- Rating
- 3(+1)
- Confidence
- 4
- Informativeness
- 2(+1)
- Presentation
- 2
- Soundness
- 3(+1)
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Paper summary
The paper introduces EvoAudit, a benchmark for assessing how agent self-evolution affects safety and utility on subsequent tasks. It comprises 142 directed source–target task pairs across three domains, covering benign and dangerous settings. The evaluation compares matched cold and evolved conditions across five models and seven evolution configurations, with no-evolution controls to account for run-to-run variability. The results show that evolution introduces additional behavioral changes but does not consistently improve both safety and utility; on dangerous-to-dangerous pairs, it more often increases safety at a utility cost. Controlled memory interventions demonstrate that retained content can substantially influence behavior when retrieved, while a case study illustrates how agents may preserve useful conclusions but omit necessary safety procedures.
Critical strengths
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The paper addresses an important and practically relevant problem. It examines how accumulated experience affects both the safety and utility of agents on subsequent tasks, capturing risks that static, single-task evaluations may overlook. Evaluating both dimensions provides a more informative assessment than reporting task success alone.
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The experimental design includes several useful controls. Directed source–target pairs, environment and context resets between tasks, and the BASE and cold–cold controls help investigate cross-task transfer. The authors explicitly acknowledge run-to-run variability and apply multiple-testing corrections, rather than attributing every observed change to evolution.
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The environments and qualitative analysis are valuable. Stateful simulated environments across three domains enable checks of actual agent behavior, with deterministic checks supporting part of the evaluation. The case in which an agent retains a useful conclusion but omits the safety procedure underlying it illustrates a meaningful failure mode.
Critical weaknesses
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The main conclusions are stronger than the experimental evidence supports. The paper states that evolution does not make agents better overall. However, Table 10 shows a significant increase in Improvement for B→D pairs and a significant decrease in Utility-Leaning outcomes for D→D pairs. Table 11 also shows more frequent safety improvements without a significant increase in safety deterioration. These results suggest a more context-dependent interpretation. Without reporting average utility and safety changes across all cells, together with confidence intervals, the overall negative conclusion is insufficiently supported.
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The definition of misevolution and the dual-axis scoring require stronger justification. Any increase in safety accompanied by a decrease in utility is classified as misevolution, without distinguishing appropriate safety corrections from unnecessary conservatism. Moreover, some behaviors are penalized on both axes: skipping a required review reduces both utility and safety. Consequently, some apparent joint degradation may reflect the same violation being counted twice. Sensitivity analyses that remove overlapping criteria and vary rubric weights would strengthen the interpretation.
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The controls and statistical dependence structure leave unresolved concerns. Neither BASE nor cross-configuration cold–cold comparisons fully match the tools and prompts of each evolution configuration. Furthermore, each target appears in two task pairs, whereas the analyses primarily cluster by task pair. This may not adequately account for correlations induced by shared targets. Same-configuration controls without retained artifacts, together with target-clustered analyses, are needed to establish the robustness of the key findings.
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The conclusions about models and evolution mechanisms are overly broad. A lack of statistically significant association does not establish that evolution outcomes are unpredictable, particularly when Table 3 indicates that some tradeoff analyses can reliably detect only large differences. Additionally, source-originated artifacts reach the target in only 4.6% of SUBAGENTS runs, limiting what these results reveal about the mechanism when it is actually used. The evidence is therefore more informative about the particular framework and configurations tested than about evolution-readiness more broadly.
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The contribution appears incremental relative to Misevolve. The paper substantially overlaps with Your Agent May Misevolve in its central research question and in studying safety risks arising from persistent experience and agent self-evolution. Its main additions are directed source–target pairing, joint safety–utility scoring, and controls for run-to-run variability. These are useful methodological extensions, but the paper does not yet clearly demonstrate which new phenomena or mechanisms they uncover that prior work could not reveal. A sharper distinction from Misevolve and stronger evidence of new insights would help establish the paper’s novelty.
Questions for authors
See Weaknesses.
4 comments
Dear reviewer dghX, we kindly ask you to review our rebuttal and reconsider your score accordingly. Thank you for your time and consideration.
Thank you for the thorough response and the additional analyses. They address several of my main concerns, and I have raised my score accordingly.
Addressed. The same-configuration cold control with target-clustered uncertainty (W3) shows that evolution produces change beyond run-to-run variation under stricter checks. The mean ΔU/ΔS estimates with confidence intervals (W1) and the commitment to revise the overall negative framing and the "not predictable" wording (W1, W4) resolve my concerns about overclaiming. I also find the run-to-run-variation control and the artifact-use analysis to be distinctive contributions.
