acceptodds
Under review as a conference paper at ICLR 2027

Intent-Preserving Adversarial User Simulation for Multi-Turn Agent Evaluation

Abstract

Multi-turn agents are commonly evaluated with LLM-based simulated users, which can be overly cooperative and can therefore overestimate an agent's performance. We here introduce StressSim, an intent-preserving adversarial user simulator framework for stress-testing agents with challenging yet valid user interactions. StressSim optimises the simulator's high-level adversarial plan for each task instance. Candidate planner prompts are evolved with a genetic prompt-optimisation loop that uses rollout traces, granular task-completion signals, and validity feedback to favour conversations that reduce task success without changing the user's underlying goal. We evaluate the approach on the MultiWOZ dataset and the retail and airline domains from τ-bench with three target LLM agents, comparing against standard simulators and hand-designed non-collaborative user behaviours. We demonstrate the effectiveness of StressSim in exposing robustness gaps across frontier LLMs, with τ-bench pass^4 scores decreasing by up to 69% on gemini-3.8-flash and 62% on gpt-5.6-sol. StressSim maintains goal preservation performance (which decreases by at most 10%), using an optimisation budget of 20 rollouts per task. Sensitivity analysis suggests that increasing the budget further decreases task success. Overall our results demonstrate that StressSim exposes robustness gaps missed by standard and hand-designed user simulators while maintaining conversation realism. This is achieved through lightweight prompt optimisation alone, without model fine-tuning.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
adversarial attacks, robustness, agent evaluation, user simulation

Reviews

Among:
Shape:
1234this paper, Bottom 25%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.75 over 4 reviews, above 25% of the others.
Reviewer_iQtZOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper introduces StressSim, which is a simulated user searching for challenging conversations while preserving original task. The optimization procedure evolves planner prompts separately for each task, using task-completion scores and automated conversation-validity checks. The experiments on MultiWOZ and τ-bench’s retail and airline domains show substantial reductions in agents’ repeated-success reliability, supported by a human validation study.

Critical strengths
  1. It introduces a different but important evaluation problem that evaluating failure modes that caused by changing or obstructing the task.
  2. It is a practical approach that the pipeline consists of goal tracking, planning, and utterance generation that we can exam each components easily and the provided prompts and conversation examples help readers inspect how failures arise.
  3. The authors assess their validity judge using 100 conversations labelled by two humans, examine transfer across target models, and provide concrete agent-failure examples. These are valuable checks beyond aggregated scores.
Critical weaknesses
  1. The ablation study about the beta sensitivity trade-off is questionable to me. Formula R_adv shows that beta greater than 1 already puts all valid candidates ahead of invalid ones. Increasing beta from 2 to 5 or 10 would therefore leave the candidate ranking unchanged. Could the authors clarify how beta actually affects the search, or whether the implementation includes an additional mechanism?

  2. StressSim receives 20 adaptive optimization rollouts per task, while the baselines use fixed instructions. A budget-matched random prompt search or best-of-20 strategy baseline is needed.

  3. The evidence for intent preservation could be stronger. Human audit for StressSim conversations that pass the validity judge and cause the agent to fail.

Questions for authors

See weakness.

2 comments

We thank the reviewer for the detailed review feedback and for recognising the importance of the evaluation problem and the practicality of the modular pipeline. Please find below our responses to the concerns raised:

  • W1. We thank the reviewer for pointing out this discrepancy. The observation is correct, and led us to find two description errors as explained in GR4. The differences across Fig. 3a are of the order of two tasks out of 50 from single optimisation runs, and we withdraw the trade-off interpretation: the optimisation is insensitive to beta in the tested range. We have corrected Section 3, Algorithm 1 and revised the interpretation in Section 4.

  • W2. Budget-matched baselines: We have run the suggested experiments to compare performance against an equal budget random search (best of 20 seed-derived candidates, one rollout each) and the unoptimized seed planner. The results are summarised in GR1. The seed planner prompt applies no adversarial pressure and has poor validity, while the random search matches StressSim on MultiWOZ but at IGA 0.84, and is weaker on every metric on both tau-bench datasets. StressSim under the same budget reaches much lower pass^4 at IGA 0.92-1.00. This illustrates the impact of the reflective, genetic optimisation based approach in terms of applying adversarial pressure while complying with validity constraints.

