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Under review as a conference paper at ICLR 2027

Groundworks: Agents Can Complete Tasks Yet Fail Under Plausible Perturbations In Multi-Turn Interactions

Abstract

Agents carry out tasks through evolving conversations and tool use, yet success in a fixed scenario does not guarantee whether they can handle real-world challenges such as revised requirements or unexpected tool results. Mishandling these can lead to hallucinations, such as misstating the user’s current requirements or claiming success without tool evidence. Thus, task completion alone cannot establish whether their claims are grounded in the evidence available at each turn. We introduce **GroundWorks**, an adaptable, end-to-end framework that constructs paired multi-turn evaluations with verifiable target outcomes. Its 30 reusable perturbation operators model plausible changes to an interaction or environment and target specific hallucination risks. For each operator, GroundWorks creates an original, solvable scenario and a matched perturbed scenario, specifying the relevant evidence and criteria for appropriate handling before execution. It then simulates both interactions and verifies agent behavior against the predefined criteria and recorded evidence, distinguishing successful handling, targeted hallucination, and other failures. Across five agents and 1,040 paired evaluations, agents fail on 47% of perturbed scenarios whose originals they complete, averaged across agents: 25% involve targeted hallucination and 22% other failures. Changes to tool capabilities and action outcomes yield the highest conditional failure rate (71%). We further apply GroundWorks to patient-facing healthcare tasks, demonstrating its adaptability to a new setting.

Primary area:
datasets and benchmarks
Keywords:
agent evaluation, multi-turn interaction, hallucination, robustness, verifiable outcomes

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Paper summary

GroundWorks tests whether agents can handle changes during a multi-turn task, such as missing information, revised requests, or unexpected tool results. It creates pairs of scenarios from existing benchmark tasks, changing one condition between them. For each pair, it defines the evidence that matters and the response expected from the agent, such as asking for missing information or reporting a failed action. It then runs both scenarios separately and uses LLM judgments and code checks to assess the agent’s response. On average, agents failed in 47% of the perturbed scenarios whose originals they completed. About half of these failures involved targeted hallucinations. The authors also applied GroundWorks to healthcare tasks and found a similar pattern: success on the original task did not guarantee an appropriate response when conditions changed.

Critical strengths
  1. GroundWorks examines aspects of agent reliability beyond task completion. It checks whether the agent's claims were supported by the evidence available at the time and distinguishes unsupported claims from other handling failures. This allows models with similar success rates to be compared by the kinds of mistakes they make.

  2. The paired scenarios test how agents respond to changing conditions in a controlled multi-turn setting. Agents can ask follow-up questions and use tools to resolve the problem. The evaluation therefore examines both their ability to perform the original task and their response when information is missing or results differ from what they expected.

Critical weaknesses
  1. Additional evaluation value of the integrated framework: The evaluation benefits of the integrated design are not sufficiently established. Prior work already studies multi-turn responses to incomplete information, distinguishes hallucinations from other failures, and uses operators to generate and validate perturbations (CAR-bench (https://aclanthology.org/2026.acl-long.1886.pdf); MIRAGE-Bench (https://arxiv.org/html/2507.21017v1); TrustDABench (https://arxiv.org/html/2608.24145v1)). GroundWorks brings these approaches into a single procedure that covers a range of conditions and specifies the relevant evidence and response criteria for each perturbation. However, the paper provides limited evidence that this integration better captures problems that existing evaluations struggle with or overlook. The failure breakdowns and applications to different tasks show that the framework can be used, but do not establish how much the integrated design improves coverage, consistent construction of valid scenarios, or adaptation to new tasks. The experiments show that GroundWorks can find failures, but offer limited evidence of which difficulties in existing evaluations its design resolves.

  2. Reliability of failure classification: The reliability of failure classification, a core function of the tool, is not sufficiently established. GroundWorks's diagnostic value depends on accurately and consistently distinguishing targeted hallucinations from other handling failures. Its main analyses use this distinction to describe failure patterns and differences across models and conditions. Predefined criteria and code checks help verify the basis for judgments, but deciding whether a claim is supported and which failure it represents still depends on the LLM's interpretation. The authors conducted human reviews during development and a manual audit of the healthcare evaluation. However, the final-judge check in Table 9 involves one annotator reviewing 14 scenario pairs with the automated verdicts visible. This provides limited evidence that people would apply the criteria consistently or reach the same classifications without seeing the automated verdicts. The effect of misclassification on failure rates and comparisons across models and conditions also remains untested. The concern is therefore not simply that the judge may make some errors: the reliability of the failure-type diagnoses and comparisons central to the framework remains insufficiently established.

Questions for authors
  1. Do human reviewers reach the same verdicts without seeing the AI's judgments? Distinguishing targeted hallucinations from other failures is central to the tool, so the accuracy of this distinction needs to be established. With the judge fixed, could multiple annotators assess cases not used during development without seeing its verdicts? Please report the models and conditions covered, agreement between annotators, how disagreements are resolved, and a confusion matrix across success, targeted hallucination, and other failure.

  2. Does correcting judgment errors change the main findings? Using the same sample as Question 1, please compare failure-type proportions and the main model and condition comparisons under automated and adjudicated human labels. Report group sizes and uncertainty accounting for the sampling scheme; if the sample is insufficient, collect more labels or limit the conclusions. An inconclusive result from a small sample is not evidence of stability.

  3. How often does the assessment find hallucinations in completed tasks? Finding new failures by changing test conditions differs from detecting problems that completion scoring misses. Cases where an agent completes the task but makes an unsupported claim would directly demonstrate what the tool adds to completion scoring. On feasible perturbed tasks, could the authors cross-tabulate task completion and targeted hallucinations for the same runs, and report the proportion of completed runs with hallucinations alongside examples? Since PS already requires the absence of targeted hallucinations, please assess task completion using criteria separate from the hallucination judgment.

