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Under review as a conference paper at ICLR 2027

Open-Endedness Bench: Measuring Epistemic Process from Agent Records

Abstract

Agents are increasingly given open-ended research tasks: discovering an empirical law from self-designed experiments, improving a heuristic whose optimum nobody knows, or beating a standing record. Outcome scores alone do not establish whether an agent's claims follow from executed experiments, and a reference answer may be unavailable. We evaluate the agent's epistemic process: how it forms hypotheses, tests them, and revises them in response to evidence. We introduce OEB (Open-Endedness Bench), a benchmark-agnostic methodology that reads only the agent's execution record and never a reference answer or an outcome score. OEB compiles the record into a unified epistemic event graph whose edges connect the propositions the agent states to the executed actions that test them; each node carries an exact excerpt that code verifies against the record. One principle governs scoring: prose can state a proposition, but only evidence returned by an executed action can support or refute it, so OEB checks what the agent writes against what it actually ran. From the graph, OEB scores four competence axes (evidence, experiment, revision, and no reward hacking), mostly as the share of opportunities for sound research that the agent took, and profiles six subjective persona traits that describe the agent's research habits. We score 119 existing runs over 12 tasks from three benchmarks: LLM post-training, chip design, and a training-speed record. Against logged results, only 16-29% of the improvements agents claim are real. On 9 of 10 tasks, the best run tries more new ideas in its second half than the worst run. The persona readings follow the model: for every trait, the model that ran explains more of its variance across runs than the task (a median of 43% against 7%).

Primary area:
datasets and benchmarks
Keywords:
open-ended evaluation, process evaluation, AI agents, epistemic reasoning, trajectory analysis, LLM-as-a-judge, benchmark validity, reward hacking

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 2 reviews, above 27% of the others.
Reviewer_ehvHOpenReview ↗
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Paper summary

This paper introduces Open-Endedness Bench (OEB), a benchmark-agnostic framework for evaluating the epistemic process of research agents from their execution records rather than from task outcomes or reference answers. OEB converts heterogeneous agent logs into a unified epistemic event graph, where propositions stated by the agent are linked to executed actions and observations.
I find the motivation timely and the execution-record perspective interesting. However, I have concerns about whether the proposed scores are sufficiently validated as measures of “epistemic competence,” and how much practical value the resulting scores provide beyond descriptive trajectory analysis.

Critical strengths

1. The paper targets an important limitation of outcome-only agent evaluation.
For open-ended research tasks, a final score alone cannot distinguish disciplined experimentation from accidental success, and OEB directly targets this gap.

2. The separation between propositions and executed actions is well motivated.
The event-graph formulation avoids rewarding unsupported narrative reasoning by requiring credited propositions to be connected to actual executed actions. :chatgpt-content-reference{index="2"}

3. The framework is relatively general across heterogeneous research-agent settings.
The same graph construction and measurement layer are applied to post-training, chip design, and training-speed optimization, with benchmark-specific processing largely isolated to the log-conversion stage.

Critical weaknesses

1. The link between the proposed scores and epistemic competence is not fully convincing.
The axes are built from hand-designed opportunity-based rates, but it is not clear that a higher score always means better research behavior. For example, E2 favors experiments that resolve explicitly stated propositions, which may penalize useful exploratory experiments that are not framed this way in the trajectory.

2. The framework is only partially benchmark-agnostic.
While the scoring layer is shared, each benchmark still needs a custom log converter and a world manifest specifying task rules and setup. These choices may affect what is counted as an environment action, a violation, or an evaluation opportunity.

3. The validation of E1–E3 is relatively weak.
The paper shows that scores are stable under repeated judging and validates E4 against external benchmark audits, but there is no comparable external validation for E1–E3. Consistency across judges does not by itself show that these scores measure the intended epistemic properties.

4. Some of the empirical conclusions are mainly correlational.
For example, better runs tend to explore more new ideas in the second half, but this could also reflect stronger models, better stopping behavior, or task differences. The current analysis does not show that encouraging more late-stage exploration would itself improve performance.