  • W3. Human audit of accepted, failure-inducing conversations: We have conducted the suggested additional human validation of 100 StressSim trajectories that were marked valid by the judge, yet led to task failures, sampled across the nine agent-benchmark pairs in Table 1 (details in GR2). Two annotators followed the same protocol as the original study. Annotator 1 found 84 of the 100 conversations valid and Annotator 2 found 92 valid, with 92% inter-annotator agreement (Cohen's kappa 0.63). This indicates that the failures StressSim exposes are predominantly caused by legitimate user behaviour rather than by trajectories that exploit the judge.

Thanks for your clarification. After reading the rebuttal, I would maintain my original scores.

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

StressSim evaluates multi-turn agents by optimizing simulated user behavior to induce failures while preserving the original task intent. It combines a goal tracker, a turn planner, and an utterance generator, then uses per-task genetic prompt optimization with task-completion and validity feedback. Experiments on MultiWOZ and two τ-bench domains show substantial reductions in repeated-success reliability compared with standard user simulation.

Critical strengths

The paper addresses a meaningful weakness in agent evaluation: cooperative simulators can conceal failures in clarification, intent tracking, and tool execution. Separating adversarial difficulty from goal validity is useful for building evaluation environments and potentially generating post-training data.

The evaluation includes deterministic task outcomes, repeated trials, and human validation of the validity judge. The transfer experiments are informative: prompts found against smaller models do not reliably transfer to the stronger agent, suggesting that the discovered weaknesses depend on the target policy.

Critical weaknesses

The experiments do not sufficiently isolate the contribution of genetic optimization. StressSim combines a structured simulator with task-specific search, but the comparisons use standard or fixed behavioral prompts. An unoptimized version of the same simulator and a random prompt-search baseline with the same rollout budget are needed to distinguish the benefits of the architecture, additional search, and reflective optimization.

Validity is central to interpreting the failures, but its validation remains incomplete. The 100-conversation human study is useful, yet it does not separately establish validity among accepted StressSim trajectories that cause agent failure. Appendix D.3 also contains repeated requests for return instructions after the agent has answered, raising questions about how the non-repetition criterion is applied. Since the validity judge guides both optimization and filtering, aggregate agreement alone does not establish that the search avoids exploiting its blind spots.

Questions for authors
  1. How does StressSim compare with its unoptimized seed planner and random prompt search under the same rollout budget?

  2. What fraction of accepted, failure-inducing StressSim conversations remain valid under independent human adjudication?

  3. Are the five evaluation trajectories generated afresh after fixing the selected prompt, with no search trajectories reused? How are tasks handled when the retry limit yields fewer than five valid trajectories?

1 comment

We thank the reviewer for the detailed review feedback. Please find below our responses to the concerns and questions raised:

  • W1/Q1. Isolating the contribution of genetic optimisation: We have run the suggested experiments to compare performance against an equal budget random search and the unoptimized seed planner. The results are summarised in GR1. The seed planner prompt applies no adversarial pressure and has poor validity, while the random search matches StressSim on MultiWOZ but at IGA 0.84, and is weaker on every metric on both tau-bench datasets. StressSim under the same budget reaches much lower pass^4 at IGA 0.92-1.00. This illustrates the impact of the reflective, genetic optimisation based approach in terms of applying adversarial pressure while complying with validity constraints.

  • W2/Q2. Validity of accepted, failure-inducing conversations: We have conducted the suggested additional human validation of 100 StressSim trajectories that were marked valid by the judge, yet led to task failures, sampled across the nine agent-benchmark pairs in Table 1 (details in GR2). Two annotators followed the same protocol as the original study. Annotator 1 found 84 of the 100 conversations valid and Annotator 2 found 92 valid, with 92% inter-annotator agreement (Cohen's kappa 0.63). This indicates that the failures StressSim exposes are predominantly caused by legitimate user behaviour rather than by trajectories that exploit the judge. On the non-repetition criterion (GR2), the judge fails a conversation only if the user excessively repeats in an unrealistic manner, the same request, correction or complaint, so a single repeated request after the agent has answered, as in Appendix D.3 was deemed realistic based on the judgement of the human annotators.

  • Q3. Separation of optimisation and evaluation: The evaluation trajectories are generated afresh with the frozen prompt and no search trajectories are reused. Tasks with fewer than five valid trajectories after the retry limit are excluded from pass@k and pass^k but retained in IGA. We outline the protocol and list the affected settings where tasks were skipped from the task success metrics in GR6.

