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Under review as a conference paper at ICLR 2027

Process Matters more than Output for Distinguishing Humans from Machines

Abstract

Reliable human-machine discrimination is becoming increasingly important as Large Language Models and autonomous agents are deployed in online settings. Existing approaches largely evaluate whether a system can produce behavior or responses indistinguishable from those of a human. This approach follows the focus on the *output* of a machine as a criterion for determining whether it can think, as suggested by Alan Turing. Cognitive science provides an alternative approach: considering the *process* by which that behavior is produced. To evaluate whether differences in cognitive mechanisms can reliably distinguish humans from machines, we introduce a process-based framework, the *Process Turing Test*, and evaluate it across a battery of cognitive tasks spanning decision-making, working memory, and planning. These tasks, such as *mental rotation* and *sequence prediction*, yield process-level measures that reveal how behavior is generated, complementing conventional measures of overall task performance. We also include multiple CAPTCHA tasks in the battery to compare the experimental paradigms to challenges deployed in the real-world. Across the battery, process-level features provide substantially stronger discriminative signal than performance metrics alone, reliably distinguishing humans from agents even when task performance is matched (mean process-feature classifier AUC = 0.88). To assess agentic process limitations, we conduct a controlled red-teaming study comparing off-the-shelf frontier agents (Claude Sonnet 4.5, GPT-5, Gemini 2.5 Pro), Centaur (a large language model fine-tuned on 10.7M human decisions), and two task-specific fine-tuning methods applied to models of different sizes and families: **action-level supervised fine-tuning (A-SFT)** and **process-level fine-tuning (P-SFT)**, which directly optimizes process features. We find that broad fine-tuning on human choices makes task processes more human-like relative to off-the-shelf frontier agents, and task-specific process-level fine-tuning further improves human-like behavioral mimicry, though this advantage largely disappears under cross-task transfer when process targets do not naturally generalize across tasks. These results highlight process specification as a central bottleneck in achieving human-like cognitive processes in machines.

Primary area:
applications to neuroscience & cognitive science
Keywords:
human–machine discrimination, LLM agents, Process Turing Test

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_R3rxOpenReview ↗
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
  1. 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.

  2. 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.

  3. 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
  1. 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.

  2. 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.

  3. 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.

  4. 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.

  5. It seems that the AI USE STATEMENT is missing.

Questions for authors

None

6 comments

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):

Task setSingle output AUC (CV mean)Single process AUC (CV mean)# tasks favoring process
All tasks0.640.7621/30
Output matched0.510.7010/13
Output unmatched0.720.8011/17

Second, we used every per-trial outcome as a richer output representation. Process features still significantly improve discrimination:

Task setRicher output AUCOriginal process AUCCombined AUC (gain)
All (30)0.860.870.92 (+0.06, p = .001)
Matched (13)0.770.870.89 (+0.12, p = .005)

Regarding which processes provide additional information, we grouped process features into interpretable categories:

  • error structure (biases, swaps, intrusions)
  • condition effects (performance variability by task manipulation)
  • exploration (information search)
  • learning
  • trial-to-trial dependencies (win-stay/lose-shift, stickiness)

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:

AgentRun|d| Sampling|d| IGT|d| WCST|d| meanFool rate (%)
GPTPaper0.271.911.911.367.6
GPTText0.332.031.281.212.0
GeminiPaper1.260.561.381.070
GeminiText1.210.540.930.900
ClaudePaper1.153.320.481.650
ClaudeText1.052.930.521.5015.0

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:

  • IGT learning slope: 0.095 vs. 0.085 (difference +0.010; 95% CI [−0.030, 0.049]).
  • WCST learning slope: −0.123 vs. −0.122.
  • WCST perseveration cost: 0.183 vs. 0.180.

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:

ModelOriginal fool rate (%)Adapted-detector fool rate
Centaur4424
A-SFT 1.5B / 7B / 14B / 32B / 70B27.5 / 52.5 / 38.5 / 47.5 / 45.5%20 / 37 / 29.5 / 38 / 23.5
P-SFT 1.5B / 7B / 14B / 32B / 70B74 / 68 / 52.5 / 45 / 90.5%60.0 / 59.5 / 39 / 40 / 63.5
A-SFT mean42.329.6
P-SFT mean66.052.4

“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.

