acceptodds
Withdrawn from ICLR 2027

Verified World-Model Repair for Long-Horizon Interactive Agents

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Long-horizon interactive agents can fail because a false belief about the world survives the very action that should disprove it. We introduce verified world-model repair, a framework that maintains a structured belief state, localizes action-conditioned prediction errors, converts them into scoped repair programs, and commits a repair to memory only after independent validation. A stepwise recovery specialist learns complete successful recovery trajectories rather than isolated next-action corrections. We also construct the World Evolution Dataset (WED), a family-disjoint dataset and paired-recovery protocol derived from 10,000 interaction episodes and 162,756 transitions. Across five random seeds on ALFWorld failure checkpoints, the full system recovers 169 of 185 cases (91.35%), compared with 109 of 185 (58.92%) for a strong goal-state controller. Learning only the first corrective action reaches 44.14%, whereas learning the full recovery trajectory reaches 90.99%. The method remains effective on held-out scenes, objects, and task templates, and reaches 93.69% on Qwen3-8B after development-only adaptation, while limiting harmful corrections to 3.6%. On frozen WebArena and OSWorld subsets, it improves programmatic task success over the strongest reflection baseline by 6.10 and 6.00 percentage points, respectively. These results indicate that reliable long-horizon recovery requires verifying a correction and carrying it through the remaining task, rather than merely revising the next action.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM agents, world-model repair, agent memory, long-horizon recovery, self-correction, computer-use agents

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_msJJOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper studies how long-horizon interactive agents can recover after an observation contradicts what they expected, and proposes a repair framework called EvoWorld. The framework keeps a task-local belief state and predicts the visible effect each action should have. When a new observation contradicts that prediction, or repeated actions on the same target make no progress, it builds a scoped repair program, executes it one step at a time, and checks each step against visible evidence. Repair records accepted during development are frozen and read as context at test time. The experiments have two parts that use different systems. On ALFWorld, the authors build the World Evolution Dataset, WED, and use its recovery data to train a LoRA recovery specialist on complete recovery trajectories, from a failure checkpoint to task completion; evaluation uses matched failure checkpoints split by task family. The full system recovers about nine in ten cases, clearly more than the paper's own goal-state variant, and learning complete trajectories clearly outperforms learning only the first corrective action. On OSWorld and WebArena, the system uses neither WED nor any training: a frozen backbone is combined with the repair controller and the frozen records, and it improves on the strongest baseline, AWM-offline, by about three percentage points. The paper uses different names for this method in its title, introduction and contribution list, so this correspondence has to be pieced together from the main text and the appendices.

Critical strengths
  1. Relating predicted visible effects to actual observations, and limiting repairs to the affected scope, is a useful way to avoid persisting with falsified beliefs or unnecessarily repeating completed subgoals. This is a practical, inspectable contribution to agent recovery.
  2. Methods resume from copies of the same failure checkpoint, with family-level bootstrap intervals and discordant-pair counts. External gains over AWM-offline are reported consistently across seeds, and negative or statistically uncertain cases are also disclosed. These features provide meaningful evidence and help readers assess both gains and limitations.
Critical weaknesses
  1. The paper argues that recovery requires correcting and carrying forward the agent's understanding of the environment, beyond changing its next action. However, an action failing to produce its expected effect may reflect a misclick, environmental delay, or execution error rather than an incorrect belief. The paper neither analyzes these failure causes nor removes belief repair while retaining state tracking and observable checks, so it does not isolate the proposed mechanism.
  2. The evaluation split and comparison settings limit conclusions about generalization and the sources of improvement. Appendix A.4 states that 30 of the 37 task families in the main ALFWorld evaluation contributed to candidate development. Pooling development and confirmation families means the roughly 90% recovery rate is not an independent confirmation-set estimate. The separation between frozen repair records and external evaluation tasks also needs clarification. The supervision comparison is confounded: complete-trajectory and first-action supervision differ by roughly 12× in training records, and two of the three first-action seeds select the initial checkpoint before recovery training. The performance gap therefore cannot be attributed to supervision span alone. Moreover, Full includes a learned specialist and controller rules on ALFWorld, but uses a frozen backbone, controller, and repair records on OSWorld/WebArena. The observable verifier in Table E4 is excluded from the final ALFWorld configuration, and the external evaluations lack component ablations. The experiments thus support the effectiveness of the overall system more directly than they establish the separate contributions of recovery learning, verification, additional data, and controller rules.
Questions for authors
  1. What are the Full-versus-Goal outcomes on the seven untouched confirmation families alone? Which reported evaluations or memory controls use the 30 design families?
  2. Which verification checks, semantic priorities, and stage-compatibility rules are active in the final Full system? Please distinguish them from the compiler/verifier excluded in Table E4 and identify what Goal and other baselines share.
4 comments
AuthorsOpenReview ↗

Response to Reviewer msJJ

Thank you for highlighting attribution, data separation, and configuration. We address W1-W2 and Q1-Q2 below. The abstract now consistently identifies the method as EvoWorld.

