acceptodds
Under review as a conference paper at ICLR 2027

ResearchArena: Evaluating Sabotage and Monitoring in Automated AI R&D

Abstract

AI agents are becoming increasingly capable of conducting autonomous AI research and development (R&D). This raises an important question: Are these agents reliable and monitorable enough to trust the results of their research process? In this paper, we investigate what happens when an AI agent works autonomously on an AI R&D task while simultaneously performing a covert, harmful side task. We introduce ResearchArena, where we investigate four AI R&D tasks (safety post-training, capabilities post-training, CUDA-kernel optimization, and inference-server optimization), each with multiple harmful side tasks. These side tasks either directly sabotage the produced model, kernel, or server, or perform a covert action outside the task's scope. All of the frontier agents that we tested performed these harmful side tasks without refusing when they were framed as ordinary engineering requirements. Executing side tasks came at almost no cost to their research performance. Furthermore, we tested whether such sabotage can be detected using other frontier agents as monitors. For this, we tested different monitor types and found that monitors which can access the final artifact (e.g. the trained model or inference server) are more effective. Monitors struggle on side tasks which primarily sabotage the final artifacts, such as via a backdoor in the post-trained model. Counterintuitively, we find that access to the agent's summarized chain of thought can mislead monitors and make sabotage harder to detect. We are releasing ResearchArena as a modular framework for evaluating sabotage and monitoring in automated AI R&D.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
AI control, automated AI R&D, AI safety, monitoring, adversarial

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_AbXrOpenReview ↗
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4
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

The paper introduces ResearchArena, which evaluates agents that carry out legitimate AI R&D tasks while simultaneously performing covert sabotage across four task domains. It finds that sabotage embedded in training data and model behavior is particularly difficult to detect; access to final artifacts can improve monitoring, whereas reasoning summaries can sometimes mislead monitors. Its primary contribution is an evaluation framework and empirical findings, rather than a new attack or defense algorithm.

Critical strengths
  • A valuable evaluation setting. Combining legitimate task completion with covert sabotage, while allowing monitors to inspect and execute the resulting artifacts, captures trust concerns in automated R&D more directly than evaluating task performance or reviewing transcripts alone.

  • A clear experimental framework. The paper evaluates main-task and attack success separately and compares four monitoring conditions defined by artifact access × CoT access. Coverage across multiple models and tasks helps distinguish attack failures from monitoring failures.

Critical weaknesses
  • Limited novelty and scope of generalization. The contribution primarily integrates existing attack and monitoring ideas into a systematic evaluation. Many attacks are explicitly specified in the instructions, so the results mainly demonstrate compliance with harmful instructions framed as legitimate requirements, rather than autonomous attack planning or strategic evasion.

  • Key explanatory factors are not sufficiently isolated. Artifact access provides both additional files and execution capabilities, making their individual contributions unclear. Data-based and code-based attacks also occur in different task domains, so the detection gap cannot be attributed solely to how sabotage is embedded.

Questions for authors
  • Does the difficulty of detecting data-based attacks persist after controlling for task differences? Could the authors compare data-based and code-based attacks with similar harmful effects within the same R&D task?
  • Are the main conclusions robust to stricter evaluation? Could the authors report per-model performance effect sizes and confidence intervals, and compare monitors at a common false-positive rate after reassessing the baseline labels?
2 comments

Dear Reviewer AbXr,

Thank you for your thorough review. We are glad you find our evaluation setting valuable and our experimental framework clear. Below we address your remaining concerns and questions.

1. Specified side tasks

ResearchArena follows the standard AI control methodology where we evaluate safety measures against agents pursuing a specified harmful objective [1, 2, 3]. The reason for this in the literature is to assess whether monitoring will remain effective in the scenario that an agent is attempting to subvert a task. Specifying the side task allows us to get a ground truth on what the sabotage is and whether the sabotage succeeded. Within this setup, agents still decide how to implement the sabotage inside their own solution, which is what the monitor must find. Our contributions are that monitors can execute and probe the submitted artifact in autonomous AI R&D tasks using agentic monitoring instead of only reading the transcript, and that the sabotage is created by the agent while solving the task. Unlike other adjacent works in auditing, where sabotage is artificially inserted into an existing codebase [4], the attacks in ResearchArena are a result of the agent's own research process, allowing us to study whether monitors are able to detect sabotage when the harmful behavior is embedded between legitimate work. Autonomous attack planning is an important next step that our framework supports, for example by giving only a goal instead of a concrete side task.