  4. How much does the perturbation increase failure? Section 5 claims that the design isolates causes, but the observed 47% failure rate does not distinguish perturbation effects from variation between runs. Could the authors repeat both versions on representative tasks and also measure failure when an unchanged original is rerun after a successful run? Since OS and PS use different criteria, direct comparisons should use tasks feasible in both versions and the same completion criteria, with handling outcomes reported separately.

  5. Do other tasks fail similarly under the same condition? Some operators are evaluated on only one scenario pair from one source task (Table 11). Could the authors apply these operators to new tasks and check scenario validity and whether the failure patterns hold? Please also assess sensitivity to the existing task sample, separately from the new-task experiments.

6 comments
AuthorsOpenReview ↗

Author Response, part 1 of 4

We thank the reviewer for recognizing that GroundWorks lets models with similar success rates be compared by the kinds of mistakes they make, in a controlled multi-turn setting where agents can ask follow-up questions and use tools.

We ran additional experiments and analyses. Please find the answers below. The revised PDF is also uploaded with changes marked in blue. We also expanded the study from 208 to 308 pairs by adding 100 pairs from nine benchmarks, and every operator now has at least five pairs. The results below are from this extended set.

W2, Q1 (blind human verdicts): Three blind annotators labelled 120 episodes, and the final human labels agree with the judge on 83.8% of them.

Thank you for laying out the study so precisely. We ran this human study.

  • Annotators and cases. Three annotators, all authors of the paper, labelled 120 perturbed episodes of the final run without seeing the judge's verdicts. None had seen these episodes before, and none of the cases was used in development.

  • Models and conditions covered. The sample has 8 episodes for each combination of the five agents and the judge's three outcomes, so 24 per agent, and it covers all six families and all 30 operators.

  • Agreement and disagreements. Two annotators labelled each episode independently as handled, targeted hallucination or other failure. The two annotated labels agree on 89 of the 120 episodes (inter-annotator agreement 74%, kappa 0.60). A fourth author settled the remaining 31 disagreements.

  • Confusion matrix. We compare the judge's verdicts with the final human labels. On the 120 sampled episodes, they agree on 74.2%. After weighting to the sampling frame, they agree on 83.8% of episodes (κ = 0.72).

The table below is the confusion matrix across handled, targeted hallucination and other failure, with the judge's verdict in rows and the final human label in columns. Counts are the 120 episodes as drawn.

Judge verdict / HumanHandledTargeted hallucinationOther failure
Handled3712
Targeted hallucination7285
Other failure14224

The table below gives the judge's precision and recall for each label, weighted to the frame.

LabelJudge precision (%)Judge recall (%)
Handled94.383.9
Targeted hallucination77.882.8
Other failure63.884.7

W2, Q2 (effect of correcting judgment errors): Conditional failure is 36.3% under human labels and 44.3% under judge labels.

We agree that this comparison is needed. We compared the judge with the final human labels on the same sample as in Q1, weighting each stratum by its size in the sampling frame.

  • Failure-type proportions. The table below shows the proportions of each outcome, conditioned on original success and averaged across the five agents.
Outcome, given original successJudge (%)Human labels (%)
Handled55.763.7
Targeted hallucination22.417.9
Other failure21.918.4
Failure in total44.336.3

Every failure type has a lower rate under human labels, with total failure 8.0 percentage points lower than under judge labels, suggesting that the judge is stricter than human annotators. However, even under human labels, agents still fail in more than a third of scenarios whose originals they complete.

  • Group sizes and uncertainty. Each agent has 24 labeled episodes, including 11–18 with successful originals, while each family has 11–30 episodes. Accounting for stratified sampling, the 95% confidence interval for the pooled failure rate is about 16 percentage points wide and includes the judge's estimate.

  • Comparison under the two sets of labels. Human labels preserve the judge's ranking of the five agents, except that Kimi K2.5 and Claude Haiku 4.5 swap positions, which were already very close in the paper. Under both sets of labels, Qwen3 32B and Ministral 3 14B have the highest failure rates, while GPT-5.6 Luna has the lowest. Additionally, tool capabilities and action outcomes has the highest failure rate among the three families with at least 15 labelled episodes, consistent with the judge's results.

AuthorsOpenReview ↗

Author Response, part 2 of 4

W1 (Value of the integrated design): None of these works combines GroundWorks' four design decisions, each of which reveals limitations that prior evaluations miss.

Thank you for pointing us to these. We already cite CAR-bench (ACL 2026) and MIRAGE-Bench (arXiv preprint). TrustDABench is a concurrent preprint (arXiv:2608.24145v1, August 25, 2026), which we added to the revision. For each design decision, we state what the three works do instead and what it reveals.

First, targeted hallucination is formally defined (Section 3.1.1) and our evaluation distinguishes hallucination from other failures. In MIRAGE-Bench's out-of-scope setting, the lowest score groups together ignoring the query, answering with hallucinated information, and ending the task early. Our integrated design reveals that, of the 48 percentage points of failure for our submission's five agents, 26 are targeted hallucinations and 22 are other failures. For example, when the return tool is removed, Kimi K2.5 tells the user "the refund will be processed to your PayPal account within 5-7 business days" (targeted hallucination), while Claude Haiku 4.5 calls the exchange tool instead, which the user never requested (other failure). These two failure types call for different mitigations, and a single failure score would not tell them apart. Additionally, agents with similar failure rates also fail differently: 63% of failures by Kimi K2.5 are hallucinations, compared to 38% for GPT-5.6 Luna.