Reviewer_HAopOpenReview ↗
Rating
1
Confidence
2
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

This paper proposes StressSim, an intent-preserving adversarial user simulator for multi-turn agent evaluation. It uses a modular LLM-based architecture and genetic prompt optimization to generate challenging user interactions while preserving the original task goals.

Critical strengths

The paper addresses a meaningful problem: conventional LLM user simulators may be overly cooperative and fail to expose weaknesses in multi-turn agents. The experiments demonstrate substantial reductions in task-completion performance while maintaining relatively high goal preservation.

Critical weaknesses

1. Presentation quality.

The overview diagram is overly simplified and does not adequately communicate the framework's key components and interactions, weakening the overall presentation.

2. Dependence on underlying LLM capabilities.

The framework heavily relies on the reasoning and generation capabilities of its underlying LLM. However, the paper does not investigate how simulator model capability affects the results, making it difficult to isolate the contribution of the proposed architecture.

3. Insufficient evidence for the Genetic Optimizer.

The proposed optimization procedure is inspired by GEPA and iteratively selects high-scoring planner prompts based on rollout feedback. Figure 3(b) only demonstrates the effect of increasing the search budget, without establishing that genetic optimization outperforms simpler alternatives. The absence of a budget-matched random search baseline makes the incremental contribution of the optimizer unclear.

4. Limited transferability and potential evaluation overfitting.

Table 3 shows that optimizing directly against GPT-5.6-sol produces substantially stronger results than transferring strategies from other models, suggesting considerable dependence on target-specific optimization.

Additionally, repeatedly optimizing against a fixed evaluation mechanism may introduce overfitting risks. The Goal-information Coverage dimension also shows disagreement in Cohen's κ (0.343 versus 0.736 across two annotators), raising concerns about evaluation reliability.

Questions for authors

1. How does StressSim's performance change when using simulator LLMs with different capabilities? How can the architectural contribution be distinguished from the underlying model's capabilities?

2. If the Genetic Optimizer were replaced with random candidate search under the same rollout budget, what advantages would StressSim retain? Is there evidence that the genetic optimization mechanism itself contributes meaningful improvements?

3. Given the limited transferability observed in Table 3, to what extent do the optimized strategies represent general challenging user behaviors rather than target-specific vulnerabilities?

4. How do the authors address potential overfitting to the fixed validity evaluation mechanism, particularly given the disagreement in Goal-information Coverage judgments?

1 comment

We thank the reviewer for the feedback. Please find below our responses to the concerns and questions raised:

  • W1 Presentation: We have replaced the overview figure with a more detailed version. The top half now shows the per-turn interaction loop: the goal-state tracker, adversarial planner and utterance generator producing each user message from the task goals and dialogue history, alongside the agent under test and its environment. The bottom half shows the optimisation loop: the deterministic task score and the LLM validity judge scoring each completed conversation, the validity-penalised objective, and the per-task genetic optimiser proposing new planner prompts. The figure also makes explicit that the final prompt is frozen and evaluated on fresh conversations.

  • W2/Q1 Dependence on the simulator LLM: We separate the architectural contribution from model capability by holding the model fixed and changing only the architecture. Every simulator in the paper uses the same simulator LLM backbone (gpt-5.4-nano) with no fine-tuning: the standard simulator, the four NC baselines, the new seed-planner and random-search baselines, and StressSim. Any difference in performance between them therefore comes from the architecture and the optimisation, not from the underlying model. The comparisons isolate the components step by step:

    • Standard simulator vs. StressSim: the full framework against plain prompting of the same model.
    • Seed planner vs. StressSim (GR1): identical modules, but the planner prompt is not optimised. It applies no adversarial pressure and has poor validity, so the model alone does not produce the effect.
    • Random search vs. StressSim (GR1): identical modules and rollout budget, with only the search procedure changed. Random search falls short on pass^4 reduction, validity, or both, which isolates the contribution of the genetic optimiser.
  • W3/Q2: We have run the suggested experiments to compare performance against an equal budget search and the unoptimized planner prompt. The results are summarised in GR1. The seed planner prompt applies no adversarial pressure and has poor validity, while the random search matches StressSim on MultiWOZ but at IGA 0.84, and is weaker on every metric on both tau-bench datasets. StressSim under the same budget reaches much lower pass^4 at IGA 0.92-1.00. This illustrates the impact of the reflective, genetic optimisation based approach in terms of applying adversarial pressure while complying with validity constraints.