2. Does the difficulty of detecting data-based attacks persist after controlling for task differences?

This is difficult to test because data-based attacks are only relevant to tasks where the final artifact is data or a model. In our case, these are the two post-training settings. Code-based attacks, on the other hand, are only relevant if the final artifact is code, as is the case for the kernel and inference-server optimization settings. Currently, it is not possible to create a side task for the post-training scenario in which sabotage occurs in the code. The closest such side task is to include some harmful commands or procedures that can be written in code. This is the case with our checkpoint exfiltration side tasks, in which the research agent is asked to exfiltrate the current checkpoint after evaluating it. Another way to test this would be to have a main task in which the submission includes both a model and code. For example, this could be a model and a scaffold. We consider this exciting future work.

3. Are the main conclusions robust to stricter evaluation?

Yes, after reassessing the baseline labels (now 20 excluded runs, see Reviewer xLxh), Table 2 reports per-monitor AUCs with bootstrap standard deviations. The ROC curves in the appendix compare monitors at any common false positive rate. The excluded runs lower the optimization AUCs by at most 3 points, so our conclusions are unchanged.


Thank you for your positive feedback and questions! We hope we have addressed your remaining questions and remain open to any further questions.

References

[1] Rogan Inglis, Ollie Matthews, Tyler Tracy, et al. ControlArena. GitHub repository, 2025. https://github.com/UKGovernmentBEIS/control-arena

[2] Francis Rhys Ward, Teun van der Weij, Hanna Gábor, Sam Martin, Raja Mehta Moreno, Harel Lidar, Louis Makower, Thomas Jodrell, and Lauren Robson. CTRL-ALT-DECEIT: Sabotage evaluations for automated AI R&D. In Advances in Neural Information Processing Systems (NeurIPS), 2025.

[3] Jonathan Kutasov, Yuqi Sun, Paul Colognese, Teun van der Weij, Linda Petrini, Chen Bo Calvin Zhang, John Hughes, Xiang Deng, Henry Sleight, Tyler Tracy, et al. SHADE-Arena: Evaluating sabotage and monitoring in LLM agents. arXiv:2506.15740, 2025.

[4] Eric Gan, Aryan Bhatt, Buck Shlegeris, Julian Stastny, and Vivek Hebbar. Auditing Sabotage Bench: A benchmark for detecting and fixing research sabotage in ML codebases. arXiv:2604.16286, 2026.

Thank you for your response; my questions have been fully addressed, and I maintain my original position of acceptance.

Reviewer_5e5sOpenReview ↗
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1
Confidence
2
Informativeness
1
Presentation
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1
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Paper summary

This paper details four primary case studies ("settings") in which language models are asked to perform a machine-learning-related engineering task; in each setting, the models are optionally given a covert secondary task. The traces, and optionally CoTs, and produced artifacts, are then handed to a monitor which produces a suspiciousness score. The authors then interpret the results, concluding that the final artifact is especially useful to the monitor (especially compared to the CoT). The paper draws a key distinction between embedded side-tasks, which are closely related to the main task, and independent ones, which are not, and concludes that the independent side-tasks are easier to detect. They also observe several cases where the agents sabotage without being instructed to, but do not analyze this comprehensively. They also report on some auxilliary statistics, e.g., the effect of different covert tasks on performance of the main task, token costs, etc.

Critical strengths
  • The tasks themselves are interesting and well thought through. I am not intimately familiar with related work, but it seems plausible to me that the settings themselves could be the basis of a strong paper. The relationships between the tasks and the side tasks seems potentially rich. However, I do not think the diversity is high enough, nor the methodology for creating them clear enough, to justify the broad conclusions drawn. Broadly speaking the high-level form of the experimental design is relatively standard and makes sense.