W1: Failure causes and targeted belief revision. A mismatch triggers diagnosis, not a presumption of incorrect belief. Appendix D.10 labels causes from pre-action belief, action return, and subsequent observation before inspecting controller success; ambiguous events remain other/uncertain.

On 100 shared event starts, both conditions have five executed actions to satisfy the local observable target (Table D12):

Results below list the control without targeted revision first, then Full.

Belief mismatch: 26/46 versus 42/46. Execution failure: 16/23 versus 18/23. Environment delay: 10/17 versus 11/17. Other/uncertain: 7/14 versus 8/14. Total: 59/100 versus 79/100.

The largest difference is in belief mismatch: 16 additional local recoveries among 46 events. Separately, the terminal-task control yields 63/111 without targeted belief revision versus 96/111 for Full. It disables diagnosis-driven revision of conflicting state while retaining ordinary state tracking, observations, visible checks, and the other repair components (Tables B4 and D10).

W2 / Q1: Confirmation families and experience sources. Section 5.2 and Table D9 separate the registry subsets:

Design (30 families): Goal 86/150; Full 134/150; gain 32.00 points.

Confirmation (7 families): Goal 20/35; Full 31/35; gain 31.43 points.

Combined: Goal 106/185; Full 165/185; gain 31.89 points.

The confirmation row contains 35 outcomes from seven families. Appendix A.4 specifies configuration freezing before confirmation evaluation, with no prompt, weight, or seed selection using its outcomes. The combined row is not an independent confirmation estimate.

The 36/9 parameter-training/development split is distinct from the 30/7 design/confirmation registry. Primary evaluation uses all 37 families; supervision, components, and controller comparisons use the specified three-seed sets. Table A6 identifies the memory control as leave-family-out evaluation on the 30 design families: each target family's trajectories and outcomes are excluded from its own memory construction and selection, which use the other 29 families. Fresh-error and sealed-program controls have separate task lists.

External memories use designated development interactions, exclude formal evaluation records from generation and screening, and retain environment-qualified source identifiers. Files are frozen and read-only during evaluation; Full reads at most the first 12 records in fixed order. Task-local state updates do not write back (Appendix B.2; Table A6).

W2: Supervision imbalance and update-0 selection. The source pools remain 60 and 714 records. The revised comparison instead uses 122-slot views from the same 60 recovery groups, identical group allocation and reading order, initialization, optimizer, and 480 updates. First-action slots repeat each group's first correction; complete-recovery slots sample its available stages. Both are evaluated at update 480, removing the specific update-0 selection difference.

Figure 3 and Table D3 report 65/111 (58.56%) versus 91/111 (81.98%), a 23.42-point difference. The matching concerns sampled-view size and update count, not identical source diversity or token totals. This supervision result is separate from the primary model's 96/111 three-seed result (Tables A4-A5; Appendix C.1).

W2 / Q2: Active rules, verification, and benchmark instances. Table C7 states shared and distinct operations. Full, Goal, and RH share observations, environment-action limits, and terminal scoring. Full filters stage-compatible executable candidates, ranks them with the recovery scorer, and uses semantic priorities for ties. Goal updates completed stages and remaining conditions; RH maintains a program and execution ledger. Full's runtime acceptance is distinct from action legality and terminal scoring. The additional compiler/verifier in Table E4 is excluded; the online target check remains active.

Removing online acceptance gives 83/111 versus 96/111 (Table D10). Table D11 separates frozen-policy/full-controller, learned-scorer/minimal-controller, and joint configurations at 73/111, 70/111, and 96/111.

ALFWorld tests learning plus control; external instances test control and experience reuse with frozen parameters. Table F6 adds the requested external controls:

The following rates are OSWorld first, then WebArena.