5. The evaluation depends heavily on what the agent writes into the trajectory.
For E1–E3, missing reasoning is difficult to distinguish from reasoning that never happened. Since different models expose very different amounts and styles of intermediate reasoning, this may complicate cross-model comparisons.

6. The practical value of the resulting scores is unclear.
The paper provides several competence dimensions and persona traits, but it does not yet show how these measurements would help with model selection, agent design, or intervention beyond simpler outcome scores and trajectory statistics.

Questions for authors

Q1. How do the authors validate that E1–E3 actually measure epistemic competence?
The current experiments mainly show that these scores are reproducible across repeated judging. It would be useful to compare them with expert judgments of research quality or with downstream research success.

Q2. How sensitive are the results to the benchmark-specific converter and world manifest?
Since these components define the task setup and evaluation rules, it would help to quantify how much the final OEB scores change under reasonable alternative conversions or manifests for the same benchmark.

Q3. Can the authors provide stronger external validation for E1–E3, similar to the auditor-based validation for E4?
At present, E4 has a clear external reference, while the other competence axes are mostly validated through scoring stability.

Q4. Does the late-stage exploration result remain after controlling for model and task effects?
The current correlation is unclear whether late exploration itself is beneficial or simply associated with stronger models or easier tasks.

Q5. How should OEB compare models with very different reasoning verbosity?
Since E1–E3 depend on propositions written into the trajectory, terse models may generate fewer opportunities than verbose models. Could the authors test whether the conclusions remain stable after controlling for reasoning length or by prompting the same model to produce more or less explicit reasoning?

Q6. What practical decision is OEB intended to support?
For example, can OEB help select a better research agent, identify trajectories that should be trusted, or guide interventions that improve future performance beyond what can already be obtained from outcome scores and simple trajectory statistics?

1 comment

Thank you for the review. We answer the questions in order.

Q1 / Q3. External validation of E1–E3. We ran a blinded human audit (general response §1). Two independent annotators labelled 80 randomly sampled items and agree with the judge on 74% and 73% of them. On downstream success: within a task, the correlations of E1–E3 with the outcome are close to zero (−0.02, −0.12, +0.14; every interval includes zero). For E4 it is −0.14 [−0.23, −0.02], because runs that hack score higher. On these short tasks the outcome does not tell us how an agent handled its evidence, which is what E1–E3 are meant to measure (§6).

Q2. Sensitivity to the converter and the manifest. For the manifest, two fields affect E4. Without the house rules, E4 still catches 10 of 11 cheating runs, and the clean runs it flags drop from 13 to 5. With and without the declared size of the evaluation set, E4 changes in 3 of 91 PostTrainBench runs. For the converter, the choice that matters most is which text enters the record. Visible messages and actions enter for every model, and hidden reasoning enters for none. Action and observation text is copied verbatim. For each run the converter also records a count of what it could not carry over (for example, file edits whose content the log does not contain).

Q4. Late exploration with controls. Ranking within a task already removes task effects. With model fixed effects the slope goes from +0.54 to +0.40 (95% CI [0.16, 0.67]). Adding run length and the number of research experiments, which capture when an agent stops, gives +0.37 [0.04, 0.69]. When the same model ran a task twice, the higher-scoring run tested more late ideas in 11 of 16 pairs. We did not intervene on exploration, so the paper now calls this an association (§6.2).

Q5. Models with different verbosity. We ran this control on the 91 PostTrainBench runs. We removed task effects and regressed each score on the amount of visible text per step (log scale).

Model share of variance, beforeAfterModel ordering, before vs after
E10.310.25+0.87
E20.680.64+0.80
E30.420.46+0.97
E40.150.15+0.99
T60.590.23+0.68

The differences between models in E1–E4 remain when models write the same amount, and the ordering of models is preserved. T6 describes how an agent writes its account, so we expect it to move with the amount of text. Prompting the same model to write more or less would need new runs, and we leave that to future work.