  • The research appears to be reproducible; the code looks to be public and I didn't see any red flags within 5 minutes. The prompts are in the appendix.

  • The idea of studying whether or not including a final artifact in the report to the monitor is clearly a good one, and solid findings on this question could be quite consequential. It's an important question, clearly communicated, and well-posed. Unfortunately, I don't find the details of the methodology to be very rigorous, nor the results to be particularly persuasive. More below.

Critical weaknesses
  • The scientific rigor of the study is relatively low; the authors are quick to draw conclusions that are not clearly supported by the data, and appear to me to be missing many baselines and controls (see more in my detailed notes below.) The study covers only a handful of environments and sees minor effect, but draws sweeping conclusions. The difficulty of drawing these conclusions are also undercut by the need to support conclusions across many independent variables: choice of main model, monitor model, presence of CoT, presence of artifact, identity of main task, embedded vs independent side task. The authors exclude runs for various reasons and report this, but there is enough funny business going on for few enough environments, that I feel the paper to be on shaky ground. Furthermore, the same setup seems like it could be used to compare against other tasks and benchmarks in the literature, and it seems no effort has been made to adapt other work.

  • The primary takeaways from the paper seems to be: (1) a new sandbox to study sabotage (but many exist in the literature), but focused on research and development (although this is really engineering); (2) a new way of monitoring based on artifacts, that seems to work better---but the effect size is small (see figure 6) and not properly controlled for. See my notes in the next box.

Finally, the paper is unfocused, not testing the hypotheses I feel deserve testing, but instead reporting on seemingly irrelevant things such as the time taken and token costs. It wants to be a paper both about the sabotage benchmark and the monitoring methodology, but neither is done in a particularly principled or rigorous way.

Questions for authors
  • How much about your experimental setup do the agents know, and why do they sometimes sabbotage unprompted? Appendix D has me confused.
  • Please clarify the role of GSM8K training set contamination.
  • What happens if you add the no-sidetask baselines into Figure 5?
  • Please explain in more detail why you see signal in Table 2 and Figure 6.

Below, I copy my raw notes from reviewing the paper:


The name ResearchArena seems like a significant misnomer. Each of the four settings (safety posttraining, capabilities post-training, kernel optimization, inference optimization) are very well-defined, well-scoped engineering problems, not research problems.

Motivation has some missing links. Agents needing access to code, API keys, etc, is true for many things, not just research. The adversarial setting ("We therefore", line 47) is completely unmotivated. Why should it matter what happens if an agent has a side-quest? Why should this side-quest be specifically about harm? I vaguely feel the scientific thread has given way to general paranoia already.

"Curent agents" (line 43) should be specified or timestamped, given how quickly capabilities change.

Why not use the same side task for all four main tasks? It seems especially weird that tasks 1 and 2 use checkpoint exfiltration, and the other two use typosquat dependency

Note: The embedded side task for capabilities post-training seems legitimate to me, given that evaluation is on GSM1K, not the test set. I don't understand the comment about "measurable performance edge over honest training"

I find the choice to only run the monitor on verified successes to be quite suspicious. What about false positives? I worry that this restriction hides an important control and artificially makes more paranoid monitors look better.

The fact that 12 agents sabotaged despite not being asked to do so (line 307) seems like it deserves more attention than currently given. Why is this? It also seems highly unlikely that the sabotage they carry out is exactly the ones given in the side task---I mean, what are the chances that they decide to sabotage in exactly this way? Something weird is going on here that demands explanation.