Full: 27.98% and 29.99%. Without memory: 25.76% and 27.78%. Without online repair: 24.10% and 25.91%. Without visible verification: 26.50% and 28.02%.

Controls share the main task lists, three runs, 20/30-action limits, and Full outcomes. The negative error-factor holdout is retained.

Reviewer_msJJOpenReview ↗

Reply to Authors

Thank you for the detailed responses.

Weakness 1 is largely addressed. Weakness 2 is partially addressed. But the representation of the reply and the paper has space to improve. It is too difficult to understand. There are some issues in the revised paper. For example, the mean steps are missing in Table 2/H2. Also, the main results have changed. It is better to explain why. For these reasons, I would maintain the score.

AuthorsOpenReview ↗

Clarification of Revised Results and Manuscript Corrections

Thank you for your follow-up and for acknowledging that Weakness 1 has been largely addressed. We apologize for the issues in the previous revision.

Due to an oversight, we uploaded an incomplete manuscript version, resulting in missing numerical values and some internal configuration labels. We have corrected these issues, completed the mean steps in Tables 2 and D2 and the confidence intervals in Tables H1 and H2, and improved the clarity of the relevant descriptions.

Regarding the changes in the main results, Reviewer ywiY raised concerns about model selection fairness, while Reviewer msJJ identified imbalances in supervision data volume and checkpoint selection. We therefore revised the experimental protocols, standardized the relevant selection procedures, and reran the affected experiments. The updated results reflect these changes, while the main conclusions remain consistent.

We apologize for not explaining these changes clearly in our previous response. The corrected manuscript includes the completed results and clearer explanations, with revisions highlighted in red.

Thank you again for your constructive feedback.

Reviewer_msJJOpenReview ↗

Reply to Authors

Thanks for the clarification. I have updated the score.

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

This paper investigates inaccurate state beliefs and failure recovery in long-horizon interactive agents. It combines state repair, observable verification, and training on complete recovery trajectories, and constructs the WED data and a paired recovery evaluation protocol. The method is evaluated on ALFWorld, WebArena, and OSWorld, with a focus on whether agents can continue to complete the remaining task after correcting an error.

Critical strengths
  1. The research problem has practical value, and the method is designed around the complete recovery process. Long-horizon interactive agents must not only detect and correct errors but also continue to complete the remaining task after a correction. The paper integrates error localization, local state repair, observable verification, and subsequent recovery execution. It particularly emphasizes confirming repair outcomes through visible evidence after execution while retaining completed subgoals. These designs address practical problems such as persistent incorrect beliefs, repeated operations, and further failures after error correction.

  2. The recovery evaluation protocol is reasonably designed and provides valuable mechanism analyses. All methods start from independent environment copies at the same failure checkpoint, operate under the same interaction budget, and use ultimate task completion as the criterion for successful recovery. WED partitions the data by task family, helping to reduce the risk of leakage from related trajectories appearing across splits. The paper also examines complete recovery supervision, verification memory, and repair-program matching, providing some basis for understanding the role of each component.

  3. The complete system achieves favorable experimental results across multiple environments. Table 2 shows that Full achieves a recovery rate of 91.35% on ALFWorld, compared with Goal's 58.92%, while the average number of interaction steps decreases from 13.85 to 10.52. Table 4 shows that Full's task success rates on OSWorld and WebArena exceed those of AWM-offline by approximately 3.23 and 3.34 percentage points, respectively. These results demonstrate gains in recovery success and execution efficiency and support the overall framework's applicability across different interactive environments.

Critical weaknesses
  1. The distinctions from prior work and the additional contributions have not been sufficiently established. Prior studies, such as AdaPlanner [1] and AgentRefine [2], have addressed feedback-based correction after failure and training on error-correction trajectories. Although the paper discusses some related work, it does not sufficiently explain which mechanisms and capabilities state repair, observable verification, and complete recovery training add relative to those methods. It therefore remains difficult to determine whether the contribution primarily consists of systematically integrating existing ideas or constitutes a clear methodological innovation.

  2. The existing experiments do not directly validate the key differences sufficiently. The paper presents valuable mechanism analyses of complete recovery supervision, verification memory, and repair-program matching, but has not sufficiently established the advantages of the new designs over existing feedback-based repair and recovery-training methods. For example, the comparison between complete recovery supervision and first-action supervision supports the importance of learning the subsequent recovery process, but does not directly establish its incremental value over existing training on error-correction trajectories. More targeted comparisons or ablations would help clarify the magnitude of the contribution.

