acceptodds
Under review as a conference paper at ICLR 2027

LLM Agents Mistake Success Elsewhere for Completion Here

Abstract

Testing operations in isolated environments before production execution is a standard safety practice. When an agent retains this test history, can it correctly determine what still needs execution in the target environment, even when the history explicitly identifies where each operation occurred? We evaluate 13 deployments on controlled transformations of 60 public tasks from the benchmark family and AppWorld, preserving native tools and authentic receipts. We assess actual effects with native state checks and completion claims with human-validated LLM annotation. With complete environment mappings recorded separately from receipts, successful rehearsal history raises false completion claim rates from 1.9% to 79.7% on and from 7.7% to 69.9% on AppWorld, compared with matched pre-execution controls. The increase occurs in all 13 deployments on both task sources. Copying the already available environment relation beside its receipt reduces these rates to 18.6% and 24.7%, respectively, and substantially improves completion of the required operation. Changing receipt formatting alone produces no comparable reduction. These results show that truthful history and complete execution-scope information do not ensure correct decisions about what still needs execution. Success is environment-specific: reliable continuation requires applying that scope to both actions and completion claims.

Primary area:
foundation or frontier models, including LLMs
Keywords:
large language model agents, tool use, execution scope, agent evaluation, execution histories

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_r6bfOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper identifies an acion integrity failure mode where agents mistake success elsewhere as succuss in current environment, with experiments on 60 adapted tasks and 13 models. Evaluations show that existing model has high false completion claim rate, and providing information on environment relatoin mitigates this failure and improves the completion rate.

Critical strengths

Identified and evaluated an action integrity failure mode in LLM agents, where agents mistake successful operations in the testing environment for the task completion in another execution environment.

Critical weaknesses

The evaluation only covers 60 unique task, with 36 from tau-bench and 24 from AppWorld, and only has single run per task for each model. Though the author emphasizes 780 runs in total, which may give a misleading impression on the statistical robustness, these evaluations are repeated on a narrow set of tasks that limit the reliability of the conclusions.

Questions for authors

Section 3.2 remains unclear why there're only 36 tasks selected from tau-bench and 24 from AppWorld, which are small numbers that limit the statistical robustness of the conclusion. Are these the only tasks that meet the selection criteria?

2 comments

Thank you for asking us to strengthen task coverage and repeatability. We now report three repeated runs on all 60 original tasks and a separate extension to 30 additional public tasks, both on six fixed deployments. Both reproduce the false-completion failure and the execution benefit of the local full join. Section references point to the revised manuscript.

1. Task coverage and statistical units

The main study has 60 source task instances (36 tau, 24 AppWorld). Across 13 deployments, each condition contains 780 task–deployment episodes; 12 conditions give 9,360 episodes. Section 3.4, Table 2 and Appendix D now distinguish these quantities explicitly. Statistical inference resamples tasks within each source, keeping each task's paired conditions and deployment measurements together rather than treating 780 rows as independent tasks. The six-deployment repetition and additional-task panels are reported separately with their own denominators.

2. Why 36 tau and 24 AppWorld tasks?

We fixed the 36-task tau and 24-task AppWorld allocation before collecting the reported model continuations, balancing source/operation coverage, native-qualification workload and API cost within the available candidate inventory. These were practical panel-size targets, not limits on task eligibility.

The tau screen identifies 690 structurally eligible instances; the selected 36 cover airline, retail and telecom and ten target APIs. The 24 AppWorld tasks cover distinct generator families across five applications. All 60 selected tasks passed independent native qualification: the reference execution succeeds, omitting the target write fails, and restoring it recovers success. Section 3.2 and Appendix A give the source-based selection rules and audit scope.

To assess whether the findings depend on this panel or a single rollout, we added 30 disjoint public tasks and three repeated runs on all 60 original tasks, both on six fixed deployments. The results below show that the false-completion failure and the benefit of the local full join persist.

