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Under review as a conference paper at ICLR 2027

Neurodata Without Boredom: Benchmarking Agentic AI for Data Reuse

Abstract

Neuroscience data are highly fragmented across labs, experimental paradigms, and storage formats, and reuse often requires substantial manual effort to decipher each dataset's bespoke formatting choices and documentation. Agentic AI is a natural candidate to reduce this burden: LLMs read code and text quickly and with apparent attention to the low-level details humans tend to skim over. To measure how well agentic AI can perform data reuse, we select eight recent papers on large-scale mouse neural population recordings, covering diverse recording modalities and experimental paradigms. We provide coding agents with the data, code, and paper, and prompt them to reformat the data for a common downstream task: training a decoder from neural activity to task and behavioral variables. This task is a demanding benchmark target, since many conversion decisions are under-specified and several choices are defensible, yet a subtle but scientifically significant error can invalidate the resulting dataset in ways aggregate metrics do not reveal. We therefore evaluate agents using both outcome-based metrics and a process-based rubric scored independently by two human evaluators against manual reference solutions. We find that agents perform well on most subtasks, but rarely string together a fully error-free solution. We characterize the types of mistakes agents make, and suggest data-sharing best practices for agent-assisted data reuse. We further find that agents-as-judges are unreliable at catching errors on their own, but can automate process-based evaluation when given reference solutions. We show that newer models and prompt engineering improve performance, but no configuration we test eliminates end-to-end errors. All reference solutions, decision records, agent trajectories, and ratings are released as benchmark assets.

Primary area:
applications to neuroscience & cognitive science
Keywords:
agentic AI, coding agents, data conversion, benchmark, neural data, neural decoding, data standardization, LLM-as-a-judge

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_G6svOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper introduces a benchmark for evaluating coding agents on neuroscience data reuse. It includes eight datasets from published studies of large-scale neural population recordings in behaving mice, spanning different recording modalities, experimental paradigms, and storage formats. Agents receive the data, published code, paper, and structured instructions, and must convert the datasets into a common format for downstream neural decoding. The evaluation combines automated checks of dataset properties and decoder performance with a process-based rubric. Two human evaluators independently rate 1,236 decisions each across the initial agent runs. The paper identifies scientifically consequential errors that executable code and aggregate decoding metrics can miss. It also evaluates reference-assisted and reference-free agent judges, and uses the former to compare newer models, prompts, and harnesses. The study provides useful evidence about current agent limitations, but important questions remain about the interpretation of benchmark failures and the reliability of automated comparisons.

Critical strengths
  1. The benchmark targets a meaningful scientific bottleneck and evaluates semantic correctness beyond executability. Understanding heterogeneous datasets requires interpreting variable meanings, filtering rules, and temporal alignment. The examples show why successfully running conversion code or achieving good decoder accuracy does not establish faithful data reuse. This is a useful contribution to evaluating scientific agents.
  2. The initial evaluation involves substantial manual inspection and transparent reporting. Two evaluators independently assess the decisions with agent identities hidden, and each dataset–agent pair is run three times. The rubric permits justified alternatives and solutions that improve on the reference. Detailed failure cases, agreement measurements, and the reported release of reference solutions and trajectories make the study more informative than an evaluation based only on aggregate success rates.
Critical weaknesses
  1. The benchmark does not sufficiently separate scientifically incorrect conversions from reference disagreement and potentially concerning choices. Section 4.1 acknowledges that outcome checks can reject valid alternatives, including unspecified units. Table S1 also reports failures arising from different missing-data handling decisions rather than technical violations of the specification. The process rubric partly addresses this, but Appendix H defines “concerning” as not strictly wrong, while Section 4.4 groups it with “incorrect” for error detection. Consequently, the reported failure measures combine demonstrated mistakes with choices requiring further inspection. This matters especially for end-to-end assessment, where one disputed decision can determine whether an otherwise acceptable conversion passes. The paper needs a clearer, adjudicated distinction between scientific invalidity, justified alternatives, and unresolved concerns.
  2. The automated evaluator is insufficiently validated for the subsequent model and prompt comparisons. Reference assistance improves judging, but Table 2 reports supervised-judge precision of only 0.342 and 0.292, and the combined judge reaches 0.359. Figure S3 shows a per-trial score correlation of only 0.47 with the first human evaluator. These results establish partial usefulness, but do not establish that automated scores reliably preserve comparisons between configurations. Figure 4 relies on these judges, without a corresponding human validation of the newer configurations. Moreover, the outcome-based evidence does not consistently corroborate the process-score trends: under the revised prompt, GPT-5.6 increases the process score from 0.85 to 0.88 relative to GPT-5.4, while its outcome score decreases from 0.76 to 0.68 in Figure S7. The latter difference is not statistically significant, but its opposite direction warrants a more qualified interpretation.
Questions for authors
  1. Evaluation clarification: How do end-to-end success rates change when only adjudicated “incorrect” decisions count as scientific failures, while “concerning” decisions are reported separately? How were disagreements about scientifically acceptable alternatives resolved?
  2. Evaluator validation: Do you have a blinded human audit of the newer-model and revised-prompt outputs that tests whether the automated judges preserve configuration rankings and estimated improvements? Are judging errors systematic across datasets or agent families?
  3. Result interpretation: How do you explain the opposite process-score and outcome-score trends for GPT-5.4 versus GPT-5.6 under the revised prompt? Which evidence supports interpreting the higher process score as improved scientific conversion quality?
3 comments
AuthorsOpenReview ↗

Rating scale

We thank the reviewer for their careful reading of our paper and supplementary materials. Their questions pointed to specific places where our analysis could be clearer, and to a few additional analyses. Addressing them has strengthened the paper.