  3. The model or configuration selection procedures lack sufficient transparency, limiting attribution of the performance gains. Figure 2 presents a development-set selection procedure, and the appendix provides some selection settings. However, it remains unclear whether EvoWorld-Goal and the other main comparisons in Table 2 received comparable selection opportunities, particularly in terms of the number of candidates, selection criteria, and tuning budgets. If the selection conditions differ across methods, part of the performance difference may arise from the selection process. The current report is therefore insufficient to determine the extent to which the performance gains stem from the method itself and whether the comparisons are sufficiently fair.

References

[1] Haotian Sun, Yuchen Zhuang, Lingkai Kong, Bo Dai, and Chao Zhang. AdaPlanner: Adaptive Planning from Feedback with Language Models. In Advances in Neural Information Processing Systems, volume 36, pages 58202–58245, 2023.

[2] Dayuan Fu, Keqing He, Yejie Wang, Wentao Hong, Zhuoma GongQue, Weihao Zeng, Wei Wang, Jingang Wang, Xunliang Cai, and Weiran Xu. AgentRefine: Enhancing Agent Generalization through Refinement Tuning. In International Conference on Learning Representations, pages 65185–65204, 2025.

Questions for authors
  1. What are the key new mechanisms in this paper relative to prior work? Please specify how the proposed approach differs from AdaPlanner [1] and AgentRefine [2] in state repair, observable verification, and recovery training, and what capabilities these differences provide that the earlier methods lack or have not fully realized.

  2. Which experiments directly validate the value of these new mechanisms? How do the existing mechanism analyses support the paper's advantages over existing feedback-based repair and error-correction training methods? Could you provide comparisons or ablations targeting the key differences to further distinguish the contributions of the individual designs, rather than only demonstrating improvements in the complete system's performance?

  3. Are the selection conditions comparable across the main methods, and do the main advantages hold after controlling for the selection process? Please report the number of candidates, development data, selection metrics, and tuning budgets for EvoWorld-Goal and the other main comparisons in Table 2, and explain their comparability with Full. For methods that require training, could you provide comparisons at a fixed number of training steps? For methods that require configuration tuning, could you provide results under equivalent selection conditions?

2 comments
AuthorsOpenReview ↗

Response to Reviewer ywiY

Thank you for recognizing the recovery problem, matched-checkpoint evaluation, and mechanism analyses. We address the distinctions, targeted evidence, and selection conditions below.

W1 / Q1: Distinctions from AdaPlanner and AgentRefine. Section 2 and Table B3 now state these connections explicitly. AdaPlanner performs feedback-based in-plan/out-of-plan refinement, assertion checks, and breakpoint continuation. AgentRefine learns from multi-turn error-and-correction trajectories and masks loss on erroneous turns. We do not claim that feedback, continuation, or correction trajectories are new individually.

EvoWorld organizes recovery around an affected entity, location, or active subgoal, a persistent local program, and a target-related acceptance condition. Its learning component constructs candidate-action scoring records from successful suffixes following fixed failure checkpoints. Evaluation asks whether recovery continues through completion of the remaining task, rather than stopping at the first correct action. Sections 3.2-3.4 make these execution and learning decisions explicit.

W2 / Q2: Evidence targeting the mechanisms. The revision links each design to a specific control. On 37 families and three seeds, Full reaches 96/111. Removing explicit scope gives 87/111; removing the persistent program gives 83/111; removing online acceptance gives 83/111 (Figure 4 and Table D10). Table B4 specifies the single disabled operation and retained components. Weights, initial visible inputs, failure states, and action budgets remain shared.

The local scope analysis separately compares 101/120 successful repairs with scope against 78/120 without it under a common five-action endpoint (Table D13). This is not pooled with terminal-task recovery.

The revision also includes the two closely aligned controller comparisons identified in the reviews. Under the same seed-matched recovery-trained OpenCUA-7B checkpoint, Table D14 reports 74/111 for prompting-based EVU, 68/111 for manual-guided AutoManual, and 96/111 for Full. Appendix C.6 specifies the adaptations. These are common-weight controller comparisons; the internal ablations examine individual operations.

W3 / Q3: Selection conditions and fixed-update supervision. We agree that the original selection description was insufficiently explicit. Section 5.1, Appendix C.1, and Table C6 now distinguish learned-checkpoint selection from fixed inference configurations:

Primary Full: checkpoints at updates 0, 240, and 480; 480 recovery updates.