  • W4/Q3: As discussed in GR5, we see Table 3 as a finding of the paper rather than a limitation: fixed difficult-user behaviours, whether hand-designed or optimised against a different agent, do not reliably expose the weaknesses of a given agent, and an adaptive per-target search is needed. Optimising directly against gpt-5.6-sol gives a relative reduction in pass^4 (62%) comparable to the smaller agents, so the method scales to frontier agents; what does not transfer is the specific strategy. On whether the strategies are general or target-specific, the answer is both at different levels: the taxonomy in Table 4 shows recurring strategy families across both datasets (e.g. conditional and staged disclosure), while the search selects which family and which instantiation is effective for a given agent.

  • W4/Q4 Overfitting to the validity judge: To check whether the search exploits blind spots of the fixed validity judge, we conducted an additional human validation of 100 StressSim trajectories that were accepted by the judge yet led to task failures, sampled across the nine agent-benchmark pairs in Table 1 (details in GR2). Two annotators followed the same protocol as the original study. Annotator 1 found 84 of the 100 conversations valid and Annotator 2 found 92 valid, with 92% inter-annotator agreement (Cohen's kappa 0.63). The failures StressSim exposes are therefore predominantly caused by legitimate user behaviour rather than by trajectories that exploit the judge. On the Goal-information Coverage disagreement, this axis is also the one on which the two annotators agree least with each other (kappa 0.525), so the gap between 0.343 and 0.736 largely reflects the difficulty of the criterion for humans rather than inconsistency of the judge. Against both annotators the judge has recall of 1.000 on this axis and errs only by rejecting conversations humans would accept (GR3), so its errors remove conversations from the evaluation rather than admit invalid ones.

We hope the additional control studies, the human audit, the edits to the figure address the soundness and presentation concerns raised by the reviewer.

Reviewer_4spcOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes StressSim, an adversarial user simulator designed to expose agent failures through challenging but realistic user interactions while preserving the original user goal. The framework consists of a goal-state tracker, an adversarial planner, and a user utterance generator. It uses genetic prompt optimization to find effective adversarial strategies for each instance, without requiring model fine-tuning. The authors evaluate StressSim on MultiWOZ and tau-bench, showing that it can expose more agent failures than standard user simulators and several manually designed non-cooperative baselines. The paper also studies whether adversarial strategies transfer across different agents and includes a human evaluation to assess the reliability of its automated validity checks.

Critical strengths
  1. Relevant problem. Existing user simulators tend to be overly cooperative and may fail to expose important agent weaknesses. Exploring more challenging but realistic user interactions is an interesting and useful direction for evaluating multi-turn agents.

  2. Explicit validity constraints. The framework considers both goal-information coverage and behavioral validity, which helps ensure that the identified failures are not simply caused by unrealistic user behavior. The human annotation study also provides some evidence that these checks are reliable.

  3. Concrete diagnostic value. The environment-based evaluation can identify actual task failures rather than relying on agents’ self-reported success. The examples also show meaningful failure cases, such as incorrect booking modifications and missing tool calls.

Critical weaknesses
  1. Missing controlled comparisons. StressSim uses 20 adaptive rollouts per task, while the main baselines rely on fixed strategies. It would be helpful to compare against equal-budget random prompt search and an unoptimized version of the same simulator to better understand how much of the improvement comes from the proposed optimization. Ablation studies would also help clarify the contribution of each component.

  2. Limited validation of the validity claims. The human evaluation only covers 100 conversations, and the agreement on goal-information coverage is relatively inconsistent. It would be more convincing to manually examine the trajectories that successfully induce agent failures and verify that they still preserve the original user intent. Also, the paper does not evaluate whether the identified failures or agent rankings align with real human interactions, which limits its claims about real-world evaluation.

  3. Inconsistent empirical improvements. The results are not consistently better than the baselines. For example, on MultiWOZ with Gemini, the unavailable-service baseline achieves a much lower pass^4 than StressSim (0.160 vs. 0.620), while having only slightly lower validity (0.980 vs. 1.000). This result deserves more discussion. It would also be helpful to report confidence intervals and results across multiple optimization runs to better understand the stability of the improvements.