3. Replication on 30 additional public tasks

We selected and natively qualified 30 disjoint tasks before collecting their new model outcomes, using fixed source-based ranking and round-robin rules: 24 new tau instances within the main study's operation types, and six AppWorld instances from six generator families absent from the main panel. All have passing native references, a necessary target operation, a state-distinguishing query and an executable recovery path. Task state, tools, inference settings, budgets and scoring are fixed across paired conditions.

Six deployments and one rollout per task–deployment–condition give 180 initially-incomplete episodes per arm:

OutcomeDistributedLocal full join
False completion claims120/18024/180
Native target completion41/180149/180
Official whole-task success41/180147/180

The ordinary pre-execution control yields 2/180 false claims and 160/180 native target completions, showing that the tasks are executable without the rehearsal-success history. The local full join reduces false claims by 53.3 percentage points (source-stratified task-cluster 95% interval [46.1, 60.0]) and increases native completion by 60.0 points [53.9, 66.1]. Both outcomes improve in each source-level and deployment-level summary. Section 4.5 and Appendix B.7 (Tables 20–21) report this cohort separately: coverage spans 90 tasks, with a 13-deployment core and six-deployment extension.

4. Stability across three repeated runs

We concentrated the supplementary evaluation on six deployments to prioritize repeated runs and targeted controls while retaining coverage across developers and tool interfaces. The main study retains all 13 deployments. On all 60 main-study tasks, we ran pre-execution, distributed and local full join conditions three times on GPT-5.5, GPT-5.6-sol, DeepSeek-V4-Pro, Kimi-K2.6, grok-4 and gpt-oss-120b: 360 initially-incomplete episodes per condition per run.

RunFalse claims: distributed/local full joinNative completions: distributed/local full join
1248/4989/299
2246/5491/296
3253/5686/293

The false-claim reduction is 53.3–55.3 points in every run. Pooled false claims fall from 747/1,080 to 159/1,080; native completions rise from 266/1,080 to 888/1,080. The paired reduction is 54.4 points (task-cluster 95% interval [49.3, 59.5]); resampling tasks and shared run indices gives [48.9, 60.0]. Pooled outcomes improve in each source-level and deployment-level summary. Section 4.5 and Appendix B.2 (Tables 12–13) provide the breakdowns. Together, these repetitions and the disjoint task extension strengthen robustness beyond a single rollout on the original panel.

Thank the authors for the clarification and additional experiments, which better support the conclusion. I am inclined to boardline accept given that these revisions has been integrated into the manuscript. A side note that it's better to highlight the revisions in the manuscript with other colors, which would enhances the readability.

Reviewer_srZnOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies how LLM agents mistake success in a rehearsal environment for completion in the current environment. Across 60 tasks and 13 deployments, false completion claims rise sharply despite complete scope mappings. Placing scope information beside the relevant tool result reduces errors and improves execution. The findings highlight the gap between having correct information and using it correctly.

Critical strengths
  1. Clear distinction between complete scope information and its correct use. An important failure mode in agent memory.
  2. A practical problem for testing, switching environments, and resuming tasks. Truthful tool results may still be irrelevant to completion in the current environment.
Critical weaknesses
  1. Only one rollout per task–deployment–condition. Run-to-run variability remains unknown.
  2. F=A(1-S) captures a claim–state mismatch, but not its cause. I would like to see a corresponding breakdown of false-claim trajectories in the rehearsal conditions: no attempted write, a failed or incorrect write, or an effect that was subsequently changed. This would better support the interpretation that agents leave required operations undone.
  3. Table 10 is heavily Yes-dominated. Despite the sensitivity analyses, reliability on No and Unclear cases remains uncertain. The revised labeling rules also lack independent validation.
Questions for authors
  1. Are the effects stable across repeated runs? Could results be broken down by history length, operation type, and use of state queries?
  2. Any examples of explicit environment comparison or state checking? Do these behaviors explain differences between the distributed, local pointer, and full join conditions?
  3. The comparison with the ordinary pre-execution control changes both the success history and the surrounding context: the ordinary controls omit cross-environment metadata. A control with the same environment setup and comparable history length, but without a successful rehearsal of the focal operation, would help determine how much of the increase is specifically attributable to rehearsal success. This concern does not directly affect the distributed-versus-local-join comparison, which retains the same underlying facts. Could you add a control with the same environment mapping and similar history length, but no successful rehearsal? This would help separate success-result effects from additional context.
  4. How would local join compare with an explicit environment-ID check, followed by required state verification on a mismatch? Please consider both accuracy and extra tool calls.
1 comment

