1.The differentiated contribution is narrower than the framing suggests. Profile inference, conditioning on user history, and soft-prompt personalization already have substantial precedent. The paper cites PERSOMA, Recon, and Latent Personal Memory, so this is not a claim that its recent literature coverage is absent. However, directly relevant USP (ACL 2025), HumanLM (2026), and Turing-RL (2026) are missing from the supplied manuscript [R1–R3]. These study inferred profiles or training objectives for individualized simulation. They do not duplicate the paper’s known-target KL evaluation, but they reduce the novelty of the broader motivation and require a sharper account of what new knowledge this particular protocol establishes.
2.The comparisons do not fully support the broader method-class conclusions. The three observational strategies are sensible first controls, and Figure 2(a) already compares KL at equal budgets of 1–25 conversations. However, the questionnaire and generation-attribution comparisons use 25 conversations for text methods and 200 for conversational soft prompts (Sections 5–6). Comparing models given vastly different amounts of data fails to isolate whether the performance gap stems from the representation/optimization strategy or simply from seeing more evidence. Furthermore, a single greedy prompt-inversion instruction that favors a committal description is a limited representative of text-based inference (Appendix C). A stronger evidence-grounded profile or a retrieval/selection-based candidate baseline would better test the Introduction's claim that user-specific optimization is required to capture the target conditional distribution. The empirical distillation references cannot by themselves identify all information revealed by conversations, as the paper correctly acknowledges that they are not theoretical upper bounds. Residual gaps mix elicitation, sampling, representation, and optimization effects.
3.Essential experimental choices require too much cross-referencing. Section 3 defines the observational access restriction, but understanding the complete pipeline requires combining the main results with Appendices B.2–B.4, C, G, and I. The five-token default is evaluated in the 1/5/10-token ablation in Figure 2(d), but the main text should point to this ablation when the parameterization is first introduced. More consequentially, observation budgets and checkpoint rules vary across results. The terminology around interaction length must be unified: Figure 2(a)’s “3 user turns” needs to explicitly map to Appendix C’s “three generated user responses” and clarify how this aligns with Appendix B’s depth convention, which counts the opening dilemma as a turn. A compact main-text table covering observations, targets, privileged access, selection, and evaluation budget would make the study substantially easier to assess.
[R1] Wang et al. 2025. Know You First and Be You Better: Modeling Human-Like User Simulators via Implicit Profiles. ACL.
https://aclanthology.org/2025.acl-long.1025/
[R2] Wu et al. 2026. HumanLM: Simulating Users with State Alignment Beats Response Imitation.
https://arxiv.org/abs/2603.03303
[R3] Wang et al. 2026. Learning User Simulators with Turing Rewards.
https://arxiv.org/abs/2606.19336