First-action and complete-recovery controls: fixed update 480; 480 updates each.

Inference-only methods, including Goal and RH: one preset configuration; no additional recovery updates.

EVU and AutoManual adaptations: one adaptation using shared Full weights; no additional recovery updates.

Full selects by terminal recovery on common starting points from the same nine development families; ties retain the earlier checkpoint. Fixed methods have no configuration sweep. Weights, prompts, experience, and rules are frozen before formal evaluation. This reports the different selection opportunities explicitly, rather than calling them identical searches.

The supervision control removes checkpoint-selection differences: both views are evaluated at update 480, with the same initialization, optimizer, 60 source recovery groups, 122 sampled slots, and group-level reading schedule. First-action slots repeat the earliest correction; complete-recovery slots sample available later stages. Both continue to the same terminal criterion and action budget.

First-action supervision: 19/37, 22/37, and 24/37 for seeds 17, 29, and 43; total 65/111 (58.56%).

Complete-recovery supervision: 28/37, 31/37, and 32/37 for the same seeds; total 91/111 (81.98%).

The reported difference is 26 endpoints, or 23.42 points (Figure 3; Tables A4-A5 and D3). Repeated slots are not counted as independent source records. This is an internal supervision comparison, not a performance comparison against AgentRefine.

Table 2 reports 165/185 for Full versus 106/185 for Goal, a 31.89-point difference between complete configurations. The fixed-update supervision and shared-weight controller/component comparisons provide the more specific evidence separating recovery learning and controller operation. Detailed candidate settings, controls, and results are now cross-referenced in the main text.

Thank you for the detailed response and the clarifications in Table B3, Table D14, and Appendix C. However, my main concerns remain:

Novelty relative to AdaPlanner and AgentRefine. The response acknowledges that feedback-based correction, continuation, and correction trajectories are not new individually. The remaining distinctions (organizing the recovery around a scope, a persistent local program, and target-related acceptance) are mostly about how existing ideas are combined. This does not change my view that the contribution lies mainly in system integration.

The key differences are still not tested against AdaPlanner or AgentRefine. The new controller comparison covers EVU and AutoManual, not the two methods I raised. The comparison of first-action and complete-recovery supervision (65/111 vs. 91/111) is an internal ablation, as the response itself states, not a comparison against AgentRefine-style training. The incremental value over these methods therefore remains unclear.

Selection conditions still differ across methods. Thank you for reporting the selection settings explicitly. They show that Full selects among multiple checkpoints using development-set recovery, while Goal and the other inference-only baselines use a single preset configuration. The fixed-update ablation separates selection effects only within the paper's own supervision variants. The main Table 2 gap (165/185 vs. 106/185) is still not compared under equivalent selection conditions.

I will therefore keep my current rating.

Reviewer_GVWBOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes EVOWORLD, a method for recovering from persistent incorrect beliefs in long-horizon agents. It combines explicit belief tracking, action-effect prediction, scoped repair with observable verification, reusable repair memory, and complete-recovery supervision. The paper also introduces the World Evolution Dataset (WED) and a matched-checkpoint recovery protocol. The approach is evaluated on ALFWorld, OSWorld, and WebArena, with additional ablations examining supervision, memory, and generalization.

Critical strengths

The matched-checkpoint recovery protocol is well aligned with the problem being studied. It starts each method from the same failure checkpoint and evaluates terminal task completion. Thus, the protocol focuses on whether an agent can recover from a failure and complete the remaining task. This provides a meaningful empirical framework for studying recovery, independently of my concerns about the proposed method and its comparisons.

Critical weaknesses

W1. The substantive contribution beyond closely related prior work is unclear.

EVOWORLD combines an online recovery mechanism with offline repair memory. However, prior work has explored both components. The online recovery mechanism overlaps with EVU (https://arxiv.org/abs/2604.17252), which the paper does not discuss, while the offline repair memory overlaps with the "Corrected Error" rules in AutoManual. It is therefore unclear what substantive contribution EVOWORLD makes beyond these two approaches.

Q1. Does the online recovery mechanism constitute a substantive contribution beyond EVU?

EVU studies belief inertia. It explicitly maintains a belief state, predicts action outcomes, verifies them against environmental feedback, and updates the belief accordingly. EVOWORLD is motivated by a highly similar failure mode, and likewise maintains explicit beliefs, predicts the target-related effect of an action, compares the prediction against the subsequent observation, and initiates a correction when the observation contradicts the expectation (Contribution 1).