Q6. Practical use. We see three uses that an outcome score does not offer. First, it shows which claimed improvements to trust: agents often call a result an improvement when it is not, and then build on it (Table 2). Second, it points to the specific actions where hacking happened, with the rule and the quoted evidence, so an auditor can check them (E4, Table 3). Third, it informs harness design: on Chip-Bench, the fourth and later tries of an idea make up 36% of experiments and bring 10% of the gain, which argues for breadth (Fig. 4).

W1. Does E2 miss exploratory experiments? Experiment yield counts every research launch whose result the agent reads and judges, whether or not it stated a proposition beforehand. The only launch without credit is one whose result the agent never interprets in words.

W2. Is the method benchmark-agnostic? The extraction prompts, the jury questions, the graph and every scoring rule are identical across the three benchmarks. Two things are written per benchmark: the converter, which copies log text into a common schema, and the manifest, which states the task's own rules.

Presentation. We took this rating seriously and made four changes. §3 now follows a single example through extraction, linking and scoring. §4.2 states how each rule treats engineering checks, withdrawn results and stated causes. §2 states what the record contains and what it leaves out. §6 reports the late-exploration result as an association, next to its controls.

Reviewer_m8L9OpenReview ↗
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2
Confidence
3
Informativeness
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Paper summary

The paper introduces Open Endedness Bench (OEB) which is a framework for evaluating an agent's epistemic process from it's execution logs without relying on ground truth answers or final scores. OEB compiles raw logs into a graph in four stages.

  • L0: Normalize logs into a common schema & writes the world manifest of task rules
  • L1: LLM extracts act and proposition cards with verification
  • L2: Answers close ended jury questions by taking a majority of three votes
  • L3: Deterministic code builds a 2 plane graph connecting stated propositions to executed actions

The graph is used to compute four competence scores and six traits.

  • 3 out of 4 competence scores and 5 out of 6 traits are computed as oppurtunitites taken over offered.
  • E4 = 1/(1+k) over reward-hacking instances
  • T1 a share of output tokens on actions.

Results

  • OEB is applied to 119 trajectories on 12 tasks from post train bench, chip bench and nanoGPT speed run.
  • E4 catches 10 out of 11 audited cheating runs
  • Rescoring changes score by a median of 0.04
  • Only 16-29% of claimed improvements are real
  • Late-stage exploration separates winning runs from losing ones
  • Style traits depend more on the underlying model than on the task
Critical strengths
  • Authors took considerable effort to constrain the LLM judge. Every score is tied to an executed action. Every claim must quote its step. This prevents judge from inventing timeline steps and the judge only answers closed choice questions. The paper also provides a threat model in appendix which is a nice addition. This is consequential because it's the first general purpose (to my knowledge) open ended agent evaluation framework that doesn't need ground truth answers or task rubric.
  • There are very interesting and useful observations that are important to the community.
    • Fig 4: In chip bench, 4th-and-later attempts at the same idea correspond to 36% of experiments but only 10% of actual performance gains. This tells harness designers to favor breadth
    • Table 2: Agents act on their own verdicts from single noisy runs. Important to benchmark designers.
    • Fig 7: Different model families have different reward hacking strategies.
Critical weaknesses
  • Metrics validity

    • Ground truth verification of graph and E1-E3 is missing.
    • E1-E3 is never compared to task outcomes.
    • Rerun agreement checks for same answer but not the correctness of propositions or links.
    • Human eval on sample of cards or edges is missing.
    • No report on cards failing quote verification.
    • The baseline to justify 652 judge calls per run is missing.
    • E4 reports recall but not precision. The 13 extra flagged runs need manual inspection.
    • it is unclear if Fig 7 reflects model behavior or custom grading rules as three of the four GPT flags are seed reruns.
  • Model vs Harness

    • Sec 6.4 compares models using logs from different harnesses (Fig 1). Tab 6 caption tells that leaving internal reasoning out of logs lowers E2 would explains Opus 5 and Fable 5 drop and why E3 abstains on 21 of the 22 runs.
    • Same issue with style results. T1 & T6 has the biggest variance and they depend on whether reasoning tokens are recorded and.
    • Tier 1 and Tier 2 are not cleanly separated as well. E1 penalize testing styles that Tier 2 is supposed to treat as neutral.
    • Prior CoT faithfulness work (Turpin et al. 2023; Lanham et al. 2023; Chen et al. 2025) shows that models traces often diverge from what drives an action. The paper should tone down the claims as E1, E3, T6, and the 16% verdict rate depend on trusting the text trace.