  4. Unclear penalty sensitivity analysis. Given the binary validity score and rank-based selection, the tested penalty values (\beta=2,5,10) should lead to the same candidate ranking, since valid trajectories would always rank above invalid ones. Therefore, I am not sure why Figure 3a shows different results and interprets them as a trade-off related to penalty strength. The authors should clarify whether these differences come from implementation details or sampling randomness.

Questions for authors

See Weaknesses

1 comment

We thank the reviewer for the detailed review feedback and appreciating the motivation behind our proposed approach. Please find below our responses to the concerns and questions raised:

  • W1. Missing control experiments: We have run the suggested experiments to compare performance against an equal budget search and the unoptimized planner prompt. The results are summarised in GR1. The seed planner prompt applies no adversarial pressure and has poor validity, while the random search matches StressSim on MultiWOZ but at IGA 0.84, and is weaker on every metric on both tau-bench datasets. StressSim under the same budget reaches much lower pass^4 at IGA 0.92-1.00. This illustrates the impact of the reflective, genetic optimisation based approach in terms of applying adversarial pressure while complying with validity constraints. On component ablations: read together with the standard user, the two new rows form a cumulative ablation of the method (standard, seed planner, random search, StressSim), in which each row adds one component: the seed adversarial planner prompt, search over 20 candidates under the validity-penalised objective, and reflective mutation on rollout feedback. The individual simulator modules are not ablated, which we will note in the limitations.

  • W2. Human validation of failed trajectories: We have conducted the suggested additional human validation of 100 StressSim trajectories that were marked valid by the judge, yet led to task failures, sampled across the nine agent-benchmark pairs in Table 1 (details in GR2). Two annotators followed the same protocol as the original study. Annotator 1 found 84 of the 100 conversations valid and Annotator 2 found 92 valid, with 92% inter-annotator agreement (Cohen's kappa 0.63). This indicates that the failures StressSim exposes are predominantly caused by legitimate user behaviour rather than by trajectories that exploit the judge. We will add this study to the paper. Regarding alignment with real human interactions, our work is focussed on stress testing of conversational agents, and thus aims to find the "worst-case", yet realistic user behaviour, rather than necessarily modelling real-world distributions of user behaviour.

  • W3. We agree the MultiWOZ results deserve additional discussion, since the unavailable-service baseline obtains lower pass^4 than StressSim for all three agents, and we will revise the corresponding statement in Section 4.1. This baseline is a strong but narrow prior: in the original implementation of Shim et al. [1], the proposer is given the underlying backend API and asked to add conditions to its requests that it knows the agent cannot fulfil. It is therefore not a generic difficult-user behaviour but a strategy with privileged knowledge of the environment. This is particularly strong on the MultiWOZ environment, as an agent discovers backend APIs through helper functions, thus unfulfillable conditions can send it into repeated lookups and overall task failure. Similar failure patterns were reported in the original paper. This adversarial strategy is not as effective on the tau bench environment as that provides complete API documentation in the system prompt, thus unfulfillable conditions can be quickly rejected. In contrast, StressSim has no such environment-specific prior and searches a broad space of valid behaviours with 20 rollouts per task. It still reduces pass^4 on MultiWOZ by 0.30-0.44 absolute, more than the other three NC behaviours. Across the nine agent-benchmark pairs StressSim obtains the lowest pass^4 on all six tau-bench pairs (tied at 0.000 on airline with gpt-5.4-nano), and the second-lowest on all three MultiWOZ pairs, whereas no single NC behaviour is consistently the strongest. This motivates the need for a dynamic, optimisation based method to stress test varying agents. On confidence intervals and multiple optimisation runs: we follow the evaluation protocol of tau-bench [2] and Shim et. al. [1], which run repeated trials per task to obtain pass@k and pass^k and report their point estimates, and we will state in the limitations that each task is optimised once, so variance across optimisation runs is not captured.

  • W4. We thank the reviewer for pointing out this discrepancy. The observation is correct, and led us to find two description errors as explained in GR4. The differences across Fig. 3a are of the order of two tasks out of 50 from single optimisation runs, and we withdraw the trade-off interpretation: the optimisation is insensitive to beta in the tested range. We have corrected Section 3, Algorithm 1 and revised the interpretation in Section 4.

