- Rating
- 3(+1)
- Confidence
- 3(+1)
- Informativeness
- 3(+1)
- Presentation
- 3
- Soundness
- 2
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Paper summary
The paper compares humans and agents on 30 cognitive tasks to test whether process features provide more discriminative information than aggregate performance. It collects data from 97 retained human participants and three frontier agents. On three text-compatible tasks, it then compares Centaur, action-level fine-tuning, and process-level fine-tuning. Process features improve discrimination, while the benefits of directly optimizing them are largely specific to the supervised features and tasks.
Critical strengths
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The question has practical relevance. When agents and humans achieve similar task scores, interaction behavior can provide information that final accuracy misses. The paper turns this question into a concrete cognitive-task battery.
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The evaluation covers varied tasks and actual human behavior. The 30 tasks span decision-making, memory, perception, and planning, including both CAPTCHA and structured behavioral paradigms. This reduces dependence on a single challenge.
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The separation of observed, left-out, and cross-task evaluation is useful. The paper shows substantial gains on supervised features and reports their decline on new features and tasks. This negative transfer result is more informative than reporting only the highest fool rate.
Critical weaknesses
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The central framing is broader than the comparison performed. The output baseline in Section 2.4 receives one aggregate performance metric per task, while the process classifier receives multiple trajectory features. This establishes that detailed behavior contains information beyond a scalar score. It does not establish superiority to output-based approaches generally, since behavioral sequences are also system outputs. The paper should identify which additional observations provide the advantage and what they add over richer output representations. Otherwise, the process-versus-output distinction suggests a stronger result than the experiment supports.
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The process features may partly reflect interaction protocols rather than cognitive mechanisms. Agents receive screenshots and issue JSON actions that Playwright executes, while humans interact directly with the interface. Seeing the same page does not give both groups the same information flow or action organization. Click order, exploration paths, and update frequency can therefore differ for interface-related reasons. The acknowledged video-input limitation is relevant, but related protocol effects may also affect performance-matched tasks. Confirming key results through a common text/action interface would strengthen the process interpretation.
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P-SFT uses an important approximation for sequential behavior. Sampled actions shape subsequent prompts, but gradients do not pass through those history choices. Updates therefore come primarily from probability-based feature estimates on visited histories, without the full effect of changing earlier choices on later histories. This is understandable for local measures such as stickiness. Its implications are less clear for learning slopes, exploration, and other trajectory-level features.
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A fixed detector's fool rate does not separate human alignment from detector distribution shift. Fine-tuned models are excluded from detector training. Their higher fool rates could reflect closer human behavior, but also incorrect extrapolation on an unseen agent distribution. Transfer attacks against a fixed detector are valid experiments. A broader claim of reduced distinguishability needs a detector trained on some adapted runs and tested on independent runs. Also, the 13 matched tasks are defined by failure to detect a performance difference; that should be distinguished from established output equivalence.
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It seems that the AI USE STATEMENT is missing.
Questions for authors
None
6 comments
A polite ask for reviewer's feedback on our rebuttal
Dear Reviewer R3rx,
Thank you for your feedback and suggestions. We have posted detailed responses and additional experimental results addressing your concerns, and would appreciate your thoughts on whether these resolve the points raised. We would be happy to clarify any remaining questions.
Best regards, The authors
Thank you for the additional analyses. The richer-output baselines address my concern in W1, and including adapted runs in detector training reduces my concern in W4. I still have questions about W2 and W3. For W3, your finding that “estimates and rollout measurements agree closely” checks feature values, while my concern was about “the full effect of changing earlier choices on later histories”. What evidence addresses the omitted gradient contribution? For W2, does the “common API text interface” also align human observations and action representations, or is it shared only across models? Also, why does removing process features change median output |d| from 0.08 to 0.17? Please clarify whether the same tasks and runs were used.
We thank the reviewer for their comments, and address each below:
1. Single-metric baseline and richer outputs.
We address this in two steps. First, we equated dimensionality by comparing classifiers using one output and one process feature, selecting the most discriminative one. A single process feature remains more discriminative on most tasks (feature selection used only each fold’s training data):
Second, we used every per-trial outcome as a richer output representation. Process features still significantly improve discrimination:
Regarding which processes provide additional information, we grouped process features into interpretable categories:
Error structures (+0.07 AUC, gains in 8/11 tasks) and exploration (+0.12, 3/3) provided the most consistent gain to the richer output alone (note that categories apply to different task subsets).
2. Potential interaction-protocol confounds; test a common text/action interface.
We tested this interpretation by ablating all features that could in any way be explained by how the browser harness acts (all timing, cursor-trace, and click-order features) and compared it to our full result set. Even with this broad ablation, process features still distinguished humans and agents on tasks where their outputs showed no significant difference (Mann–Whitney p > .05; median output |d| = 0.17 vs original |d| = 0.08): mean AUC was 0.80 versus 0.87 with all features.
We also reran frontier agents through the common API text interface on the three fine-tuning tasks. Substantial process distances and low fool rates persist:
3. Gradients through sampled histories and trajectory-level features
We tested whether the approximation distorts trajectory-level targets by comparing the probability-based feature estimates used in training with the same features measured from the model's actual sampled choices (1.5B P-SFT, 200 rollouts per task). For example, for IGT task, we compared second-half minus first-half good-deck probabilities with the corresponding difference in observed choice proportions.
The estimates and rollout measurements agree closely:
The only systematic difference is in deck entropy (1.29 vs. 1.21) consistent with finite-sample bias from 10 choices (observed entropy closely matches humans (1.21 vs. 1.23)). Agreement on trajectory-level estimates and held-out improvements over A-SFT in learning and exploration support that the approximation is adequate for these tasks.
4. Detector shift and output equivalence.
Excluding adapted models intentionally tests transfer evasion against a detector trained on humans and base agents, which we believe is appropriate for our paper's core question. Including adapted runs in detector training reduces fool rates, but P-SFT retains a substantial advantage over A-SFT: 52.4% versus 29.6% of runs are classified as human on independent held-out runs:
“Output matched” denotes no significant output difference (Mann–Whitney p >= .05), not established equivalence. We will revise the wording.
5. AI use statement. We apologize for the oversight, and will add the statement.