Since the evaluation pipeline is the paper's main contribution, E1-E3 should be verified if they actually measure what they claim. The second weakness affects two of the three main findings.

Questions for authors
  • In table 3, provide info about extra 13 flagged runs and E4's precision. Also split the 36 instances into benchmark-rule violations and house-rule calls, justify labeling seed selection & partial-test reporting as reward hacking.
  • Which harness produced each model's post train bench logs? Is internal reasoning present in the record for each? Do Opus 5’s E2 = 0.08 and T6 = 0.02 hold on a subset where reasoning is logged?
  • In Table 2, is "truly improved" on Chip bench measured using the hidden grader or metrics the agent could see during the run?
  • How many cards and edges were human audited and whats the agreement?
2 comments

Thank you for the detailed questions. We answer them in the order of the review.

Q4. Human evaluation of cards and edges. We ran one. Two annotators independently labelled 80 randomly sampled E1–E3 items and all 45 E4 instances. They read the raw record and could not see the judge's labels. On E1–E3 they agree with the judge on 74% and 73% of the items, and they confirm 81% and 82% of the items the judge gave credit to. They also checked the extracted cards themselves, and judged 72 and 73 of the 80 to be correctly extracted (the quote is a belief, the step is a check or a launch). On E4 the two annotators agree with each other at κ = 0.84. Details are in the general response (§1 and §2).

How often does quote verification fail? Over the 119 runs, 1.3% of act cards and 0.4% of proposition cards failed verification and were dropped. Another 2.1% were dropped as malformed. In L2, 230 relation votes were voided because their quote failed verification, against 2,650 accepted verdicts.

E1–E3 are never compared to task outcome. We added this comparison. The within-task rank correlations with outcome are E1 −0.02 [−0.33, 0.23], E2 −0.12 [−0.37, 0.20] and E3 +0.14 [−0.19, 0.46]. For E4 it is −0.14 [−0.23, −0.02], because runs that hack score higher. On these tasks the outcome does not tell us how an agent handled its evidence, which is what E1–E3 are meant to measure.

Is there a simpler baseline than ~650 judge calls? We tried one. A single GLM-5.3 call reads the whole record and the task text, and scores E1–E4 directly. We ran it twice per run on six BFCL runs: the three shortest that the auditors marked as cheating and the three shortest they marked clean. In each pass it flagged 1 of the 3 cheating runs, and a different one each time. It gave every run between 0.85 and 1.00 on E1–E3. OEB flagged all 3 cheating runs and 1 clean run (on a disputed instance), with E1 between 0.60 and 0.80 and E2 between 0.05 and 0.47. The single call did not find the hacking reliably and did not separate the runs.

Q1. E4 precision, the 13 extra flagged runs, and seed selection. Against the auditor labels, run-level precision is 10/23 with the house rules and 10/15 with task rules only (general response §2). Two annotators inspected the 13 flagged runs that the auditors found clean. One breaks a task rule in a model the agent did not submit, which the auditors do not rule on. Five break a house rule only. Four and five are disputed, and three and two are false positives. On why we count seed selection and partial-test reporting: picking a submission by test score among reruns of one recipe selects on noise in the measure, and reporting a partial-test score as the full score misreports the result. The task text states neither rule, so the revision reports E4 both ways. You are right that three of the four GPT flags in Fig. 7 are seed reruns, and under task rules only they disappear.