References

[1] Shim, J., Song, W., Jin, C., Kook, S., and Jo, Y. (2026). Non-Collaborative User Simulators for Tool Agents. ICLR 2026.

[2] Yao, S., Shinn, N., Razavi, P., and Narasimhan, K. R. (2025). tau-bench: A Benchmark for Tool-Agent-User Interaction in Real-World Domains. ICLR 2025.

Comments on the paper

4 comments
AuthorsOpenReview ↗

Global response (1)

We thank the reviewers for engaging with the paper, and providing valuable feedback. We are encouraged that all four reviewers find the problem meaningful and relevant, and that they highlight the explicit separation of adversarial difficulty from goal validity (4spc, kzsr), the modular and inspectable pipeline with concrete failure examples (4spc, iQtZ), the human validation and transfer experiments (kzsr, iQtZ), and the substantial reductions in task completion at high goal preservation (HAop). The remaining concerns are largely shared across reviewers, and we address them below with new budget-matched baselines, a human audit of judge-accepted, failure-inducing conversations, and a correction to the objective description. Furthermore, we have made corrections to the manuscript (highlighted in blue).

GR1. Budget-matched random search and seed prompt baselines

All reviewers requested for additional baselines to isolate the impact of the search-based approach and the reflective optimisation process. We thus run two sets of additional experiments:

  • Seed Planner Prompts: This is essentially an unoptimised version of StressSim, that uses the seed adversarial planner prompt, run on gemini-3.8-flash and Kimi-K2.6.
  • Budget-matched random search: StressSim run with a population of N=20N=20 and zero generations. The seed planner prompt and 19 candidates proposed from it by the reflection LLM are each evaluated on a single rollout, and the highest-scoring candidate under the validity-penalised objective is frozen and evaluated as usual. It therefore has the same seed prompt, reflection LLM, objective and 20-rollout budget as StressSim, but no reflective mutation on rollout feedback. These experiments are only run on gemini-3.8-flash due to time constraints.

Both sets of experiments used the same evaluation settings and tasks as the previous experiments in the paper to enable a fair comparison. The results are summarised below:

DatasetAgent LLMUserpass@1pass@4pass^4IGA
MultiWOZgemini-3.8-flashstandard0.9400.9440.9160.920
seed planner (0 rollouts)0.9520.9800.8680.780
random search (20 rollouts)0.8400.9560.6480.840
StressSim (20 rollouts)0.8560.9800.6201.000
kimi-k2.6standard0.9240.9800.8200.940
seed planner (0 rollouts)0.8800.9720.6800.820
StressSim (20 rollouts)0.7840.9800.3840.940
τ\tau-bench retailgemini-3.8-flashstandard0.5880.7880.3200.960
seed planner (0 rollouts)0.6480.9040.3760.660
random search (20 rollouts)0.4800.7320.2240.680
StressSim (20 rollouts)0.3840.6680.1001.000
kimi-k2.6standard0.5520.8400.3200.900
seed planner (0 rollouts)0.5520.8720.2880.720
StressSim (20 rollouts)0.2720.5920.0000.920
τ\tau-bench airlinegemini-3.8-flashstandard0.3800.5680.2441.000
seed planner (0 rollouts)0.4040.6240.2480.540
random search (20 rollouts)0.4600.6360.2160.720
StressSim (20 rollouts)0.2880.5120.0760.920
kimi-k2.6standard0.4080.5520.2000.920
seed planner (0 rollouts)0.4160.6640.1640.660
StressSim (20 rollouts)0.3480.6800.0720.940

These baselines isolate the contribution of the reflective genetic optimisation over both the initial seed prompt and a budget-matched random search. The unoptimised seed planner applies little or no adversarial pressure (for gemini-3.8-flash, pass^4 is at or above the standard simulator on both tau-bench datasets and 0.868 vs 0.916 on MultiWOZ; for kimi-k2.6 the reductions are at most 0.14) and displays substantial validity failures (IGA 0.540-0.820 across both agents). The two observations are linked: pass@k and pass^k are computed over valid conversations only, so a planner whose challenging behaviours mostly violate the assigned goal has no measurable effect on the conversations that remain. Random search under the same 20-rollout budget recovers some validity (IGA 0.680-0.840) and lowers pass^4 to 0.648 on MultiWOZ and 0.224 on retail, and leaves it unchanged on airline (0.244 to 0.216). StressSim under the same budget reaches much lower pass^4 (0.620, 0.100 and 0.076 for gemini-3.8-flash; 0.384, 0.000 and 0.072 for kimi-k2.6) at IGA of 0.920 or higher in every setting. Since random search shares the seed prompt, reflection LLM, objective and rollout budget with StressSim, the difference between the two isolates the effect of reflective mutation, which uses rollout feedback to propose the next candidate rather than sampling blindly from the seed. Random search matches StressSim's pressure on MultiWOZ but at IGA 0.840; on both τ\tau-bench datasets StressSim is stronger on every metric.