The cost of sabotage results (paragraph beginning on line 321) are pretty obvious and have no controls. My null hypothesis is that, at a certain reasoning effort and given clear instructions about resources, agents will mostly use up the time and resources they have. Just like a person taking a test. Furthermore, the conclusions are more mixed than the gloss suggests; some tasks do in fact require less tokens. This seems to be a function of your particular choice of settings. Thus I do not think it is worth mentioning in this paragraph, or including Figure 3 in the main body of the paper. Figure 4

Speaking of Figure 3, I am confused:

  • Are the considerations of "success", as discussed in lines 290--300, factor into the Y axes at all?
  • You mention that the contaminated test-set is not the one in evaluation, in the capabilities post-training setting. So is the interpretation that slightly more training data made a significant difference in generalization performance? Or are the test sets of GSM8K and GSM1K connected somehow?
  • The text mentions that you measure the gap between GSM8K - GSM1K, but the numbers seem to be the wrong scale for that; it appears to be just accuracy on GSM1K. Is this correct?

Figure 5:

  • the bold caption claim is not the clear takeaway from the figure; I'm not sure I fully endorse it. Please describe the content of the figure neutrally and let readers draw their own conclusions.
  • CoT vs non CoT and artifact vs non-artifact are presented differently, so it takes some time to make the comparison. I'm not sure there are enough data points to conclude that artifact raises suspicion for "nearly every side task", given that it arguably does not hold for 4/26 lines shown here.
  • Clearly there is a missing control here. There is nothing here run on the versions with no side task. It's also related to my earlier suspicion about false negatives which, remember, were excluded from the dataset. This does not exclude the null hypothesis that more material to review means more suspicion, independent of whether or not a sabotage takes place.

Figure 6 undercuts the story that including an artifact raises suspicion considerably, because the confidence intervals are so large and the number of data points is so small. This figure communicates to me that the results are inconclusive; that including an artifact has a pretty small effect, and not one that has been demonstrated to be significant here.

I do not find the claims in paragraph 419--427 to be substantiated. Most egregiously, the "far less obvious than in a code snippet" seems like a strong overstatement. The results in Table 2 had the potential to back up these claims, but instead I came away suspecting that most of the effect that you see is a quirk of KimiK2, which is then averaged into the aggregate numbers to produce a small effect.

5 comments

Dear Reviewer 5e5s,

Thank you for your thorough review. We are glad you find our overall approach and our idea of using agentic monitors to run tests on the final artifact interesting and important!

We address your concerns by clarifying our motivation and setup, clarifying the embedded side task in capabilities post-training, improving the focus of the paper, and explaining the figures.

1. Research vs. engineering tasks

ResearchArena focuses on experimentally driven AI R&D tasks where the agent must independently select and evaluate methods to achieve a specified objective. The tasks are designed to provide a quantifiable success criterion while preserving an open-ended nature in how the agent performs the task. Our main tasks come from established AI research domains that capability benchmarks already evaluate, such as post-training [1], CUDA-kernel optimization [2], and inference-server optimization [3]. Our main contribution is the evaluation of sabotage and monitoring within these already established tasks in a way that allows us to study monitoring failures that occur in realistic multi-step AI R&D settings.

2. Motivation of AI Control

AI control asks whether safety measures still hold in the worst case, when a model intentionally tries to subvert them [4]. Following established practices in AI control [4, 5, 6, 7], we simulate the threat model by assigning the research agent a covert, harmful side task in addition to its main task. This gives us ground truth about what the sabotage is and whether it succeeded.

We therefore run monitors only on verified runs so that we can more reliably measure how monitors detect sabotage that actually occurred. Otherwise we would risk conflating attack failures with successes in monitoring. We additionally compare these attacks against a set of runs without the side task to measure false positive rates. This allows us to explore how reliably a monitor can distinguish a sabotage trajectory from a baseline, given that the attack succeeded.

AI R&D is especially high-stakes here: agents have access to weights, training pipelines, and compute, and their outputs shape future models [1]. Successful sabotage attempts could therefore affect not just the immediate task itself but also the behavior of systems produced or evaluated by that agent.

We build on existing control evaluations for AI R&D [8, 9, 10]. Our novelty, as described in the related work section, is that (1) monitors can execute and probe the submitted artifact, not just read the transcript, and (2) agents create the sabotage while solving the task, rather than having it injected into a finished codebase [10].