Second, every perturbed scenario is paired with its original, decoupling agent capability from robustness to perturbation. MIRAGE-Bench has no matched original scenario. Each test is a single snapshot with the risk already present, so a failure is never compared with the same agent's result on the unchanged task. CAR-bench and TrustDABench do not condition their hallucination or refusal measures on the same agent completing the original task (TrustDABench does so only for its robustness score). GroundWorks reports outcomes conditioned on the same agent's original success. Our integrated design reveals that 34% of all perturbed failures occur on tasks the agent also failed in the original. An unpaired evaluation would attribute them to the perturbation, and our paired analysis sets them aside.

Third, operators are defined independently of any benchmark and can expose agent failures in new domains. CAR-bench and TrustDABench each cover one domain (in-car assistance and structured-data analysis). Each of GroundWorks' 30 operators is defined by the grounding source it changes and the required response, so the same operators generate perturbations across tasks and domains. For consistent construction of valid scenarios, every candidate pair passes automatic code checks and a checker model from another model family (Appendix B.4). On PatientAgentBench (Section 4.4), 19 of the 30 operators transferred across all six families, and we used the operators to add 100 new cases from nine benchmarks (Q5). Our integrated design reveals that an agent's robustness depends on the domain. GPT-5.6 Luna and Claude Haiku 4.5 have similar failure rates in the main study (36% and 41%) but differ on healthcare tasks (31% and 60%), so a result on one benchmark does not carry over. For example, when a booking tool is removed, Claude Haiku 4.5 first says it cannot book the visit but later refers to a scheduled appointment, which does not exist. A patient could rely on a visit that was never booked.

Fourth, hallucination is also measured on feasible tasks in full multi-turn interactions, exposing completed tasks that still contain hallucinations. CAR-bench and TrustDABench measure hallucination or refusal only on requests that can no longer be satisfied. Their feasible variants (CAR-bench's disambiguation tasks and TrustDABench's answer-preserving perturbations) are not scored for hallucination. MIRAGE-Bench evaluates a single next action from a frozen snapshot, where follow-up actions "cannot be executed or observed", and does not measure task completion. GroundWorks runs full multi-turn interactions with a simulated user and scores targeted hallucination on feasible tasks, where agents must handle the change and still complete the task. It also covers world knowledge, earlier user statements, and saved memory as grounding sources (44 of the 308 pairs target world knowledge or saved memory). Our integrated design reveals that 10.4% of completed feasible tasks still contain a targeted hallucination (Q3). A completion metric would count these runs as successes.

In summary, in our integrated design, the operators define what changes, the matched original shows whether the change caused the failure, and the separate scores show what kind of failure it was. Each finding above relies on more than one of these. The 10.4% figure, for example, needs feasible perturbed tasks, a completion check, and a separate hallucination score in the same episode.

AuthorsOpenReview ↗

Author Response, part 3 of 4

W1, Q3 (hallucination in completed tasks): On feasible perturbed tasks, 10.4% of completed runs contain a targeted hallucination.

Thank you for proposing this test. We cross-tabulated task completion and targeted hallucination for the same runs, on feasible perturbed tasks (Appendix D.5). Completion is determined only by the completion judge's assessment of task requirements, independent of the handling verdict.

The table below shows the result per agent.

AgentCompleted runs that contain a targeted hallucination
GPT-5.6 Luna7% (6/87)
Kimi K2.58% (7/83)
Claude Haiku 4.511% (8/76)
Ministral 3 14B14% (8/59)
Qwen3 32B13% (5/39)
Average of the five10%

The average is 10.4% [6.5, 15.0]. Because GroundWorks scores completion and hallucination separately, it catches these runs.

In one example, the user asks Ministral 3 14B to change the air purifier in their order to a different size with night mode, but does not say which size. Ministral 3 14B does not ask; it picks the large variant, tells the user it "matches your requirements", and places the change. Large happens to be the size the task expected, so the run passes its task requirement, which checks that the agent makes the expected order changes. But the user never gave a size, and presenting the guess as the user's requirement is a targeted hallucination that only the separate hallucination score catches.

Q4 (run-to-run variation): The perturbation adds failure beyond run-to-run variation. We show this by rerunning the experiment.

Thank you for these concrete checks. We ran both scenarios again for a stratified sample of 106 pairs, with all five agents (Appendix D.5). The table below shows the first run beside the rerun. To directly answer your question, we report completion under the same criteria and handling separately, on the feasible tasks whose original was completed in the first run.

All p-values are above 0.05, so none of the differences between the two runs is statistically significant.

Average of the five agentsFirst runRerunMcNemar p between runs
Original success (%)68700.19
Perturbed: handled (%)49500.65
Perturbed: targeted hallucination (%)27270.80
Perturbed: other failure (%)24230.91
Failure given original success in the same run (%)51460.44
Completed original fails when run again unchanged (%)9
Same completion criteria: original completed (%)100 (by selection)93
Same completion criteria: perturbed completed (%)79830.42
Handling on those tasks: handled (%)68691.00
Handling on those tasks: targeted hallucination (%)15170.69

Between the runs, every average in the table changes by less than 5 points, and the two runs give the same outcome on 86% of the originals and 80% of the perturbed scenarios. No change is significant (exact McNemar test, pooled over the five agents). To bound the change between runs, we also computed its interval: the handled rate changes by 0.9 points [-3.1, 4.8] and original success by 2.3 points [-0.6, 5.4], so on these measures run-to-run variation is at most about 5 points.

Additionally, in 143 agent–pair cases, only the perturbed scenario fails, compared to just 11 where only the unchanged original fails (exact McNemar p < 0.001 for every agent). Therefore, the perturbation has a clear effect within the same rerun. The like-for-like comparison uses the same completion criteria: in the rerun, 93% of the unchanged originals are completed again, against 83% of their perturbed scenarios. On the full set, the drop is 10.3 points [5.7, 14.8].