AuthorsOpenReview ↗

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.

Reviewer_pBMEOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes a Process Turing Test that distinguishes humans from AI agents using process-level behavioral features from cognitive tasks. The authors collect data from 97 human participants and three frontier agents across 30 tasks. On tasks designated as output-matched, process-feature classifiers achieve a mean AUC of 0.88, compared with 0.55 for output metrics. The authors then compare Centaur, action-level supervised fine-tuning (A-SFT), and process-level fine-tuning (P-SFT) on the Iowa Gambling Task (IGT), Wisconsin Card Sorting Task (WCST), and Information Sampling Task. P-SFT improves alignment on observed features and increases classifier fool rates; its advantage over A-SFT attenuates on left-out features and largely disappears under cross-task evaluation.

Critical strengths
  1. The task battery and human–agent comparison have empirical value. The 30 tasks span multiple cognitive domains and combine human data with runs from GPT-5, Gemini 2.5 Pro, and Claude Sonnet 4.5. Directly comparing output metrics with process-level features illustrates that substantial discriminative information can remain beyond aggregate task performance.

  2. The evaluation of process supervision and its generalization limits is informative. Comparing Centaur, A-SFT, and P-SFT across observed features, left-out features, and cross-task evaluation helps assess how strongly improvements in behavioral matching depend on the process representation directly optimized during training.

Critical weaknesses
  1. Insufficient positioning relative to prior work. The paper lacks a systematic Related Work discussion, particularly comparisons with CogBench and BeCAPTCHA-Mouse. The former already studies LLM behavior beyond aggregate performance, while the latter uses interaction behavior for human–bot detection. The specific advances in the task battery, process supervision, and generalization analysis therefore remain unclear.

  2. Incomplete task-performance comparisons and limited evidence across model families. Although authors report base-model classifier fool rates, complete task-performance comparisons among base Qwen/Llama models, fine-tuned models, and humans on IGT, WCST, and Information Sampling are missing. This limits interpretation of how process alignment relates to changes in task performance. Moreover, numerical cross-task fool-rate gains over the base models occur for Qwen, whereas Llama 70B changes from 18.4% to 16.0% with A-SFT and 18.0% with P-SFT. Results from four Qwen models and one Llama model provide limited evidence of consistency across model families.

Questions for authors
  1. Could authors systematically compare with CogBench and BeCAPTCHA-Mouse and clarify the specific contributions beyond related works?

  2. Could authors report task performance for the base models, A-SFT, P-SFT, and humans on all three tasks, separating within-task and cross-task settings?

  3. I suggest adding one representative model from another family under the same protocol, matching scale and training budget, to assess robustness across families.

5 comments

We thank the reviewer for their comments, and address each below:

1. Insufficient positioning relative to prior work (CogBench and BeCAPTCHA-Mouse)

Thank you for this comment, we agree that this work should be discussed in a related work section. In particular: CogBench (Coda-Forno et al., 2024) shows that performance can conceal behavioral differences, but our approach builds on this by providing a direct process-targeted adaptation and quantifying how much this contributes to agents evading detection. Furthermore, our work provides a controlled test of how transferable the adaptation is to features excluded from supervision or to other tasks.

BeCAPTCHA-Mouse (Acien et al., 2020) uses a completely different set of behavioral targets - behavioral biometrics like mouse movements, scrolling, and typing, which introduces potential interaction confounds expressed by Reviewers LCcY and R3rx. We will update our related work section and citations.

2. Adding additional model family and output table

We ran additional experiments with Llama models (1B, 3B, and 8B, alongside the existing 70B runs) and Gemma 4B. Results are largely consistent with the Qwen family models (anonymized links: distance results; classifier results).

Below is the table of outputs comparing humans, base models, A-SFT, P-SFT averaged across model sizes with SEM reported:

ModelConditionWCST accuracyIGT ($ earned)Sampling ($ earned)
Humans—0.56 (0.01)208 (11)0.12 (0.20)
Base models—0.45 (0.04)243 (26)1.93 (0.93)
A-SFTWithin task0.48 (0.01)215 (20)0.10 (0.48)
A-SFTCross task0.43 (0.03)232 (18)2.04 (0.84)
P-SFTWithin task0.53 (0.04)209 (8)0.06 (0.32)
P-SFTCross task0.45 (0.03)223 (10)1.90 (0.91)

Questions

Q1. Please see response #1.