AuthorsOpenReview ↗

Global response (2)

GR2. Validity of judge-accepted, failure-inducing StressSim conversations

Reviewers 4spc, kzsr and iQtZ requested for further validation of the trajectories that were passed by the validity judge and led to a task failure, to rule out the optimisation exploiting the judge's blind spots. We thus conducted a human validation study on 100 randomly sampled conversations (only from the StressSim eval runs) from the 9 experimental settings reported in Table 1. We specifically chose 100 traces that were marked valid and led to a task success failure. Two human annotators manually validated the conversation traces following the same protocol as the prior validation study. Results on the 100 judge-accepted, failure-inducing conversations:

  • Annotator 1: 84 valid (84%)
  • Annotator 2: 92 valid (92%)
  • Valid under both annotators: 84 (84%); every conversation Annotator 2 marked invalid was also marked invalid by Annotator 1
  • Inter-annotator agreement: 92% (Cohen's κ 0.63)

Even under the stricter annotator, the large majority of judge-accepted, failure-inducing conversations are valid, indicating that the failures StressSim exposes are predominantly caused by legitimate user behaviour rather than by trajectories that exploit the judge.

GR3. Agreement on goal information coverage

Reviewers 4spc and HAop note the lower agreement on the goal-information coverage axis in the original study (kappa 0.343 and 0.736 against the two annotators). This axis is also the one on which the two annotators agree least with each other (kappa 0.525), and the remaining gap reflects the direction of the judge's errors rather than unreliable judgements. Against both annotators the judge has recall of 1.000 on this axis, i.e. every conversation a human marked as failing coverage is also rejected by the judge, but precision of 0.231 and 0.615, i.e. it is conservative and rejects some conversations that humans would accept, at accuracy of 0.900 and 0.950 (Table 5, Appendix E). The judge's errors therefore remove conversations from the evaluation rather than admit invalid ones. The remaining five axes have kappa of 0.73-1.00 against the judge, and the final validity label, which determines whether a conversation is counted, has kappa of 0.68 and 0.84 against the two annotators respectively.

GR4. Effect of the validity penalty β\beta

Reviewers 4spc and iQtZ observe that, as written, the objective bounds the sub-task term in [0,1][0,1], so any β>1\beta>1 places every valid candidate above every invalid one and the sweep over β∈{2,5,10}\beta\in\{2,5,10\} cannot change the ranking. We thank the reviewers for the careful reading. The observation is correct, and it led us to find two description errors in Section 3 and Algorithm 1, which we will correct:

  • Objective. The 1/m1/m normalisation is a typo. The implementation uses the unnormalised sum,
\beta(1-C(\tau,x,U_\pi)),$$ so the sub-task term lies in $[0,m]$, with $m \approx 3$ on both benchmarks. - **Parent selection.** Parents are the top-$K$ candidates by penalised score regardless of validity, not the top-$K$ valid candidates; the final prompt is likewise the top-scoring candidate. Both corrections are to the description, not to the experiments. With $\beta=5$, which is used for every result in Tables 1 to 4, every valid candidate outscores every invalid one, so selecting the top-$K$ by penalised score coincides with selecting the top-$K$ valid candidates whenever at least $K$ valid candidates exist, and the returned prompt is the best valid candidate whenever one exists. The $1/m$ factor does not change the ordering of candidates within a task. The algorithm as run therefore behaves as the paper had originally described, except in generations with fewer than $K$ valid candidates, where invalid candidates fill the remaining parent slots. With these corrections, $\beta$ can change the ranking only when $\beta < m$, i.e. only at $\beta=2$ in the sweep. $\beta$ also enters the search through a second channel: the penalised score of each parent is part of the reflection input, so a larger $\beta$ signals more strongly that a validity failure dominates the parent's fitness and can push the proposed mutations towards restoring validity rather than increasing pressure. This channel operates for every $\beta$, including those that induce the same ranking. The sweep, however, does not let us measure it: the differences across the three $\beta$ values in Figure 3a are of the order of two tasks out of 50, from a single optimisation run per task, and we do not consider them evidence of a trade-off. We withdraw that interpretation: the optimisation is insensitive to $\beta$ in the tested range, and any $\beta \geq m$ guarantees that valid rollouts rank above invalid ones. We have revised the description in the paper accordingly.
AuthorsOpenReview ↗