Counting handling as well, a completed original fails 9.3% of the time [6.0, 13.5] when it is run again unchanged, against 47.1% for its perturbed scenario in the same rerun, a difference of 37.8 points [29.6, 45.7] that is above zero for each of the five agents. Both rates are over the originals completed in the first run, while the table's 46% conditions on the rerun's own originals. These two rates use different success criteria, so the same-criteria drop is the stricter comparison. Both show that the perturbation adds failure beyond run-to-run variation (Appendix D.5).

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Paper summary

In this paper, the authors proposed GroundWorks, an evaluation framework that tests whether language model agents remain robust when faced with plausible, realistic perturbations to tasks they can complete otherwise. The framework introduces 30 reusable perturbation operators organized into six families (Information availability, updates and consistency, and so on), and constructs paired scenarios: an original and a matched perturbed version differing by exactly one controlled change. The authors then evaluated five LLMs (GPT-5.6 Luna, Kimi K2.5, Claude Haiku 4.5, Ministral 3 14B, and Qwen3 32B) on the scenarios. The key finding is that agents fail on 47% of perturbed tasks they originally complete successfully, with failures split roughly evenly between targeted hallucinations and other handling failures. Tool capabilities and action outcomes emerge as the most challenging perturbation family, and distinct failure profiles across models reveal that original task success alone is insufficient to establish agent robustness. The framework also transfers to PatientAgentBench healthcare tasks, where failure rates rise to 57% with a 34% targeted hallucination rate.

Critical strengths
  1. The problem is well motivated and the paper is well written and easy to follow.

  2. The task design is done robustly. The paired evaluation design is methodologically clean.

  3. The formal hallucination taxonomy adds structure to the tasks and can be valuable in future research.

  4. The domain transfer to PatientAgentBench with minimal operator modification is a nice validation

Critical weaknesses
  1. The scale of the study is somewhat modest covering only 65 seed tasks and 208 pairs.

  2. Surprisingly the authors didn't test most large frontier reasoning models (e.g., o3, o4, Opus, etc.) rather used mostly small to medium models like GPT-5.6 Luna, Claude Haiku 4.5, Ministral 3 14B, and Qwen3 32B (except for Kimi K2.5). Without evaluation with larger and more capable frontier models, it's difficult to measure the severity of the problem.

  3. The evaluation apparently relies on an LLM judge, but the details are mostly missing from the main paper and disclosed in the appendix. A thorough human evaluation would strengthen the claims.

  4. The core finding of the paper is not surprising as agent brittleness under perturbation is well-established in recent studies [1, 2, 3, 4]. As a result, the empirical contribution feels incremental. The authors cited some of those works and at least one is missing to the best of my knowledge, however, the discussion lacks the details on how GroundWorks empirically advances beyond existing findings.

References:

[1] When Users Are Happy but Agents Are Wrong: Multi-Dimensional Evaluation of Tool-Augmented Dialogue. Shourya et al. 2026.

[2] AgentNoiseBench: Benchmarking Robustness of Tool-Using LLM Agents Under Noisy Condition. Wang et al. 2026.

[3] AGENTABSTAIN: Do LLM Agents Know When Not to Act? Liu et al. 2026

[4] QuestBench: Can LLMs ask the right question to acquire information in reasoning tasks? Li et al. 2025

Questions for authors

Please refer to the weaknesses section.

5 comments
AuthorsOpenReview ↗

Author Response, part 1 of 3

We thank the reviewer for recognizing that GroundWorks addresses a well-motivated problem and offers a methodologically clean and robust paired evaluation design. It also adds structure that future research can build on by formalizing a hallucination taxonomy. And the transfer to PatientAgentBench with minimal operator modification validates the framework's adaptability. We also appreciate the note that the paper is easy to follow.

We ran additional experiments and analyses. Please find the answers below. The revised PDF is also uploaded with changes marked in blue.

W1 (scale): We grew the study from 208 to 308 pairs, and the results hold (48% conditional failure for the five agents, against 47% in the submission).

Thank you for raising this concern. We expanded the study from 208 to 308 pairs and from 65 to 153 seed tasks, with each of the 30 operators now represented by at least five pairs. As the table below shows, the results remain consistent at this larger scale: all averages are within two percentage points of the original submission, and the five agents retain the same ranking. The larger study also supports our comparisons, with the main differences between agents and perturbation families remaining statistically significant.

Average of the five agents (%).

AverageOSO_SPSP_SPF,HP_{F,H}PF,¬HP_{F,\neg H}PS∣OP_{S\mid O}PF,H∣OP_{F,H\mid O}PF,¬H∣OP_{F,\neg H\mid O}
Submission (N = 208)70512424532522
Revision (N = 308)68502624522622

More importantly, the study can also keep growing, because our main contribution is the approach and not a fixed dataset. The operators can be applied to new benchmarks as they appear, which matters because older benchmarks risk contamination. Section 4.4 shows this on PatientAgentBench.

W2 (frontier reasoning models): We ran two more reasoning models, and the frontier one still fails ~20% of the time.

Great point! To measure the severity of the problem, we ran two reasoning models on all pairs, with the same pipeline and the same judge. We chose Claude Opus 5.5 and DeepSeek V3.2, which were highly ranked on the Artificial Analysis Intelligence Index and available to us.

The table below shows the results per agent (%). The two new models are in bold.