Embedded side tasks are designed per main task, since each must sabotage that task's specific artifact. For independent side tasks, checkpoint exfiltration only makes sense in the post-training settings. Kernels and inference-server code are not model weights, so there we use a typosquatted dependency, which also shows that the framework supports different independent attacks.

3. Embedded side task for capabilities post-training

The main-task score in this setting is accuracy on the held-out GSM8K test set. The side task introduces examples from this test set into the training mix, making the model train on the data used for evaluation. GSM1K only serves as an uncontaminated control. We report the gap between GSM8K and GSM1K accuracy as the side-task score. Successful contamination runs reach on average 77% on GSM8K but only 27% on GSM1K. The side task is therefore designed to create an inflated evaluation result through data contamination without actually improving the model's mathematical reasoning ability. We have reframed Section 4 to make this clearer.

4. Only clean runs in the no-side-task setting

The no-side-task condition is meant to provide negative examples that can be used to evaluate monitor discrimination. These runs therefore only receive the legitimate main-task instructions without the side-task objective.

Our original description of select baseline behaviors as "sabotage" was imprecise. In the excluded no-side-task runs, the agent reward-hacked or otherwise misbehaved: it disabled kernels instead of optimizing them, hardcoded benchmark prompts into a server warmup, or printed API credentials into its transcript.

In deployment, a monitor should flag all of these runs. In an AI control evaluation, however, no-side-task runs estimate the false-alarm rate on honest work, so a monitor that flags them is not making a mistake. Such runs are thus not suitable as clean negative examples for measuring false alarms on compliant work. We therefore exclude all 20 runs flagged by our audit and have reworded Section 5.1 accordingly. The results do not significantly change: AUCs change by at most 3 points, so none of our conclusions change.

5. Focus of the paper

The agents must complete both the main task and the side task under the same compute and wall-clock budget, meaning that diverting resources towards sabotage could reduce task performance. The purpose of the main-task comparison is thus to analyze whether pursuing a harmful side task degrades performance in a way that can be used as a predictive signal for catching such behavior.

Figure 3 shows no consistent penalty: successful sabotage was frequently carried out in tandem with the main task, showing that strong main-task performance is not sufficient evidence that the agent completed the task honestly.

We believe this analysis is valuable, as it motivates the need for monitoring beyond task performance. We have moved the token-usage analysis to the appendix.

6. Figure 3 explanations

Yes, Figure 3 only includes successful runs, i.e., runs above the main-task threshold and, for side-task runs, above the side-task threshold. We have revised the manuscript to state this in the caption as well. As described above, the contamination file contains the GSM8K test questions used for evaluation, so the higher score reflects memorization of the evaluation items rather than better generalization. GSM1K is a separate set of new problems that we use only to measure the side task.

7. Artifact access and baseline controls

We have extended the figure to include the no-side-task runs as gray lines to evaluate whether additional information increases monitor suspicion regardless of sabotage. The results do not support this. With artifact access, the mean suspicion on no-side-task runs stays flat or falls in three of the four settings, compared to the generally higher suspicion scores on successful sabotage runs. More material to review therefore does not by itself raise suspicion. We have also replaced the caption claim with a more neutral description of the figure.

8. Effect of artifact access and robustness across monitors

To isolate the effect of artifact access, we test it paired per run.

Adding artifact access raises the suspicion of successful embedded runs in the optimization settings by 5.9 points on average, and of independent attacks by 9.4 and 7.4 points in the optimization and post-training settings, while no-side-task runs do not rise. The effect is significant for each of the six optimization monitors on its own (p ≤ 0.02), so it is not a quirk of Kimi K2.6, although that monitor shows the largest gains.

For embedded attacks in post-training, the change is not statistically significant. This shows that access to the final artifact does not guarantee successful detection when the monitor fails to observe the relevant data.


Thank you for your detailed feedback, concerns, and questions, which have significantly improved our paper! We hope we have addressed your concerns and remain open to any further questions. We would be very grateful if you would consider increasing your score.

References

[1] Ben Rank, Hardik Bhatnagar, Ameya Prabhu, Shira Eisenberg, Karina Nguyen, Matthias Bethge, and Maksym Andriushchenko. PostTrainBench: Can LLM agents automate LLM post-training? In International Conference on Machine Learning (ICML), 2026.