Q2. Please see response #2.

Q3. Please see response #2.

AuthorsOpenReview ↗

A polite ask for reviewer's feedback on our rebuttal

Dear Reviewer pBME,

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

Dear Reviewer pBME,

We would appreciate your feedback on whether our responses and additional analyses address your concerns. Please let us know if any points need further clarification.

Best regards, The authors

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

The paper tries to match the processes of cognition rather than just the final output behavior when comparing humans to LLMs. This is a very welcome addition to the eval literature in order to improve LLM social simulation and our understanding of human behavior through reverse engineering and cognitive modeling with LLMs.

Critical strengths

As I mentioned, I really like premise with the process over results framing. There needs to be more research on this direction and more cognitive scientists and neuroscientists collaborating with AI researchers.

The task battery is large with 30 tasks across perception, working memory, and decision-making

The generalization hierarcy from observerd to left out to cross-tasks is useful and demonstrates that directly optimizing summary statisitcs does not learn the underlying mechanisms in a generalizable way

Critical weaknesses

The short trial duration threatens psychometric validity of process features: To keep the task short, they only have 10 trials. In classical psych studies, tasks like the Iowa Gambling task have 100+ trials. This is too short to measure learning slope or hit rate meaningfully. Similarly in the Wisconsin Card Sorting Task there are 10 trials and non-zero statistical reliability per run

The tasks are very narrow and shallow and not ecologically rich. These tasks are well studied in psychology for decades because they are simple and you can construct simple cognitive models of the behavior. However, this greatly limits the generalizability of those bespoke models fit to these bespoke tasks, as we see in the results here on the out of generalization test. Since we have AI models that can do incredibly rich tasks now, I would prefer human benchmarks gather rich human behavior, such as conversations or user logs, or gameplay in some high-dimensional video game. It is unclear what fitting LLM simulators to these tasks gives us for more generalizable user modeling across domains.

Another issue is that the interaction setup between humans and agents is not really apples to apples. Humans are using a mouse and keyboard live in the browser, while the models get static screenshots and spit out JSON actions through a Playwright script. Yet a bunch of the process features rely on reaction timing and motor dynamics like cursor smoothness, hover behavior, or post-error slowing. For an API model acting through a browser harness, those features are mostly just measuring network latency and script execution quirks rather than any actual cognitive process, which probably inflates how well the classifier can tell them apart. On top of that, the off-the-shelf frontier models are only prompted to get a high score on the task, never actually told to act like a human (and in tasks like delay discounting, the model is explicitly told to reason about the tradeoff while humans are just told to pick whatever they prefer). Before jumping straight to weight fine-tuning on open models, they really needed to test a LLM agent harness designed to implement cognitive modules (ie like Concordia or CoALA) or an in-context learning baseline where frontier models are actually asked to mimic human behavior or given a few human traces.

Finally, the process fine-tuning and red-teaming evaluation in the second half have some weird methodological holes. Their process loss just pushes every single model rollout toward the average human summary statistic, completely ignoring variance across people. A model can basically game their distance metric just by collapsing its behavior to the population mean on every run, which probably explains the weird inverse scaling in the results where the smallest model matches the human feature averages way better than the largest model, even though the largest model fools the classifier more often.

Questions for authors

Can you clarify how many trials were actually run in Section 3 for IGT, WCST, and Information Sampling? If IGT and WCST were run for only 10 trials (as stated on line 154 and line 315), how many rule shifts occurred in WCST, and what is the test-retest reliability (or split-half reliability) of the human process features over just 10 trials?

How were features like post_error_slowing, cursor_smoothness, pre_move_hovers, and tap_error_mean computed for JSON-outputting VLMs in Section 2? If you remove all timing- and trajectory-based features that are constrained by the Playwright JSON interface and keep only discrete choice-sequence features, what is the resulting classifier AUC on the output-matched tasks?

Why does P-SFT (1.5B) achieve near-zero distance in Table 3 and Table 5 while P-SFT (70B) has much larger distances, yet P-SFT (70B) fools the Random Forest classifier at a much higher rate (90.5% vs. 74.0% in Table 4)? Does the 1.5B model suffer from variance collapse around μ^(human)?

5 comments

We thank the reviewer for their comments, and address each below:

1.Psychometric validity of process features.