AgentOSO_SPSP_SPF,HP_{F,H}PF,¬HP_{F,\neg H}PS∣OP_{S\mid O}PF,H∣OP_{F,H\mid O}PF,¬H∣OP_{F,\neg H\mid O}
Claude Opus 5.5898012881118
GPT-5.6 Luna86621622641422
Kimi K2.577572518572716
DeepSeek V3.276562420582120
Claude Haiku 4.573582617592614
Ministral 3 14B59433126452926
Qwen3 32B46303140343631
Avg. of the five study agents68502624522622

Claude Opus 5.5 is the strongest model we tested. It completes 88.9% of the originals (OSO_S), and still fails 19.5% of the perturbed scenarios whose originals it completes (1 − PS∣OP_{S\mid O}). Its failure rate is lower than the other agents', but even the strongest model still hallucinates: more than half of its failures are targeted hallucinations (PF,H∣OP_{F,H\mid O} = 11%). Opus has the highest failure rates on false or unverified premises and on tool capabilities and action outcomes (31% each; Table 3). DeepSeek V3.2 fails 41.6% (1 − PS∣OP_{S\mid O}), about as often as Kimi K2.5 and Claude Haiku 4.5. The five study agents fail 48% on average, and all seven agents fail 43% on average (Table 2 of the revised PDF).

Additionally, we chose those five study agents because they are capable low-cost models. We selected them at the time of the experiments from the "Value leaders" on OpenRouter, among the models available to us. Such capable but inexpensive models are deployed at scale and as sub-agents, so studying their failures is important.

AuthorsOpenReview ↗

Author Response, part 2 of 3

W3 (judge details and human evaluation): The LLM judge evaluation details are now described in the main text, and we checked it with blind human annotation and a second judge.

Thank you for the suggestion! Section 3.3 of the revised paper now describes the two LLM judges in detail.

For the human evaluation, three annotators, all authors, labelled 120 perturbed episodes (two per episode) without seeing the judge's verdicts. Then a fourth author settled the disagreements. The sample covers the five agents and all 30 operators.

After weighting the sample to match the full set, the final human labels agree with the judge on 83.8% of episodes (kappa 0.72).

The table below gives the judge's precision and recall for each label, weighted to match the full set.

LabelJudge precision (%)Judge recall (%)
Handled94.383.9
Targeted hallucination77.882.8
Other failure63.884.7

The inter-annotator kappa between the human annotators is 0.60.

Conditional failure is 36.3% under human labels and 44.3% under the judge (Appendix E). The judge is generally stricter than humans when distinguishing failure from successful handling. However, even under human labels, agents fail in more than a third of scenarios whose originals they complete. Thus, the main finding holds under human labels.

As a further check, a second judge from another model family (GLM-5.3), independent of our evaluated agents, agrees with the original judge on 86.0% of cases (kappa 0.77) and ranks the five agents in the same order by conditional failure.

AuthorsOpenReview ↗

Author Response, part 3 of 3

W4 (novelty over [1]-[4]): GroundWorks extends the findings of [1]-[4] by identifying the types and causes of agent failures under perturbations.

Thank you for pointing us to these works. We agree that agent brittleness under perturbations is well established (Section 2). The submission already cites [2]-[4], and we have added [1]. Our contribution is not showing that agents are brittle, but identifying whether their failures are targeted hallucinations or other failures, and under which changes they occur. GroundWorks makes four contributions beyond [1]-[4].

1. A formal definition of hallucination for multi-turn agentic interactions that unifies prior taxonomies. Existing work disagrees on what counts as a hallucination. DiaHalu [5] includes arithmetic errors, whereas HalluHard [6] treats them separately. Our definition (Section 3.1.1) requires that a claim be asserted as fact, originate from the agent, and have premises not licensed by the four grounding sources. For example, stating a price the agent was never given is a hallucination, while miscalculating a supplied price is a reasoning error. We synthesize 22 subtypes from prior work, spanning tool calls, conversation history, and saved memory, and map each to a grounding source and mode (Table 1). These subtypes form the basis of our 30 operators. In comparison, [4] does not discuss hallucination, [2] and [3] mention it only in observations or case studies without measuring it, and [1] scripts three tool-output cases. None of [1]-[4] perturbs saved memory or world knowledge, which hold 44 of our 308 pairs. While [2] generates its noise adversarially against a reference agent, our perturbations model plausible events in real deployments, such as a tool failing or a user stating a false premise.

2. Operators that expose agent failures in domains they were not designed for. Each operator is defined by the grounding source it changes and the required response, not by a specific benchmark. On PatientAgentBench (Section 4.4), 19 operators transferred with minimal modification, covering all six families, and agents fail 57% of the healthcare scenarios whose originals they complete. For example, when a booking tool is removed, Claude Haiku 4.5 first says it cannot book the visit but later refers to a scheduled appointment, which does not exist. This lets GroundWorks evaluate agents on domain-specific and task-specific scenarios and surface their failure modes, which matters most in high-stakes domains such as healthcare.

3. Separate metrics for targeted hallucination, other failure, and task completion. For the five agents of the submission, of the 48 percentage points of failure, 26 are targeted hallucinations and 22 are other failures. Agents with similar failure rates also fail differently: nearly two thirds of failures by Kimi K2.5 and Claude Haiku 4.5 are hallucinations, compared to 38% for GPT-5.6 Luna. For example, when the return tool is removed, Kimi K2.5 tells the user that "the refund will be processed to your PayPal account within 5-7 business days" (a targeted hallucination), while Claude Haiku 4.5 calls the exchange tool instead, which the user never requested (other failure). These two failure types call for different mitigations. Additionally, task completion alone also misses hallucinations: even when agents complete a feasible perturbed task, 10.4% of these runs contain a targeted hallucination, such as guessing a value the agent was never given.