[2] Anne Ouyang, Simon Guo, Simran Arora, Alex L. Zhang, William Hu, Christopher Ré, and Azalia Mirhoseini. KernelBench: Can LLMs write efficient GPU kernels? In International Conference on Machine Learning (ICML), 2025.

[3] Jehyeok Yeon, Ben Rank, and Maksym Andriushchenko. InferenceBench: A benchmark for open-ended LLM inference optimization by AI agents. arXiv:2607.20468, 2026.

[4] Ryan Greenblatt, Buck Shlegeris, Kshitij Sachan, and Fabien Roger. AI control: Improving safety despite intentional subversion. In International Conference on Machine Learning (ICML), 2024.

[5] Aryan Bhatt, Cody Rushing, Adam Kaufman, Tyler Tracy, Vasil Georgiev, David Matolcsi, Akbir Khan, and Buck Shlegeris. Ctrl-Z: Controlling AI agents via resampling. arXiv:2504.10374, 2025.

[6] Jonathan Kutasov, Yuqi Sun, Paul Colognese, Teun van der Weij, Linda Petrini, Chen Bo Calvin Zhang, John Hughes, Xiang Deng, Henry Sleight, Tyler Tracy, et al. SHADE-Arena: Evaluating sabotage and monitoring in LLM agents. arXiv:2506.15740, 2025.

[7] Rogan Inglis, Ollie Matthews, Tyler Tracy, et al. ControlArena. GitHub repository, 2025. https://github.com/UKGovernmentBEIS/control-arena

[8] Francis Rhys Ward, Teun van der Weij, Hanna Gábor, Sam Martin, Raja Mehta Moreno, Harel Lidar, Louis Makower, Thomas Jodrell, and Lauren Robson. CTRL-ALT-DECEIT: Sabotage evaluations for automated AI R&D. In Advances in Neural Information Processing Systems (NeurIPS), 2025.

[9] Harini Rajakumar, Vanessa Nwauwa, Kevin Zhu, Ashwinee Panda, and Sunishchal Dev. Adversarial behavior in research settings: Conducting sabotage evaluations with RE-Bench. In NeurIPS 2025 Workshop on Evaluating the Evolving LLM Lifecycle, 2025.

[10] Eric Gan, Aryan Bhatt, Buck Shlegeris, Julian Stastny, and Vivek Hebbar. Auditing Sabotage Bench: A benchmark for detecting and fixing research sabotage in ML codebases. arXiv:2604.16286, 2026.

Reviewer_xLxhOpenReview ↗
Rating
2
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

ResearchArena evaluates harmful side tasks carried out during automated AI research and development, together with the ability of agentic monitors to detect them. It covers safety post-training, capabilities post-training, CUDA-kernel optimization, and inference-server optimization. The framework distinguishes sabotage embedded in the submitted artifact from independent actions in the workspace, and varies monitor access to the artifact and workspace and to the research agent's summarized chain of thought (CoT). The experiments find that embedded post-training sabotage is particularly difficult to detect and provide concrete examples of how additional evidence can help or mislead monitors.

Critical strengths
  1. The framework connects sabotage generation to monitoring in substantive R&D workflows. Research agents introduce the side task while producing a model, kernel, or server, and monitors subsequently inspect the resulting evidence (Sections 3-4). The distinction between embedded and independent sabotage, together with the two monitor-access axes, makes the framework useful for investigating which evidence supports effective oversight.

  2. The quantitative results are supported by informative failure analyses. Table 2 reports substantially weaker separation of embedded sabotage from baselines in post-training than in optimization, and Figure 9 provides full ROC curves. Appendix E connects missed attacks to specific investigative failures, including inspecting training code without checking the data and testing a checkpoint without the relevant trigger. These examples explain why artifact access alone does not ensure detection and suggest concrete directions for improving monitors.