EVOWORLD additionally introduces a "repair scope" and an explicit "repair program." However, the manuscript does not establish why these additions constitute a substantive advance over EVU-style belief updating.

  1. Repair scope (Section 3.2). EVOWORLD introduces repair_scope, defined as the entity, location, or subgoal to reconsider. However, I could not find a description of how this scope is constructed. Appendix B.1 similarly states only that the controller forms "a diagnosis, a scope, and a short repair program." How is the repair scope determined? What benefit does explicitly localizing the repair scope provide?
  2. Repair program (Section 3.2). EVOWORLD constructs a short repair program and executes it step by step, obtaining new observations between actions. Why is this necessary, rather than simply updating the belief and continuing to plan, as in EVU? What additional failure mode does this mechanism address?

Since both methods are evaluated on ALFWorld, a matched comparison with EVU on this benchmark, using the same failure checkpoints, backbone, and evaluation conditions, would directly test whether these additional online recovery mechanisms provide value beyond belief updating.

Q2. Does the offline repair memory constitute a substantive contribution beyond AutoManual?

EVOWORLD stores reusable repair experience by recording where the repair applies (scope), when the repair should be triggered (signal), what correction should be performed (repair), and when the repair should be considered complete (verification). I view this offline repair memory as substantially overlapping with the "Corrected Error" rules in AutoManual, which similarly record where a correction applies, what error requires correction, and how the error should be handled.

  1. What capability does EVOWORLD provide beyond AutoManual's "Corrected Error" rules? I recognize that EVOWORLD uses a more explicit representation by separating repair experiences into scope, signal, repair, and verification fields. However, it is unclear whether this more structured representation constitutes a substantive contribution in itself. The clearest distinction appears to be the verification field, which specifies when a reused repair should be considered complete. If this is the key advance, what failure mode does it address, and what evidence demonstrates its additional value over AutoManual-style corrective memory?
  2. Why is AutoManual not included as a baseline? AWM-offline is a reasonable baseline. However, AutoManual is more directly aligned with the failure-specific corrective memory emphasized by EVOWORLD. AutoManual is also evaluated on ALFWorld, making a direct comparison feasible. Such a comparison would be more diagnostic of the memory contribution than the current comparison with AWM alone.

W2. The proposed system differs materially across evaluation settings.

The paper evaluates EVOWORLD across ALFWorld, OSWorld, and WebArena. However, the systems evaluated in these settings differ materially in their core components.

In ALFWorld, recovery-specific learning plays a central role. OpenCUA-7B is adapted using LoRA with complete-recovery supervision, and the resulting complete-recovery specialist is used to rank candidate actions. In OSWorld and WebArena, this recovery-specific training is not used. The OpenCUA-7B backbone remains frozen, and the system uses the repair controller with frozen development experience.

Thus, the main ALFWorld result evaluates a system incorporating a learned complete-recovery specialist, whereas the OSWorld/WebArena results evaluate a different instantiation based on a frozen controller and offline repair memory. I understand that these systems share the same high-level interaction loop. However, the major components driving their behavior differ, making it unclear which methodological claims are supported by each set of results.

Q3. What justifies the substantially different configurations across benchmarks? Why is recovery-specific training used on ALFWorld but omitted on OSWorld and WebArena? Given these differences, what constitutes the core method of EVOWORLD, and how should the results across these benchmarks be interpreted as evidence for the same methodological contribution?

Questions for authors

Please see weaknesses.

1 comment
AuthorsOpenReview ↗

Response to Reviewer GVWB

hank you for recognizing the matched-checkpoint protocol and identifying the closest related methods. We address your questions below.

Q1: Contribution beyond EVU and matched comparison. We apologize for omitting EVU from the original discussion. Section 2 and Table B3 now acknowledge its explicit estimation, verification, and belief updating. EvoWorld's focus is the execution of local recovery: scope limits what is reconsidered, a persistent program retains the repair sequence and current step, and an observable acceptance condition governs advancement and return to the original task.

Section 5.6 and Table D14 add a prompting-based EVU adaptation. EVU, AutoManual, and Full use the same seed-matched, recovery-trained OpenCUA-7B weights, restored failure states, visible prefixes, task goals, checkpoint action budgets, and terminal evaluator. Each constructs its own control state. Every executed helper-function subaction counts toward the action budget; reasoning calls are accounted for separately. This compares controller adaptations under shared learned weights, not differently trained original checkpoints.