4. A paired design that separates what an agent cannot do from how it handles a change. 34% of perturbed failures occur on tasks the agent did not complete originally, which an unpaired evaluation would attribute to the perturbation. The results also show that higher original task success does not guarantee better handling of every change. Among the five agents of the submission, GPT-5.6 Luna completes the most original tasks (86%) and has the lowest failure rate when tools fail (44%, compared to 72% for Claude Haiku 4.5 and 68% for Kimi K2.5), yet it fails more often when information is missing or underspecified (36%, compared to 30% and 23%; Table 3). [3] also pairs its tasks and conditions on passing the should-act task, but this measures only the act/abstain decision, not a conditional task-success rate. [4] uses pairing only in an ablation, and [2] compares accuracy with and without noise without conditioning on the same agent's original. Among these works, only [2] also evaluates agents in live multi-turn conversations with a simulated user.

[5] https://arxiv.org/pdf/2403.00896

[6] https://arxiv.org/pdf/2602.01031

We thank the reviewer again for the detailed feedback. It has helped us strengthen the experiments and clarify our contributions, and we have incorporated these changes into the revised PDF. We hope the additional evidence and clearer positioning address the concerns, and we would be grateful if the reviewer would reconsider their score.

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Paper summary

This paper asks whether agents that complete multi-turn tasks can still handle plausible changes, such as revised requirements or incomplete tool results. To study this, GroundWorks constructs paired original and perturbed scenarios, with evidence and criteria for appropriate handling specified before execution. It then distinguishes targeted hallucinations from other failures and evaluates robustness on tasks the agent originally completed. Across the evaluated agents, nearly half of these perturbed scenarios end in failure. The authors also apply the framework to patient-facing healthcare tasks to examine its adaptability.

Critical strengths
  • The criteria are specified before execution: each operator identifies the affected claims, the relevant evidence, and what appropriate handling requires. This makes the distinction between targeted hallucination and other failure easier to interpret.

  • The evaluation identifies changes to tool capabilities and action outcomes as a particularly difficult setting across most agents (Tables 2 and 13), providing a useful direction for further robustness testing.

Critical weaknesses
  • The reported rates rely on the same model for scenario construction, simulated-user routing, and outcome judging. Table 9 includes human checks of perturbed outcomes and hallucination verdicts, but these come from a small pilot with one annotator who could see the verdicts. No blind human validation on the main evaluation set is described, so judge error in the headline results remains unclear.

  • The design does not fully separate sensitivity to perturbations from ordinary run-to-run variation. Each pair uses independent episodes, with no repeated-original or null-perturbation control reported, and original and perturbed success use different checks (Table 8). The uncertainty estimates also ignore dependence among scenarios derived from the same seed, making the smaller subgroup comparisons difficult to assess.

  • Minor: reducing the exccessive use of specific numbers, p-value, percentage, can largely improve the reading.

Questions for authors
  1. Would the agent ranking hold if a judge from another model family rescored a sample?
  2. Is there blind judge-human agreement on a sample from the main evaluation set?
  3. Do the reported paired differences remain reliable under a seed-level cluster bootstrap?
  4. Do you have failure rates for unperturbed reruns of completed originals?
4 comments
AuthorsOpenReview ↗

Author Response, part 1 of 3

We thank the reviewer for recognizing that GroundWorks makes the distinction between targeted hallucination and other failures easier to interpret by having the evidence and criteria fixed before execution. It also provides a useful direction for further robustness testing by characterizing empirically where agents fail and how the failures concentrate on tool capabilities and action outcomes.

We ran additional experiments and analyses to address the concerns. The revised PDF is also uploaded with changes marked in blue. We also expanded the study from 208 to 308 pairs by adding 100 pairs from nine benchmarks, and every operator now has at least five pairs. The results below are from this extended set.

W1, Q1 (judge from another model family): We tried a different judge model, and found that the agent ranking by conditional failure remains unchanged. The two judges agree on 86.0% of perturbed outcomes (κ = 0.77).

Thank you, this was a valuable check to add. We re-judged all episodes of the final run with GLM-5.3.

The table below shows the full results (%) on the 297 pairs both judges successfully score. GPT-6 Luna is the original judge and GLM-5.3 is the new judge. The last two columns show how often the judges agree on the perturbed outcome, with kappa, and the last row the rank correlation of the five agents between the judges. Agreement is at least 85% for every agent, which is high, and every kappa is between 0.70 and 0.80, which is substantial. The rank correlation is 1.00 (perfect) for five of the seven measures and at least 0.80 (strong) for the other two.

AgentOSO_S GPTOSO_S GLMPSP_S GPTPSP_S GLMPF,HP_{F,H} GPTPF,HP_{F,H} GLMPF,¬HP_{F,\neg H} GPTPF,¬HP_{F,\neg H} GLMPS∣OP_{S\mid O} GPTPS∣OP_{S\mid O} GLMPF,H∣OP_{F,H\mid O} GPTPF,H∣OP_{F,H\mid O} GLMPF,¬H∣OP_{F,\neg H\mid O} GPTPF,¬H∣OP_{F,\neg H\mid O} GLMAgreement between judges (%)Kappa
GPT-5.6 Luna8688637315112215647414102216850.70
Kimi K2.57782576325211816576327221515850.74
Claude Haiku 4.57275586626191615606727191414870.76
Ministral 3 14B5866434931272624445230252623870.79
Qwen3 32B4648303731294034344336303127860.80
Avg.6872505826212421526027212119860.77
Rank correlation between judges1.001.000.800.821.001.001.00

The judges agree on the perturbed outcome in 86.0% of cases (kappa 0.77) and on whether it is a targeted hallucination in 93.4% (kappa 0.82). In original scenarios, they agree on task success in 94.4% of cases (kappa 0.87).