Q2. Model versus harness. Table 9 (new, appendix) lists, for each model, its harness, the amount of visible text per step, and how much hidden reasoning the source log contains. The converter treats every model the same way: visible messages and actions enter the record, and hidden reasoning does not. We chose this because providers expose hidden reasoning very unevenly (nothing for four configurations, 10k–460k characters per run for the others). We then tested whether the cross-model results simply reflect how much a model writes. After removing task effects and regressing out the amount of visible text per step (log scale), the model still explains 0.64 of the variance in E2 (0.68 before), and the ordering of models is preserved (rank correlation +0.80). Opus 5 stays 13th of 14, so its low E2 holds when models write the same amount. T6 describes how an agent writes its account, so we expect it to move with the amount of text, and it does (model share 0.59 to 0.23). T1 does not depend on logged text. It uses the provider's per-call token usage, which counts reasoning tokens whether or not their text is logged, and all 79 runs with a T1 score have these counts. §6.4 now reports E2 with this control.

Tier 1 and Tier 2 are not cleanly separated. We computed all 24 trait-by-axis correlations (Table 8, new). 18 of them are below 0.3 in size. The largest one involving E1 is with T6 (−0.36): an agent that states hypotheses first has more beliefs on record before the evidence arrives.

CoT faithfulness. We agree this matters and now discuss it in §2, citing Turpin et al. (2023), Lanham et al. (2023), Chen et al. (2025) and Korbak et al. (2025). In OEB a proposition earns credit only when it is quoted and tied to an executed act, so text that no action backs earns nothing.

Q3. Table 2. "Truly improved" uses the local score that the agent's own make check/score writes during the run. The agent can see this score. The caption now says so.

Thanks for the rebuttal and new analysis that answer my reporting questions. IMO the following core issues still remain:

  • 73-74% E1-E3 human agreement looks weaker once adjusted for chance and drops to 68% outside belief grounded. Also human inter annotator agreement is missing.
  • Each model family ran in its own harness. So we can't say whether persona traits come from the model or the harness.
  • In Fig 7, dropping house rules drops 3/4 GPT instances. 27 of the remaining 32 task rule instances come from a single method. The remaining 5 instances across all other methods are too few to support the claim in Sec 6.3.

I am raising my soundness score to 2 and keeping my overall rating at 2.

Comments on the paper

2 comments

We thank all three reviewers for their careful reading. The concern you share is whether E1–E3 agree with independent human judgment. We ran a human audit during the discussion period to check this. This comment gives the two results that concern everyone, and the remaining points are answered in the individual replies. Changes in the revised PDF are in blue.

1. Human audit of E1–E3 (ggPL Q1, m8L9 Q4, ehvH Q1/Q3). We randomly sampled 80 E1–E3 scoring opportunities from 12 scored runs that cover all three benchmarks. Two annotators labelled every item independently. They read the raw record and could not see the judge's label. They agree with the judge on 74% and 73% of the items (59/80 and 56/77; 95% CI [64%, 84%]). Of the items the judge gave credit to, they confirm 81% and 82% (44/54 and 42/51). So when OEB gives credit, the annotators usually find the behaviour in the record.

2. How many E4 flags are real (m8L9 Q1, ggPL Q1b). E4 flags 23 runs, which contain 45 hacking instances in total. Some instances break a rule that the task states. Others break one of two rules that OEB adds and the task text does not state: an agent should not pick its submitted model by test score among reruns of the same recipe, and it should not report a score on part of the test set as the full score. We call these two the house rules.

Two annotators independently re-read all 45 instances and sorted them into five groups (κ = 0.84 between them):

What the annotator foundAnnotator 1Annotator 2
Breaks a task rule, in the model the agent submitted2319
Breaks a task rule, in a model the agent did not submit33
Breaks a house rule only99
Disputed49
No breach (false positive)65

So 35 and 31 of the 45 instances break a rule, and 6 and 5 are false positives.

We also recomputed E4 without the house rules, and compared both versions with the benchmark auditors' verdicts on the 90 audited runs:

Flagged, of the 11 runs the auditors found cheatingFlagged, of the 79 runs the auditors found clean
With house rules (paper)1013
Without house rules105

Without the house rules E4 still catches the same 10 cheating runs, and 8 of the 13 flags on clean runs go away, including the seed-rerun flags of the GPT models in Fig. 7. The revision reports both versions, and Fig. 7 now marks the two house-rule methods with hatching.