Thank you. References are to the revised manuscript.

1. Repeatability

On all 60 main-study tasks, we repeated pre-execution, distributed and local full join three times on GPT-5.5, GPT-5.6-sol, DeepSeek-V4-Pro, Kimi-K2.6, grok-4 and gpt-oss-120b: 360 initially-incomplete episodes per arm/run, with fixed settings/budgets.

RunFalse claims: distributed/local full joinNative completions: distributed/local full join
1248/4989/299
2246/5491/296
3253/5686/293

False-claim reductions are 53.3–55.3 percentage points per run. Pooled false claims: 747→159/1,080; native completions: 266→888/1,080. Reduction: 54.4 points (task-cluster 95% interval [49.3, 59.5]; shared-run sensitivity [48.9, 60.0]), with gains by source and deployment (§4.5; B.2).

2. Paths to false claims

Main-study distributed false claims, target initially absent:

Observable pathtauAppWorld
No new tool proposal25521
Other calls, no business-write proposal105181
Target API proposed, effect absent at end013
Other write or unclassified API proposals143
Total false claims374218

Omission precedes claims in 360/374 and 202/218 cases. Write or unclassified API proposals exclude a case from this group, even if undispatched. The other 30 contain attempted writes or unresolved paths. No logged intermediate completion precedes final absence; some AppWorld paths lack complete state coverage (§4.1; B.3).

3. Background-matched control

Of 20 fixed candidates, 17 support native non-target reads with unchanged state and identical before/after responses; three lack one and were excluded before model calls. Across six deployments and three runs, replacing only the target-success call/receipt lowers false claims from 225/306 to 11/306 and raises native completion from 78 to 282. Mapping, earlier history, request/approval, tools, initial state and message count/order stay fixed. Median absolute character-length change is 1.41%; tokens are not matched. The success record matters beyond shared background (§4.5; B.2).

4. Independent annotation validation

To test underrepresented No/Unclear cases, two humans independently blind-labeled 200 main-study replies outside the submission's 904-response validation sample, using the clarified rubric without other labels/native scores or AI.

Judge labelCountH1 matchesH2 matches
Yes103102103
No803635
Unclear1731

Raw judge–human agreement is 70.5%/69.5%; human–human agreement is 87.5%. No/Unclear disagreements remain. Weighting for their oversampling estimates 97.11%/97.98% agreement over the 8,130 main-study replies initially labeled only by the judge, not accuracy.

Substituting either human's original labels changes four main contrasts (distributed versus pre-execution/local full join, by source) by at most 0.43 points. The maximum weighted shift estimate is 1.41 points, not a bound. All directions persist despite class-wise disagreement.

After blind labels were locked, authors adjudicated 65 disagreements with AI-assisted text inspection. Uniform checks of 16,736 nonempty main/supplementary replies covered cross-message sentence continuations and task-defined monetary tolerances. Together these change 83 labels and nine false-claim outcomes; native outcomes stay fixed. These clarifications lack blind revalidation (Appendix C; Tables 22–24).