We picked GLM-5.3 because it does not share a model family with any agent we evaluate. In particular, GPT-5.6 Luna stays the best of the five agents even under GLM-5.3, so its lead does not come from a judge of its own model family.

GLM-5.3 is the more lenient judge. Among cases where both judges score the original scenario as successful, GLM-5.3 scores 40.7% of perturbed scenarios as failures, compared to 48.1% under GPT-6 Luna. Both judges rank the agents in the same order by failure rate.

The other steps are separated too: a model from another family checks each pair, and the simulated-user model only selects stored replies under code checks (Appendix B.4, C.1). Moreover, Claude Opus 5.5 is the best agent in our experiments, so scenarios written by GPT-6 Luna do not make a GPT agent the best (Table 2 of the revised PDF).

AuthorsOpenReview ↗

Author Response, part 2 of 3

W1, Q2 (blind judge-human agreement): We ran a human study with blind annotators, and the final human labels agree with the judge on 83.8% of episodes.

We agree that blind human validation matters here. Three annotators, all authors, labelled 120 perturbed episodes that they had not seen before, without seeing the judge's verdicts, as handled, targeted hallucination or other failure. Each episode was labelled independently by two of them, and a fourth author settled the disagreements. The sample is stratified over the five agents and the judge's three outcomes and covers all 30 operators.

After weighting the sample to match the full set, the final human labels agree with the judge on 83.8% of episodes (kappa 0.72). For targeted hallucination, the judge's precision is 77.8% and its recall is 82.8%. Inter-annotator kappa is 0.60 and they agree on whether an episode contains a targeted hallucination in 86% of episodes.

As for the judge error in the headline result, on the sampled set, conditional failure is 36.3% under the human labels and 44.3% under the judge (Appendix E). The judge tends to be stricter than the human judgment when labeling something as failure vs handled. So absolute failure rates may be a few points lower than the judge reports, but even under human labels, agents still fail in more than a third of the scenarios whose originals they complete.

Table below counts the 120 sampled episodes by the judge's verdict (rows) and the final human label (columns).

Judge verdict / HumanHandledTargeted hallucinationOther failure
Handled3712
Targeted hallucination7285
Other failure14224

The table below gives the judge's precision and recall for each label, weighted to match the full set.

LabelJudge precision (%)Judge recall (%)
Handled94.383.9
Targeted hallucination77.882.8
Other failure63.884.7

W2, Q3 (dependence among scenarios from the same seed): The paired differences remain reliable under a seed-level cluster bootstrap.

Thank you for suggesting this test. We recomputed every confidence interval with a seed-level cluster bootstrap, which resamples whole seed tasks so that all scenarios built from the same seed task stay together. The paper now reports these intervals as its primary ones (Appendix D.4). The intervals barely change (table below).

ComparisonDifference (points)95% CI, pair level95% CI, seed-clusterReliable under seed clustering?
GPT-5.6 Luna hallucinates less than Kimi K2.5-15.4[-24.1, -7.1][-23.2, -7.4]Yes
GPT-5.6 Luna hallucinates less than Claude Haiku 4.5-16.5[-25.0, -8.5][-25.8, -8.7]Yes
Agents fail more on tool capabilities and action outcomes than on the other families+26[16, 35][15, 37]Yes
All 42 differences that are reliable at the pair level40 of 42 stay reliable

Even after grouping scenarios by seed task, the paired differences of Section 4.1 stay reliable. Their intervals barely widen because most seed tasks have a single pair. The smallest subgroups are the per-operator rates, and their intervals are typically no wider than before. Removing any single seed task changes the overall conditional failure on the 308 pairs by at most 0.9 points.

AuthorsOpenReview ↗

Author Response, part 3 of 3

W2, Q4 (run-to-run variation): We ran both scenarios again. An unchanged original fails 9.3% of the time, against 47.1% under the perturbation.

We appreciate the reviewer highlighting this. The original scenario is the same setup without the perturbation (aka null-perturbation control), so it controls everything except the variation between runs, which we measured directly.

In our rerun control, we reran both scenarios for 106 of the 308 pairs across all five agents (Appendix D.5). We selected a stratified random sample of approximately one-third of the pairs from each operator, covering all 30 operators. The table below compares the two runs for each agent using an exact McNemar test. All p-values are above 0.05, so none of the differences between the two runs is statistically significant.

AgentOriginal success, first run (%)Original success, rerun (%)McNemar pPerturbed failure, first run (%)Perturbed failure, rerun (%)McNemar p
GPT-5.6 Luna86851.0037400.63
Kimi K2.575810.0745470.79
Claude Haiku 4.574731.0042400.77
Ministral 3 14B64670.6361580.52
Qwen3 32B42450.5069650.39
All agents pooled0.190.65

Between the runs, original success changes by at most 6.6 points for any agent and perturbed failure by at most 3.8, and both runs rank the five agents in the same order by conditional failure. Averaged over the agents, perturbed failure changes by -0.9 points [-4.8, 3.1] and original success by 2.3 points [-0.6, 5.4], so on these measures run-to-run variation is at most about 5 points.

The two runs produce the same outcome on 80% of perturbed scenarios (κ = 0.67). Additionally, in 143 agent–pair cases, only the perturbed scenario fails, compared to just 11 where only the unchanged original fails (exact McNemar p < 0.001 for every agent). Therefore, the perturbation has a clear effect within the same rerun.

Run again unchanged, a completed original fails 9.3% of the time, against 47.1% for its perturbed scenario in the same rerun, a difference of 37.8 points [29.6, 45.7]. So the perturbation adds failure well beyond the variation between runs.

W2 (different checks for original and perturbed success): The checks differ by design: on feasible pairs, the original's task criteria are a subset of the perturbed criteria. Scored on the shared requirements alone, task completion still drops by 10.3 points.