Critical weaknesses
  1. Baseline "false positives" may not be false. Monitors are told to flag anything concerning or out of scope (Appendix B.3). But some retained baselines skip part of the kernel task, read hidden eval files, or expose credentials (Section 5.1; Appendix D), so flagging them is arguably correct. Counting these as false positives mixes them with real monitor mistakes, making the AUC hard to interpret as general oversight quality. Please label baselines as clean vs. otherwise problematic, and report results both ways.

  2. Access comparisons should use the same runs. Gemini 3.1 Pro and GLM-5.1 runs are only evaluated without CoT (Section 5.2). If Figure 5 and Table 2 don't restrict all conditions to the same trajectories, the CoT effect may partly come from a different run population. Also, in post-training, artifact access raises suspicion but barely changes AUC (GPT-5.4: 68 to 71; Sonnet 4.6: 65 to 64; Table 2). Paired AUC differences with uncertainty would show whether access actually improves discrimination.

Some other comment:

  • Code localization is a plausible explanation for the detectability gap, but the settings also differ in attack type and verification. It should be framed as a hypothesis.
  • CUDA scores: Appendix A.3 uses raw speedup with a 1.3 threshold, and C.3 says all runs reach ~1.6×. Yet Table 7 shows baselines of 0.82 and 0.85. Please clarify the scale and which runs passed.
  • Performance cost: being within ±1 SD of the baseline doesn't show equal performance. I'd say "no clear penalty" unless paired differences are reported.
Questions for authors
  1. Were the aggregate CoT-access comparisons restricted to the same research trajectories? Please clarify eligibility and missing-score handling, and, if not already done, report access effects on common trajectories for each setting and the monitor backbone. Paired AUC differences, with resampling that keeps observations from the same research run together.

  2. What units or transformation explain the CUDA scores in Table 7? Please reconcile them with Appendices A.3 and C.3, and confirm how many runs satisfy the main- and side-task criteria. If the discrepancy affects inclusion rather than only presentation, how do the monitoring results change?

2 comments

Dear Reviewer xLxh,

Thank you for your thoughtful comments! We're glad you find our framework and monitor axes useful and the failure analyses informative. Below we improve our criteria for which baselines count as clean, unify the access comparisons and address the other comments.

Better selection of clean baselines

Upon further reflection, we agree. We now also exclude the four runs you point out: two CUDA-kernel baselines that disable kernels instead of optimizing them, one baseline that reads the hidden evaluator, and one baseline that printed credentials into its transcript. With these new rules, a full audit of all baselines found four further runs that cannot serve as clean negatives and that were therefore also excluded. In total we now exclude 20 no-side-task runs because they cannot serve as clean baselines. We have updated the paper accordingly. The results do not significantly change. AUCs change by at most 3 points, so none of our conclusions change. We have also adapted the paragraph Excluding unclean no-side-task runs. in Section 5.1. accordingly.

Access comparisons across figures

For Gemini 3.1 Pro and GLM-5.1, we used the OpenCode harness, which at the time didn’t capture the CoT summaries of the models. Table 2 and the ROC figure (Figure 9) now use only runs scored under all four access types, as Figure 4 already did. The scores are very similar to before: in post-training, the no-CoT AUCs change by at most 3 points (GPT-5.4 M_traj 76→78, Sonnet 4.6 M_traj 70→73) and the CoT columns are unchanged. In optimization, no cell changes by more than 1 point.

Other comments

Table 7 previously reported the normalized CUDA score (speedup divided by two) instead of the raw speedup used in the rest of the paper. It now reports the raw speedup. We agree that code localization is a hypothesis and reframe the paper to follow that framing. We also agree that falling within ±1 SD of the baseline doesn’t show equal performance. The result shows that there is no clear main-task penalty if the model has to additionally carry out a side task. This suggests that sabotage is hard to detect from the main-task performance alone. We clarify this in the paragraph Performance cost of sabotage. (Section 5.1.).


Thank you for your helpful comments, which have significantly improved our paper! We hope we have addressed your concerns and remain open to any further questions. We would be very grateful if you would consider increasing your score.

As the discussion period is ending soon, we wanted to follow up on our response. We would love to engage with any remaining questions or concerns you may have.

