- Rating
- 3(+1)
- Confidence
- 4
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
The paper studies test time scaling for agents in environments that cannot easily be copied or reset. Running several candidate trajectories directly in such environments can cause unwanted changes and interference between trajectories.
The proposed Agentic World Modeling framework predicts action outcomes through an interactive process. For each hypothetical action, a simulator gathers relevant evidence using read-only tools. It can also use Python to construct the predicted observation. Context isolated subagents handle these prediction tasks. Several candidate trajectories are generated using the simulated observations. The highest-scoring trajectory is then selected for execution in the real environment.
The evaluation covers -bench, AppWorld, and OfficeBench with three model backbones. The paper reports average improvements of 40.07% over SIMIA and 12.36 points over the trained world-model baseline where available. It also includes ablations for adaptive retrieval and Python execution. Further experiments study simulator-side scaling and token usage. A theoretical construction shows that adaptive retrieval can require exponentially fewer reads than non-adaptive retrieval when evidence is organized through a chain of dependencies.
Critical strengths
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The paper addresses an important limitation of agent test-time scaling. Many practical environments cannot support speculative writes from several parallel trajectories. Using read-only access to ground hypothetical rollouts is a useful direction. The distinction between retrieving evidence and reconstructing an observation is also sensible. Python execution can preserve exact document contents and structured values that an LLM might otherwise regenerate incorrectly. The theoretical analysis provides a clear example of why adaptive retrieval helps when each retrieved item identifies the next relevant item. The appendix explains that this is a worst-case separation rather than a guarantee for every environment.
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The empirical evaluation includes meaningful controls beyond the baseline comparison. AWM improves over both SIMIA and the trained world model across the reported settings in Table 1. Table 4 compares against a non-adaptive version with the same maximum read budget and Python capability. The token budget is also approximately matched. For GPT-5.4, adaptive retrieval improves AppWorld Level 3 success from 37.98% to 53.88%. OfficeBench 3 apps improves from 19.64% to 34.82%. These are substantial gains and provide direct evidence for adaptive evidence acquisition. Removing Python also consistently reduces performance. Finally, the reported task success is measured after execution in the actual benchmark environment. It is not based only on the simulator declaring its own trajectory successful.
Critical weaknesses
- Sec 3.1 states that the simulator reads from the unchanged initial environment. It infers the consequences of earlier hypothetical actions from the trajectory history. This is a central part of the method. Once a branch modifies or deletes an object, later reads from the real environment can conflict with that branch's state. The paper does not provide a concrete algorithm for reconciling these cases. Section 3.2 says that causal consequences are retained and mentions a TRACE interface. However, the representation of these consequences and the behavior of TRACE are not explained in enough detail to reproduce the process. This becomes particularly important when subagents return only compact results.
The evaluation in Appendix C.3 does not fully test this issue. It appends real observations to the history at every step. This is useful for measuring one-step prediction quality, but it avoids error accumulation across simulated transitions. All six qualitative examples also concern read operations. They show that retrieving real records helps recover missing information. They do not demonstrate consistency after several hypothetical writes. The end-to-end results provide indirect evidence on stateful tasks, but a direct analysis of read-after-write and write-after-write dependencies is still needed. The reported 41.1% prediction accuracy on AppWorld also makes this analysis important.
The final execution protocol is another unresolved detail. The paper says that the selected trajectory is committed to the real environment. It does not clearly state whether this means replaying a fixed action sequence or allowing the agent to revise its actions using real observations. These choices can lead to very different outcomes when simulation is imperfect. The issue is especially important for -bench because future user responses may differ from the simulated dialogue. Without this information, it is difficult to assess how the proposed simulation supports reliable execution.
- The SIMIA case studies repeatedly show that the fixed context omits the exact file or database records needed for the requested action. Appendix B.4 states that the baseline context constructor can access the same underlying information. However, the actual retrieval and serialization procedure is not described in enough detail to assess its quality. The large headline gain therefore combines the benefit of obtaining relevant evidence with any benefit from better simulation. Table 4 is a much stronger control and does support adaptivity. Still, the paper needs clearer baseline construction details before the 40.07-point headline improvement can be interpreted properly.
The simulator is also used to score completed trajectories. The reported results therefore combine changes in trajectory generation and trajectory ranking. They do not show how much of the gain comes from each. At BoN@1 there is no choice between candidates, yet large improvements are already present. This supports better simulated rollouts, but those gains should not be described only as better trajectory selection. A fixed-candidate evaluation with a common scorer would help separate these effects.
Several evaluation details are missing. Appendix C.3 reports observation prediction accuracy without specifying the matching rule. It is unclear whether this uses exact matching, normalized structured matching, or model-based judgment. The same section says that tasks are sampled from each benchmark but only reports accuracy for AppWorld and OfficeBench. The trajectory-scoring rubric and the aggregation of multiple simulator predictions are also not sufficiently described.
The efficiency evidence is narrower than the practical claims. Token usage is measured on 64 OfficeBench tasks. The rollout budget and simulator aggregation setting for this comparison are not clearly stated. There is no corresponding analysis of latency or environment-query overhead. The subagent ablation reports token savings but does not report whether prediction quality is preserved. These omissions matter because the method introduces several dependent simulator calls for each action.
Questions for authors
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How are hypothetical state changes represented and passed between prediction subagents? Can the authors show a complete example with several writes followed by reads. How does the simulator resolve a conflict between a branch's hypothetical state and the unchanged real environment? What exactly does TRACE return?
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How is the selected trajectory executed? Is it replayed as a fixed action sequence or does the agent replan using real observations? For -bench, how are simulated user responses handled when the real user simulator responds differently? Please provide the rollout and execution procedure.
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What matching rule is used for observation prediction accuracy in Appendix C.3? Is the simulator restricted to the pre-action environment state when predicting a mutating action? Can you report results separately for reads, writes, and reads that depend on earlier hypothetical writes?
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How are the fixed contexts for SIMIA and WM-Training constructed? Why do the examples omit files explicitly named in the action? Please provide the retrieval procedure and prompts. Also clarify which model acts as the task policy in the WM-Training comparison and whether the policy is held fixed across simulator variants.
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How are completed trajectories scored? Does the scorer use additional read-only queries? How are the M independent predictions aggregated? Can you separate trajectory-generation quality from ranking quality using a common candidate set or a common scorer?
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What N and M settings are used for the token-cost experiment? Does the accounting include all prediction and verification subagents? Please report environment-query counts and wall-clock latency. It would also help to report task success for the subagent ablation and uncertainty estimates for the main controlled comparisons.
Dear Reviewer ya5j,
Thank you again for taking the time and effort to review our paper! A quick reminder: the discussion period closes this Wednesday, November 18. If you have any remaining questions, we'd be happy to address them before the deadline!
Best regards,
The Authors