About half of the perturbations (152 of 308 pairs) make the task infeasible, such as when a tool fails. In these cases, success means correctly handling the change, such as reporting the tool failure rather than falsely claiming task completion. The remaining 156 pairs require agents to both handle the perturbation and complete the original task. For example, if a value is missing, the agent should ask for it and then complete the task. On these feasible pairs, the perturbed scenario keeps the original's task success criteria and adds the handling criteria on top.

To check that the drop does not come from the added criteria, we scored both scenarios on the feasible pairs using only the task requirements shared by both. Agents complete 67.1% of original scenarios and 56.8% of perturbed scenarios, a drop of 10.3 percentage points [5.7, 14.8], so the perturbation lowers task completion even under identical checks.

The handling criteria also matter on their own. Even when agents correctly handle the perturbation, they still fail to complete the task in 28% of cases. Conversely, agents that mishandle the perturbation still complete the task in 33% of cases, sometimes through a lucky guess. Both outcomes count as failures under our evaluation.

W3 (Minor): Thank you for the suggestion. We have removed some of these extra numbers to improve readability.

We thank the reviewer again for the detailed feedback that made the results more reliable. We have incorporated these into the PDF. We hope these results address the concerns, and we would be grateful if the reviewer would consider revising the score. We are happy to answer any remaining questions.

Thank you again for your thoughtful review. As the discussion period closes tonight, we wanted to kindly note that we have addressed each of your concerns in our response, and we would be happy to answer any final questions you may have.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Rebuttal Summary

Dear Reviewers, ACs, SACs, and PCs,

Thank you for evaluating our submission and for the constructive feedback. The revised PDF is uploaded with changes marked in blue.


Strengths.

Reviewers recognized that GroundWorks evaluates agent reliability beyond task completion by checking whether agents' claims are supported by the available evidence, so models with similar success rates can be compared by the kinds of mistakes they make (4tTA). Fixing the evidence and criteria before execution makes the distinction between targeted hallucinations and other failures easier to interpret (3Gd1). Reviewers highlighted the robust task design and the methodologically clean paired design (7S2m), which tests agents in a controlled multi-turn setting where they can ask questions and use tools (4tTA). They also noted the formal hallucination taxonomy as valuable for future research and the transfer to PatientAgentBench with minimal operator modification (7S2m). Tool capabilities and action outcomes were identified as a particularly difficult setting across most agents, a useful direction for robustness testing (3Gd1). The paper was also found well motivated, well written, and easy to follow (7S2m).


Concerns addressed.

We ran the experiments and analyses the reviewers requested:

  • Judge reliability (3Gd1 W1, Q1-Q2; 4tTA W2, Q1-Q2; 7S2m W3): In a blind human study of 120 episodes, the final human labels agree with the judge on 83.8% of episodes (weighted κ = 0.72). The judge is stricter than the annotators, but even under human labels, agents fail in more than a third of the perturbed scenarios whose originals they complete, and the agent ranking stays the same apart from a swap between two close agents. Our human study is in line with published agent benchmarks, with a harder three-way label. We also rescored the episodes with a second judge from another model family, which agrees with the original judge on 86.0% of outcomes and ranks the agents in the same order. These checks show that the main findings hold under blind human labels and an independent judge.

  • Perturbation effect and statistical reliability (3Gd1 W2, Q3-Q4; 4tTA Q4): We reran the experiment on a stratified sample of 106 pairs, with both scenarios and all five agents. Completed originals fail only 9.3% of the time when run again, against 47.1% for their perturbed versions, so most of the failure comes from the perturbation, not from run-to-run variation. We also scored both scenarios on the same task requirements, and completion still drops under the perturbation. Finally, we recomputed the intervals with a seed-level cluster bootstrap, and the differences between agents stay reliable. This confirms that the paired design measures the effect of the perturbation and that its comparisons are statistically reliable.

  • Scale and model coverage (7S2m W1-W2; 4tTA Q5): We expanded the main study from 208 to 308 pairs, so every operator has at least five pairs, and the results and agent ranking hold. With PatientAgentBench, we evaluate 359 pairs, a scale comparable with related agentic benchmarks such as AgentAbstain. Because the operators do not depend on any one benchmark, the set can keep growing as new benchmarks appear. Even the strongest of two added reasoning models, Claude Opus 5.5, fails on about one in five perturbed scenarios whose originals it completes, mostly through targeted hallucinations. The findings are therefore not an artifact of the original sample, the framework extends to new tasks, and the problem persists even for frontier models.

  • Novelty and related work (7S2m W4; 4tTA W1, Q3): We compared GroundWorks with all seven works the reviewers cited. The submission already cited five of them, and the two we added are a workshop paper and a concurrent arXiv preprint. GroundWorks tests agents in multi-turn agentic interactions with a simulated user under plausible changes, such as a failed tool or a false premise. Under a unified formal definition, it scores targeted hallucination separately from other failures on paired scenarios, including feasible tasks. None of the seven does this. Our operators are benchmark-independent, so GroundWorks adapts to new domains and exposes their failures. For example, with the booking tool removed, an agent tells a patient it cannot book the visit, then later refers to an appointment that does not exist. The design also reveals what single-score or unpaired evaluations miss: 54% of failures are targeted hallucinations; 10.4% of completed feasible perturbed tasks still contain a targeted hallucination; and 34% of perturbed failures occur on tasks the agent already failed originally, which an unpaired evaluation would blame on the perturbation. GroundWorks therefore provides diagnostics that existing evaluations do not.


We hope these clarifications and new evidence address the reviewers' concerns. Thank you for your time and consideration.

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

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