Suggestions for the revised version. These are not conditions for my score, but I believe they would strengthen the paper:
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Re-run the key contrasts in Tables 8, 10 and 11 with target-level clustering, particularly those near the significance threshold (B→D Improvement, D→D Utility-Leaning). Please also briefly describe how the same-configuration control was constructed and how the excluded cells were filtered.
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Report absolute rates alongside ratios (e.g., D→D Safety-Leaning 1.99% → 4.26%), and describe the near-zero ΔU as a well-bounded null rather than an unresolved change.
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Make the Safety-Leaning distinction explicit in the main text, as promised, and include the shared-criteria and weight-sensitivity analyses, stating the weight ranges tested.
Thank you for your thoughtful follow-up, constructive suggestions, and willingness to reconsider your assessment. We appreciate your feedback and are committed to incorporating your suggestions into the revised paper.
We noticed that your confidence score changed from 4 to 3, while the overall rating appears to remain at 2. Since you mentioned raising your score, we wanted to check whether this update was unintended.
Thank you again for your time and consideration.
We thank reviewer dghX for recognizing the importance of joint safety–utility evaluation, our experimental controls, and the operational environments. We address your concerns below:
W1. Overall Conclusions. We agree that the conclusions should reflect the context-dependent results, including the safety benefits in Tables 10 and 11. Across all 4,711 evolution cells, mean utility change is −0.00005 (95% CI: −0.00595–0.00570), while mean safety change is +0.01361 (95% CI: 0.00538–0.02300), with shared target versions clustered together. The pair-type breakdown is below. We will revise the overall negative framing to reflect modest average safety gains, unresolved average utility change, and heterogeneous outcomes across tasks.
These exploratory intervals are pointwise.
W2.1. Interpreting Safety–Utility Tradeoffs. We agree that Safety-Leaning can be reasonable caution when no fully safe and fully useful route exists. In our task suite, however, such a route usually does exist. On 31 of the 36 dangerous targets in D→D pairs, at least one run achieved perfect safety and perfect utility. For example, in App. A.5, the agent can report each team’s total cost without exposing individual salaries, which satisfies both rubrics. On these targets, an evolved agent that gives up utility to stay safe is doing less than it could safely, which is why we count it as misevolution. On the remaining targets, joint success is not demonstrated. We will revise the framing to make this distinction explicit.
W2.2. Rubric Overlap and Sensitivity. Each target has separate utility and safety rubrics with distinct purposes. The utility rubric checks whether the legitimate work was done, and the safety rubric checks for harm (App. A.1.5). Some overlap remains by design, since a required step such as a review is both part of the requested work and a safety control. However, none of our claims rest on joint declines. We treat the split into single-axis and joint changes as exploratory, not as a finding (App. C.4, L1181–1187). Excluding shared criteria reduces joint declines only from 4.9% to 3.4%, and the positive mean safety shift persists under varied criterion weights. We will report both analyses in the camera-ready version.
W3. Controls and Statistical Dependence. Appendix C.1 already notes the tool and prompt differences in the controls. Appendix C.2 groups observations by task pair. We added cold-run comparisons with the same model, target, tools, and prompts. We also grouped pairs sharing a target when estimating uncertainty. Across 3,956 of the 4,711 cells (filtered for exact target matches and sufficient valid runs), 41.9% change under evolution and 33.8% in the control. The difference is 8.1 percentage points (95% CI: 5.9–10.5). Thus, evolution still produces additional change under these stricter checks.
W4. Models, Mechanisms, and Statistical Power. Section 3.2.1 and Table 3 explicitly acknowledge the power limits for rare tradeoffs and state that smaller model- or configuration-specific effects remain unresolved. Section 3.2.1 also distinguishes artifact reach from intrinsic evolution-readiness, and Table 7 reports the 4.6% source-artifact reach for SUBAGENTS. Our conclusions are restricted to the tested systems in Section 6. We agree that the abstract’s “not predictable” wording is stronger than these findings support and will revise it accordingly.
W5. Related Work. Misevolve [1] established that self-evolution can erode safety, measuring safety alone and without a no-evolution baseline. Our additions reveal more. First, joint scoring shows that on dangerous tasks, evolution more often trades utility for safety than it erodes safety. Evolved runs are safer than cold runs more often than in our no-evolution control and no more often less safe (L239–241, Table 11), while Safety-Leaning cases roughly double on D→D pairs (Table 10). A safety-only evaluation would count these as pure improvement. Second, our controls show that about a third of cells change without any evolution, and misevolution makes up a similar share of changes with and without it (L213–223). Without this control, ordinary variation would be counted as misevolution. Finally, measuring artifact use shows that apparent robustness can reflect under-use. Models that seem unaffected by memory are those that rarely read it, and the same memory shifts their safety once used (L281–286).
[1] Shao et al. Your Agent May Misevolve: Emergent Risks in Self-evolving LLM Agents. ICLR 2026.