFdiffusion3 failures within 12 hours on one A10G may reflect insufficient training resources as well as implementation difficulty; the exploratory with-code runs do not provide a reliable compute-matched reference. The authors acknowledge many of these limitations, but the commercial and managed-access implications remain stronger than the evidence directly establishes. The supported conclusion is narrower: agents can recover selected functionalities of familiar tools when substantial training resources are already supplied.

Questions for authors

What explicit criteria distinguish full success, partial success, and invalid submissions? Were these criteria fixed before inspecting results, and how are they reconciled with the allowance for arbitrary architectures? Please report raw functional scores and qualification outcomes separately.

Can you report the secondary metrics for every submission, particularly CMD uniqueness and novelty, ProteinMPNN perplexity, and RFdiffusion3 structural novelty and lookup fraction? For CMD, what anonymized task specification, data documentation, and evaluation artifacts can be released to permit independent verification?

What performance can a validated reference implementation achieve when trained under the same data, hardware, and time constraints? This would help separate limitations in agent implementation from limitations imposed by the training budget.

Please reconcile the CMD complexity scores of 25.7 and 51.9 and clarify whether complexity ratings consistently describe the restricted benchmark tasks or the complete original tools. Given only three evaluated tasks, how much of the complexity-based interpretation remains supported after this correction?

1 comment

Thank you for the constructive review. We address each point below:

1. Criteria for identifying success

We agree that only assessing single outcomes is insufficient to establish full reproduction of a BAIT. However, we are intending to measure whether coding agents can produce a tool that successfully reproduces a key function of the original BAIT. This alone has significant implications for protecting BAITs: users may only need a specific capability. In this first demonstration of the benchmark, we did not prespecify criteria for success. Instead, we report reproduction fidelity as a percentage of the original tool’s performance. For RFdiffusion3, we did prespecify a threshold of TM-score ≥ 0.95 to identify potential lookup from known PDB structures; this threshold was met by all GPT-5.6 Sol attempts on RFdiffusion3. This threshold was intended to separate cases of true reproduction against look-ups, not to reject any attempts.

We have now removed the 75% success threshold previously used in Figure 3b, along with the “partial success” wording in § 3.1, to avoid implying hard cut-offs for success. Architectural choices remain unrestricted per § 2. Our comments about 'simpler diffusion model' or 'did not attempt to recreate RFD3 in earnest' were observations about why we believe quality was low (e.g., scope narrowing to easier distributions).

Now that we have initial evidence of performance on the benchmark, we agree that prespecifying clear success thresholds would be valuable for future evaluations. We have recommended this in the discussion.

2. Secondary metrics

We now provide all secondary metrics in Appendix B, which support the replication fidelity of CMD and ProteinMPNN. CMD uniqueness is 96.9-99.6% and novelty is 80.7-96.3%, suggesting low rate of repetition and/or overfitting to training. ProteinMPNN perplexity improves alongside recovery, with comparable scores to the open-weights checkpoint at 4.047. These secondary metrics confirm that high-scoring submissions generate diverse, novel outputs rather than trivial solutions.

For RFdiffusion3, we conduct further analysis on the produced structures. The highest designability scores were associated with high rates of known PDB structures, which is more aligned with look-ups rather than genuine reproduction. We clearly flag this in Table 9 and Figure 3e. They also reveal a subtle failure mode, as Opus 5 and Qwen3.8-2.4T produce tools where the secondary structure distributions are far from those of the original tool and natural proteins. For these, we report the scores as given and comment in the results and discussion.

For CMD metrics, Appendix A now describes the anonymised task, corpus, the requested sample count, and the scoring definitions. However, CMD remains anonymised for commercial and legal sensitivity.

3. Validated reference implementation

We ran the released training code under the same 12-hour allowance on one A10G (§ 3.1). ProteinMPNN reached 89% of published performance, suggesting budget was not a limiting factor on agent performance. For RFdiffusion3, the open-source training run remained at 0% designability.

However, we ran the released code as published, without tuning its hyperparameters for a much shorter training run. We do not read this as proof that RFdiffusion3 is infeasible within the budget, just that we have not demonstrated feasibility. As a countervailing piece of evidence, we view the non-zero performance by some agents as evidence that the task, while difficult, is still tractable and can discriminate agent performance. We acknowledge in the text that this may confound the agents' limitations with those imposed by the budget's.

4. CMD complexity

Thank you for spotting this inconsistency. The revised CMD score is 25.7 throughout, scoped specifically to the initial LSTM/SMILES generator rather than the entire tool; we have removed the inconsistent 51.9 presentation. Appendix D documents the complexity grading approach in detail.

From our three tasks, we see some evidence of a moderate negative relationship between complexity and agent performance. We do not claim complexity as the sole cause of performance differences, and include it as a descriptive indicator of task difficulty. We leave a more rigorous treatment of complexity to future work, which would require a much larger number of BAITs. We have moderated our claims in the text accordingly.

5. Information access and memorisation

We acknowledge this limitation. We select three illustrative use cases to demonstrate the benchmark’s feasibility. We expect the benchmark to provide the most signal when tested on closed source tools so we decided not to include a wide array of open source tools. We varied the information supplied to agents during evaluation, but prior exposure during pretraining is out of our control and limits what we can infer about the effect of disclosure. We leave these questions to future controlled studies.

Comments on the paper

1 comment

We thank the reviewers for their constructive feedback. We have now re-run the main comparison under consistent experimental conditions, expanded the metrics we report per attempt, and clarified ReproBAIT's contribution as an extensible benchmark, demonstrated here on three representative biological tasks, not a full account of BAIT reproducibility.

To summarise our revisions:

  • We evaluate on a consistent ReAct harness for 12 hours on one A10G GPU across all four models and all three tasks. Instead of reporting only the best result per run, we report all three scored attempts per configuration, and mean and sample standard deviation, detailed in Table 2.
  • We further report all calculated metrics for each attempt in Appendix B. For ProteinMPNN, we report perplexity; for CMD, we report uniqueness, novelty, and ChemNet-distance; and for RFdiffusion3, we report various structural metrics.
  • We test the open-source training code for ProteinMPNN and RFdiffusion3, under the same 12 GPU-hour budget (§ 2.2). This replaces our earlier exploratory with-code comparisons.
  • Figure 3b removes the threshold for success and instead reports cost-per-attempt, so that cost comparisons can be made across differing levels of success. Appendix C reports all relevant cost data.
  • CMD’s complexity score is now reported consistently as 25.7, correcting a discrepancy with the rating for the specific molecular generator we actually evaluate.
  • We have clarified the allowance for alternative architectures, and report scores separately from diagnostic checks (§ 2).

Changes in the revised manuscript are highlighted in blue.

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

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