5. History, operations and state checking

The local full join reduces false claims in all five source/history-length groups and 28/29 source/API groups; the other has none in either arm (B.6). These strata are descriptive, not randomized. In distributed/local pointer/local full join order, episodes with an interface-filtered read are 170/207/193 on tau, versus 70/311/352 native completions (468 per arm); AppWorld gives 90/94/102 versus 79/217/222 (312 per arm). Gains do not simply track more queries (B.5). Outside these counts, a GPT-5.4 case reads roaming as disabled, attributes this to synchronization delay, omits the enabling call, yet reports completion (C): reading need not imply using target evidence.

6. Verification and tool cost

Can a verification prompt substitute for local full join? With fixed tools/budgets: 20 tasks × six deployments × three runs (360 per arm).

OutcomeDistributedLocal full joinVerification
False claims2556068
Native completions96293262
Mean dispatched calls1.482.054.51

Verification helps; the local full join completes more with 2.46 fewer calls (95% interval [1.96, 3.07]). The false-claim difference is unresolved, not equivalence. This prompt requests unconditional, agent-executed verification, not ID-triggered checking; its cost cannot be assigned to that policy (§4.6; B.4).

Reviewer_GvV4OpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
2
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2
Read review
Paper summary

The paper asks whether an agent that keeps a history of test runs can tell what still needs to be done in the target environment. The authors adapt 60 tasks from the τ benchmarks and AppWorld. In each one, the focal operation succeeded either in an isolated rehearsal copy or in the real task instance, and the agent sees a complete and truthful call-to-environment mapping before the history. Across 13 deployments, a successful rehearsal receipt leads to many more false completion claims than a pre-execution control does. Copying the same scope relation next to the receipt cuts these claims sharply and improves actual execution, while a plain JSON wrapper does not help. Effects are checked against native state, and claims are labeled by an LLM judge validated against two human annotators.

Critical strengths
  1. The design is clean. All renderings carry the same facts and differ only in how that information is presented. Actual effects come from native state rather than model text, and claims are scored separately. The already-executed world and the post-execution control rule out the simple reading that the intervention just makes agents repeat calls.
  2. The effect is large and shows up in every deployment on both sources. The appendix gives full per-model counts, task-cluster bootstrap intervals and annotation sensitivity checks.
Critical weaknesses
  1. I am not sure how realistic the setting is. The failure depends on a specific setup: rehearsal and target calls are mixed in one trajectory, and the mapping only appears as a header before the history. In real pipelines these would often be separate sessions, or the agent would be told directly. Figure 1 is schematic, and I could not find a verbatim model input in the paper or appendix.Please add at least one full verbatim input per source, and discuss or test a more natural case, for example rehearsal results passed in as a summary from a separate session.
  2. The paper is hard to read. There are many custom terms (value-complete, relationally complete, binding, directory, focal, distributed, the two worlds) and I had to go back and forth to follow them. Section 5 feels loosely tied to the main story. Related work is thin and misses work on agents overstating task success and on state tracking in long-running agents.
  3. The contribution feels narrow and the paper gives little mechanism. The main fix is to move existing text next to the receipt, which is close to known long-context usage problems. There is no analysis of why agents fail: whether they ever look at the mapping, what their reasoning shows, or whether reasoning effort matters. Two baselines are missing: a condition with no mapping at all, and a plain instruction to check current state before claiming completion.
Questions for authors
  1. What is the exact text of the resumption request and the approval turn? Does the approval refer to the rehearsal in any way?
  2. What happens if the mapping is removed entirely? If the rate is close to the distributed condition, models are basically ignoring the header.
  3. Would a plain instruction to check current state before claiming completion get close to the local join result?
  4. On the public tasks under the distributed condition, how often do agents issue any state query before claiming completion?
1 comment

Thank you. We added handoff, no-mapping and verification tests, complete inputs and trajectory analyses. References point to the revision and anonymous supplement.

