- Rating
- 2(+1)
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 1
- Soundness
- 2
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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
- 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.
- 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
- 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.
- 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
- 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?
- 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
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.
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.
Reply to Authors
Thanks for the clarification. I have updated the score.
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.