Global response (3)

GR5. Transferability and target-specific optimisation

Reviewers HAop and kzsr note that strategies optimised against one agent transfer only partially to another, and ask whether this reflects overfitting to the target and whether the discovered strategies are general challenging behaviours or target-specific vulnerabilities.

Table 3 in the paper shows that transfer is partial between two agents with smaller models: the prompts optimised against gpt-5.4-nano lower pass^4 for gemini-3.8-flash from 0.320 to 0.184, compared to 0.100 when optimised against gemini-3.8-flash itself. Prompts optimised against either smaller agent have no measurable effect on gpt-5.6-sol. Optimising directly against gpt-5.6-sol, however, reduces its pass^4 from 0.296 to 0.112 at IGA 1.000. The method therefore scales to frontier models, however the specific strategy that is effective against each model does not transfer.

We argue this is the central finding of the paper rather than a limitation. The motivation for StressSim is precisely that a fixed set of difficult user behaviours, whether hand-designed (the NC baselines) or found against a different agent (the transfer rows of Table 3), does not reliably expose the robustness gaps of a given agent. Table 3 is the direct evidence for this claim: the failure modes of a frontier agent are not those of a weaker agent, and an adaptive, per-target search is needed to find them.

GR6. Separation of optimisation and evaluation

Reviewer kzsr requested for clarification on whether the evaluation trajectories are generated afresh after the optimised prompt is fixed, with no search trajectories reused, and how tasks are handled when the retry limit yields fewer than nn valid trajectories. We clarify the protocol below since it is central to interpreting the reported numbers.

Optimisation and evaluation are completely separate phases that share no trajectories. During optimisation, each task instance is searched for 20 rollouts in total, and the search returns a single optimised planner prompt πx⋆\pi_x^\star. All rollouts generated during the search, including the rollouts of πx⋆\pi_x^\star itself, are then discarded. During evaluation, the planner prompt is frozen and n=5n=5 new conversations are generated from scratch with the frozen prompt, the same target agent and a fresh environment state for each trial. Every pass@k, pass^k and IGA value in the paper is computed from these evaluation conversations only. No search rollout contributes to any reported metric, and the optimised prompt is not updated during evaluation. The same evaluation protocol, with the same nn, retry limit and validity filter, is applied to the standard and NC baselines, so the comparison in Table 1 is between fixed simulators evaluated under identical conditions.

On the retry limit: as described in Section 4 (Metrics), invalid trajectories are discarded and a task is retried at most 15 times until n=5n=5 valid conversations are collected. If a task still has fewer than n=5n=5 valid conversations after 15 attempts, it is excluded from the pass@k and pass^k computation for that simulator, since these estimators require nn valid trials; it remains included in IGA, which is a first-attempt property defined for every task. The same rule is applied to every simulator. We report below all settings where we observed tasks being skipped due to insufficient number of valid conversations:

  • tau-retail, NC emotional, gpt-5.4-nano: 5
  • tau-retail, NC tangential, gpt-5.4-nano: 2
  • tau-airline, NC tangential, gemini-3.8-flash: 1
  • tau-retail, seed planner, gemini-3.8-flash: 1
  • tau-airline, seed planner, gemini-3.8-flash: 2

We have clarified these details and reported the number of skipped tasks in the revised version of the paper.

Dear Reviewers,

Thank you again for your reviews. As the discussion period is coming to a close, we wanted to check whether our response has addressed your concerns. In brief, we added budget-matched baselines (seed planner and random search), a human audit of judge-accepted, failure-inducing conversations, and corrections to the objective and parent-selection description. We would be grateful for any further feedback and are happy to clarify anything before the deadline.

Best regards, The Authors

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