1. Prior-session handoff and realism

We test whether session separation prevents the error when a new session receives exported rehearsal records. Receipts and mappings are quoted as user text rather than assistant/tool messages, avoiding summarization loss. On 20 tasks (ten per source), six deployments and three runs, each arm has 360 initially-incomplete episodes with fixed initial state, tools, settings and budgets. Handoff reduces false claims from 252/360 to 125/360. Within handoff, the local full join copies existing scope beside receipts, adding no observation or answer: false claims fall to 36/360 (24.7 percentage points; task-cluster 95% interval [20.6, 28.6]), native completion rises from 227 to 316, and official task success from 220 to 300.

Handoff alone nearly eliminates errors for GPT-5.5 and GPT-5.6-sol (0 and 1/60); the other four retain 20–49/60, reduced to 1–26/60 by the local full join. Thus failure extends beyond native-role history, while handoff mitigates it for some deployments (§4.4; B.1).

2. Complete inputs; approval and resumption

Appendix A.1 gives the texts below; the supplement's inputs/ provides complete examples per source, matched variants and tool schemas. AppWorld includes a decoder and marked synthetic-credential masking. The tau example's exact approval is:

Yes, I confirm those operation details and payment choices. The other recorded customer operations were also agreed.

The exact resumption request in both examples is:

Please continue the customer task from this checkpoint using the available tools, then respond to the customer.

Neither mentions rehearsal. Approval authorizes choices, not completed execution; AppWorld has no added approval turn. Separate mapping and isolation instructions specify historical locations and the current connection.

3. Readability and related work

We replace “focal” and “two worlds” with “target operation” and “initially absent/present,” define terms before use, introduce conditions in §3.3, and clarify panel baselines/denominators. Section 5 makes live execution a prerequisite for a completion tool, testing premature completion as an action, not only a text label. Section 2 adds false-completion work (Advani, 2026) and cross-session state-memory work (Fan et al., 2026). Our comparison preserves truthful receipts and complete scope facts while testing their use in execution and reporting.

4. Mechanism and omitted action

Replacing the target-success call/receipt with a native non-mutating read lowers false claims from 225/306 to 11/306 on 17/20 prespecified tasks, six deployments and three runs. Three tasks had no qualified replacement, excluded before collection. Mapping, earlier history, approval, initial state and message count/order stay fixed, not exact tokens (§4.5). This tests the success record beyond background. In main distributed false-claim trajectories, 360/374 tau and 202/218 AppWorld cases propose no business write (§4.1; B.3). The local full join helps in every history-length group, including at most eight calls (B.6); wrapping helps little and end-copy leaves more errors. Inference settings remain fixed; we do not vary reasoning effort or systematically code verbalized comparisons. Together, these behavioral tests link out-of-scope success to omission and scope presentation to better execution.

5. Does checking current state suffice?

It helps substantially. A separate matched panel has 20 tasks, six deployments and three runs (360 episodes per arm):

OutcomeDistributedLocal full joinVerify
False claims2556068
Native completions96293262
Mean dispatched calls1.482.054.51

The prompt requests current-state checking, warns against importing success elsewhere and permits qualified reporting. The local full join completes more with fewer calls; the false-claim difference is unresolved (+2.2 points for verification, 95% interval [-2.8, 7.2]), not equivalence (§4.6; B.4).

6. State queries before claims

Among affirmative terminal claims in main initially-incomplete distributed episodes, 159/443 tau (35.9%) and 83/292 AppWorld (28.4%) have a logged business-state read. Reads may concern another subtask, so these are not successful-verification rates (B.5).

7. Removing the mapping

Against the matched native-role baseline, removing only historical call-to-environment assignments raises false claims from 252/360 to 284/360 (+8.9 points, 95% interval [3.9, 13.9]); native completion falls from 96 to 61. The increase is concentrated in tau (124 to 154/180), versus 128 to 130/180 on AppWorld. Removing header assignments thus affects behavior on tau; AppWorld shows little change here (B.1).

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

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