EVU prompting adaptation: 74/111 recoveries (66.67%).

AutoManual manual-guided adaptation: 68/111 (61.26%).

EvoWorld-Full: 96/111 (86.49%).

Full's reported gains are 19.82 points over EVU and 25.23 over AutoManual. Adaptation details appear in Appendix C.6 and Table C8.

Q1.1: Scope construction and benefit. Section 3.2, Appendix B.1, and Algorithm B1 specify the procedure. The model proposes a conflicting target from the observation, preceding action and expected effect, active subgoal, and eight-step history. The controller selects the smallest supported entity, location, or subgoal scope. A conflicting property of a known target uses entity scope; an unlocated target or incorrect page/window uses location scope; incompatible stage prerequisites use subgoal scope. Ambiguous evidence leads to re-observation or localization, while unrelated completed subgoals are retained.

Removing only the scope restriction yields 87/111 versus 96/111 for Full (Table D10). On a separate set of 120 matched local-repair starts, explicit scope reaches 101/120 versus 78/120 without scope constraints, under the same five-action local endpoint (Table D13). Local repair and terminal task completion are reported separately.

Q1.2: Why retain a repair program? Correcting the belief that a dialog is open does not reopen it. Recovery still requires locating its entry, opening it, and checking the new view. The program preserves that sequence and its current step; observed effects determine whether to advance, re-localize, or resume the task. Removing the program object and step pointer while retaining scope and observation checks yields 83/111 versus 96/111 (Tables B4 and D10). This targets persistent execution state rather than belief updating alone.

Q2: AutoManual, corrective memory, and verification. Section 2 acknowledges that AutoManual already has applicability scopes, corrective rules, and verification records. Our distinction is how a record governs the current repair: its signal triggers use, its scope constrains the target, and its acceptance condition determines whether execution may resume. A returned click or changed screen can leave the intended dialog absent; target-related evidence prevents this attempted correction from being accepted prematurely.

The AutoManual adaptation retains its planner and a development-built manual frozen before evaluation. Its shared-weight result is given above. Separately, removing online acceptance yields 83/111, and removing frozen memory yields 82/111, versus 96/111 for Full. The acceptance control retains fresh observations, action legality, state updates, and terminal scoring; the memory control retains the online repair loop. Thus, the overall AutoManual gap is not assigned to a single field. The separate memory control remains 39/90 with verified memory versus 29/90 for both no memory and stale memory (Table D4).

Q3: Different benchmark configurations. Section 3.5 distinguishes a shared state-expectation-repair-acceptance loop from recovery-specific learning. ALFWorld evaluates the learned scorer jointly with this loop; OSWorld/WebArena keep model parameters frozen to assess control and experience reuse across interfaces, not transfer of the ALFWorld specialist itself. Table D11 separates frozen-policy/full-controller, learned-scorer/minimal-controller, and joint configurations: 73/111, 70/111, and 96/111. Section 5.7 and Table F6 also isolate external memory, online repair, and visible acceptance under the same frozen backbone. These additions link each methodological claim to its corresponding evaluation.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Author Response: Summary of Revisions

Dear Area Chair and Reviewers,

Thank you for the careful reviews and for recognizing the matched-checkpoint recovery protocol. We have revised the manuscript around three priorities: the contribution relative to closely related methods, transparent training and selection conditions, and the respective roles of recovery learning, local control, and frozen experience.

Main changes. The revision clarifies how repair scope is constructed and how observable acceptance governs repair execution; adds common-weight controller comparisons with prompting-based EVU and manual-guided AutoManual; and provides targeted internal and external component analyses. It also compares first-action and complete-recovery supervision at a fixed training checkpoint, separates the seven confirmation families from the 30 design families, and clarifies the roles and sources of frozen experience.

The revised tables report Full versus Goal at 165/185 versus 106/185; complete-recovery versus first-action supervision at 91/111 versus 65/111; and confirmation-only outcomes at 31/35 versus 20/35. Table D14 reports 96/111 for Full, 74/111 for the EVU adaptation, and 68/111 for the AutoManual adaptation under the same learned weights and matched recovery conditions.

The main text remains within ten pages, with changes marked in red. Detailed responses are provided under the three individual reviews. All section, figure, and table references in our replies refer to the revised manuscript. Thank you for helping us make the method and its evidence clearer.

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

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