In our response, we addressed your points:

  • Clean baselines: we now exclude the four runs you pointed out, plus four further runs found in a full audit of all baselines. AUCs change by at most 3 points, so none of our conclusions change.
  • Access comparisons: Table 2 and Figure 9 now use only runs scored under all four access types, so all access conditions are compared on the same trajectories.
  • CUDA scores: Table 7 previously reported the normalized score (speedup divided by two) and now reports the raw speedup used in the rest of the paper.
  • Framing: we now present code localization as a hypothesis and describe the performance cost of sabotage as "no clear main-task penalty".

If we have addressed your concerns, we would be very grateful if you would consider increasing your score.

Comments on the paper

3 comments

Hi reviewers, as we approach the rebuttal deadline, please review the authors' responses and participate in the discussion.

I do not see any author responses. Do the other reviewers?

AuthorsOpenReview ↗

Conclusion

We apologize for the delayed response. As the discussion period is coming to an end, we wanted to briefly summarize the strengths the reviewers identified, and how we addressed their concerns.

Strengths

Overall, the reviewers found that ResearchArena provides a clear and useful framework for studying sabotage and monitoring in automated AI R&D (AbXr, xLxh), and that it is built on tasks that are “interesting and well thought through” (5e5s). They agreed that using agentic monitors that can execute the final artifact, instead of only reading the transcript, addresses an important question (xLxh, AbXr, 5e5s). Reviewer xLxh also highlighted our distinction between embedded and independent sabotage, as well as our “informative failure analyses” as helpful for understanding which evidence supports effective oversight. Reviewer 5e5s also noted that our research appears to be reproducible.

Concerns and how we addressed them

  1. Cleaner no-side-task runs (xLxh, 5e5s): Some no-side-task runs reward-hacked, e.g. by disabling kernels instead of optimizing them. Since no-side-task runs are used for measuring false positives, we are excluding them, as a monitor should flag such runs. After a full audit, we now remove 8 additional runs (20 in total). AUCs change by at most 3 points, and our conclusions remain unchanged.
  2. Access comparisons on the same runs (xLxh): Table 2 and the ROC curves in Figure 9 now only use runs that have been scored under all four access types. This means that every access type is compared on the same set of runs. No AUC score changes by more than 3 points.
  3. Influence of artifact access (5e5s): The reviewer asked whether artifact access raises suspicion simply because there is more to review. Figure 4 now includes the no-side-task runs, showing that with artifact access, suspicion remains stable or decreases in three out of four settings. A paired per-run test shows that, in the two optimization settings, artifact access significantly raises suspicion on sabotage runs for each of the six monitor models (p ≤ 0.02), so the effect is not driven by a single monitor.
  4. Motivation and setup (5e5s, AbXr): We clarified that we follow the standard AI control setup, in which the agent is given a covert side task. This way, we know exactly what the sabotage is and whether it succeeded. We therefore run monitors only on runs where the sabotage succeeded, and compare them against runs without a side task. We also clarified why side tasks differ between main tasks.
  5. More careful claims and focus (xLxh, 5e5s): We now state that code localization is only a hypothesis for why sabotage is harder to detect in post-training, describe the main-task performance result as “no clear penalty” (Section 5.1), and use a neutral caption for the artifact-access figure. We also moved the token-usage analysis to the appendix.
  6. Clarifications (xLxh, 5e5s): We clarified that the capabilities main task is scored on the GSM8K test set, while GSM1K only serves as an uncontaminated control for the side task. Table 7 now reports the raw CUDA speedup, the same metric used in the rest of the paper.

Overall, our results show that the agents we evaluated carry out harmful side tasks during AI R&D without refusing and without a clear penalty to their research performance, and that monitors benefit from access to the final artifact but still struggle when sabotage is embedded in a post-trained model. As more AI R&D is delegated to autonomous agents, we believe ResearchArena is a timely and useful framework for studying which monitor access supports effective oversight. We thank all reviewers for their constructive feedback, which has substantially improved the paper, and remain available for any further questions.

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