Our aim was not to optimize traditional task measures, but to evaluate process-based human–agent discrimination within a practical interaction window across 30 tasks.

We report Spearman–Brown corrected odd/even split-half reliability with 95% CIs below. Reliability varies, with stronger estimates for mean sampling, stickiness, and win/stay strategies. We explicitly tested the dependence of our conclusions on features with weaker split-half reliability by excluding them from the classifier analysis: human-agent discrimination remains strong (CV AUC = 0.85), and P-SFT retains a higher average rate fool rate than to A-SFT (63.8% vs 48.9%). Our central conclusions are not impacted by the features with lower reliability.

FeatureReliability [95% CI]
WCST perseveration cost0.28 [0.15, 0.51]
WCST learning slope0.47 [0.20, 0.65]
IGT learning slope0.30 [−0.05, 0.54]
IGT stickiness0.65 [0.46, 0.77]
IGT deck entropy0.42 [0.17, 0.63]
IGT win-stay0.65 [0.43, 0.78]
IGT lose-shift0.49 [0.25, 0.78]
IGT good deck rate0.30 [0.19, 0.38]
Sampling mean samples0.85 [0.74, 0.92]
Sampling variance of samples0.52 [0.28, 0.69]

2.Limited ecological richness of the task battery

To introduce and evaluate the process versus output distinction and the fine tuning approach, we believe it’s important to start off with scientifically validated paradigms and features. Starting with user logs or open-ended gameplay would require additional choices about how to define and validate the relevant processes, and the design choices would introduce uncertainty into result interpretation.

3.Potential interface confounds and missing human-mimicry prompting baselines

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 ran an experiment prompting frontier models to mimic humans, with participants’ first three choices provided. This pushed the frontier models closer to humans, but P-SFT still maintained closer distance.

ModelDistanceFool rate (%)
Claude1.650
GPT1.367.6
Gemini1.070
Base Qwen0.866.8
Claude mimic + 3 examples0.7612
Gemini mimic + 3 examples0.6518
Centaur0.4444
GPT mimic + 3 examples0.4246
Llama 70B P-SFT0.4090.5
Qwen 32B P-SFT0.2345
Qwen 14B P-SFT0.2352.5
Qwen 7B P-SFT0.1768
Qwen 1.5B P-SFT0.0674

4. Collapsing behavior to population mean, and distance/classifier and fool rate inconsistency

We tested this empirically: for each trained feature, we divided the variance across a model's runs by the variance across human participants (a ~1 ratio means runs vary as much as people do, ~0 implies the collapse). Since P-SFT and A-SFT differ only in the process term, comparing them isolates this effect. Across all features, the median ratio was 1.45 for A-SFT and 0.71 for P-SFT at 1.5B (0.76 vs. 0.68 at 70B). Therefore, process-feature matching did not result in collapse (the CE term in Eq. 1 anchors the policy to the distribution of human action choices).

Distance and fool rate need not rank models identically: distance measure averages over all trained features equally, while the classifier uses them unequally. In the Sampling task, P-SFT 1.5B matches the human average closely and also reproduces the human participants who draw many samples - a pattern the classifier tends to associate with agents. P-SFT 70B draws fewer samples than humans do (|d| = 1.02), which places it outside the range the classifier learned to flag. Swapping only this feature between the two models reverses their ordering (1.5B rises from 74.0% to 93.5%; 70B falls from 90.5% to 70.0%).

Questions

Q1.

  • 10 trials each, the finetuning used the same trial counts as the battery
  • 2 WCST rule shifts after the first rule
  • Reliability: please refer to response #1

Q2.

  • post_error_slowing: difference in log response time after error vs. correct trials
  • cursor_smoothness: summed absolute heading changes per pixel of path length
  • pre_move_hovers: number of explored states before a choice
  • tap_error_mean: the mean absolute deviation of produced inter-tap intervals from the target rhythm

As shown our response to point #3, the main conclusions persist after removing these features.

Q3. See the response to point #4.

AuthorsOpenReview ↗

A polite ask for reviewer's feedback on our rebuttal

Dear Reviewer LCcY,

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

Dear Reviewer LCcy,

We would appreciate your feedback on whether our responses and additional analyses address your concerns. Please let us know if any points need further clarification.

Best regards, The authors

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

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