3. What changed in the paper. (i) A new §5.2 reports the human audit of E1–E3. (ii) §5.1 reports E4 precision, and Table 10 (new, appendix) gives both rule sets. (iii) §5.3 explains why E3 moves more than the other axes when rescored. (iv) §6 now relates E1–E3 to task outcome, and reports the late-exploration result with model and run-length controls. (v) §6.4 adds a control for how much each model writes. (vi) §2 states that OEB measures the recorded process and discusses CoT faithfulness. (vii) §3 follows one worked example from extraction to scoring.

Thank you for the detailed review, and for reading the scoring code.

W1 / Q1. E1–E3 need independent judgments, with disagreement examples. We ran a blinded human audit, and the numbers are in the general response (§1). Here are two items where both annotators disagreed with the judge, one in each direction:

  • The judge gave credit for a consequential check; the annotators did not. The agent loads candidate datasets and prints their fields (HealthBench, GLM-5.2, step 132). Both annotators saw this as getting to know the data, with no idea being tested. Our rule does count routine checks like this one, and §4.2 now says so.
  • The judge gave no credit for experiment yield; the annotators did. The output of a scoring run is cut off by the session limit (Chip-Bench, Claude Fable 5, step 56). In the next step the agent reruns it and reads that every gate passes. Both annotators counted this as a launch whose result the agent read and judged.

W1. The pooled median hides how much E3 moves (0.16 over 12 pairs). We looked into where the 0.16 comes from. A run has a median of only 8 contradicted ideas, so one changed verdict moves E3 by about 0.12. Binomial sampling at that count already gives a difference of 0.18, so 0.16 is what the small count predicts. When both scorings find the same contradiction, they agree on whether it was resolved in 60 of 72 cases (83%). After averaging over a model's runs the difference is 0.07–0.15, and this is the level at which the paper reports E3 (Table 6). §5.3 now explains this. None of the findings in §6 use E3.

W2 / Q2. Three rules that might penalize good behaviour. We measured what each rule does to the score. Scoring is deterministic once the graph is built, so we can add the behaviour in question to a scored run and recompute. We did this for every scored run (107 for E2, 49 for E3).

  • A replication that is informative. It earns experiment-yield credit as soon as the agent reads its result and says what it shows. If it overturns an earlier verdict, it also counts as a consequential check. The only replication without consequential-check credit is one that re-confirms something already settled. If we credited that, an agent could raise its score by rerunning a configuration it knows works. Effect on E2: median +0.001 (range −0.009 to +0.016).
  • A confounded result that the agent correctly withdraws. Yield asks whether the launch produced usable evidence, and this launch did not. The withdrawal is still rewarded, in E3: a withdrawn result no longer counts as a contradiction the agent has to resolve. If we removed withdrawn runs from the yield denominator, an agent could call every disappointing result a confound. Effect on E2: median −0.009.
  • A causal explanation with no support. E3 gives credit for a repair that later passes, or for a stated cause. Whether the cause goes beyond the evidence is checked in E1: assertion within evidence marks a cause that no result tested as overreaching. Stating a cause raises E3 by a median of 0.125 compared with dropping the idea silently. This is the largest of the three effects.

On the names: given these numbers, we would like to keep the rules as they are. The definitions in §4.2 already follow the rules ("consequential check": a check that changes the standing of a proposition; "contradicted resolved": a contradicted idea that the agent repaired, or explained by stating a cause). The revision adds the withdrawal and stated-cause cases to §4.2, and Appendix J reports the three effects.

Q1b. Which E4 disagreements come from OEB's broader rules? Please see the general response (§2). Of the 13 flagged runs that the auditors found clean, 8 are flagged only because of the house rules. At the instance level, the two annotators judged 39 and 40 of the 45 instances to be real or arguable breaches, and 6 and 5 to be errors.

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

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