Weakness 1 and Question 1

We would like to clarify our rating scale. The rubric already separates the three cases the reviewer describes. A justified alternative that differs from the reference is rated ok, or better if it improves on it. Both count as correct throughout the paper, including in the end-to-end assessment.

We group concerning with incorrect deliberately. Together they define decisions that fall below the scientific standard expected of a data-reuse pipeline. A concerning decision is not technically wrong, in the sense that the code runs and the output satisfies the specification, but it is a choice that would not be accepted in actual data conversion code.

For example, two Codex trials on Zhong2025 filtered neurons by stimulus or reward selectivity (d′) before exporting the dataset (Appendix B, Example 1). Nothing in the task forbids this, and each filter has a plausible rationale. However, a dataset prepared for general decoding analyses that has already been filtered for decodable neurons would bias every downstream analysis toward high decoding performance. No experienced researcher would accept it as a faithful conversion. Similarly, one Codex trial on Chen2024 used raw DeepLabCut tongue positions without handling occluded frames (Example 4). The output is well-formed, but it mixes tracking noise into the decoded variable.

We agree that Appendix H’s wording (“not strictly wrong”) understates this, and we will revise the definition to make the standard explicit. That said, we agree it is informative to report the two categories separately. The end-to-end row of Figure 2 already distinguishes trials containing at least one incorrect decision (x) from trials whose only issues are concerning (!). Counting only incorrect decisions as failures, 23 of 48 trials pass end-to-end, compared with 6 when concerning decisions are included. We will report both numbers in the revision.

Lastly, we would like to note that each evaluator independently judged whether the agent’s solution was a justified alternative (ok) or fell below the standard (concerning or incorrect). The ratings were not adjudicated after the fact. Instead, we report agreement between the two evaluators (Figure S1), who agree on 90% of decisions at the binary level, indicating that the boundary between acceptable and below-standard decisions is reproducible across two independent sets of human evaluators.

AuthorsOpenReview ↗

Evaluation validation

Weakness 2 and Question 2

We do agree with the reviewer that human validation is needed to confirm the Figure 4 trends. We are therefore running a blinded human evaluation of the Claude Code configuration with Opus 5 and the revised prompt. Because each configuration involves rating several hundred individual decisions against the manual solutions, this evaluation requires additional time and will not be complete within the discussion period. We will report the results in the revision.

With that said, our goal in Section 4.5 was to build a reasonable automated pipeline that would make it practical to evaluate new models, prompts, and harnesses without a full round of human rating each time. We see the limits of this pipeline as part of our contribution. Our results show that agent-as-judge evaluation must be used with caution in this setting. The unsupervised judges are close to chance, and even the supervised judges have low precision (Table 2). Our human ratings of 1,236 decisions from two independent evaluators can therefore serve as a benchmark asset for developing and validating more reliable agent judges.

At the same time, we believe the supervised judge is a reasonable basis for an overall score, even if individual ratings are noisy. At the level of per-trial scores, the combined supervised judge correlates with the first human evaluator at r = 0.47, compared with r = 0.63 between the two human evaluators (Figure S3). The comparisons in Figure 4 are further averaged over 24 trials per configuration, which reduces the impact of noise in individual judgments. We used this pipeline for these reasons. We agree, however, that this does not rule out systematic judge biases that could affect particular comparisons. In the revision, we will state explicitly that the Section 4.5 results are estimates from the supervised judges and qualify our conclusions accordingly. We will also highlight improving this pipeline as an important direction for future work. That includes making agent judges more reliable, so that a full human evaluation is not needed each time a new model is released.

Regarding systematic judging errors, for agent families, Table S5 in the paper breaks down judge performance by which agent’s trials are being scored, including cross agent family judging. We find no evidence that either judge favors its own model family. Each judge’s false-positive rate is nearly identical on Claude Code and Codex trials (Claude judge 0.20 vs. 0.20; Codex judge 0.32 vs. 0.30), and the difference in precision in Table S5 is largely explained by the higher error rate in Claude Code trials (15.2% vs. 10.5% of decisions).

Across datasets, we also did not find statistically significant differences. The judges’ precision does not differ reliably across datasets. We did confirm that both judges are consistently harsher than the human evaluators on subtasks where several approaches can be defensible. For trial filtering, the proportion of decisions rated at least ok was 0.85 for Evaluator #1, but only 0.50 and 0.29 for the Claude and Codex judges, which rated it lower in 6 and 7 of the 8 datasets, respectively. For variable processing, the proportions were 0.78 for Evaluator #1, compared with 0.57 and 0.47 for the judges, which were lower in 7 and 8 of the 8 datasets. Lastly, we found that all raters (human and agent) agree that Hasnain2024 is the most difficult dataset.

AuthorsOpenReview ↗

More detailed analysis of the evaluation metric

Question 3

We thank the reviewer for this careful observation. We looked into the discrepancy between the outcome-based and process-based score in this case. On closer inspection, we found that this does not reflect a general disagreement between the two evaluations. The drop in outcome score is driven by two datasets, Hasnain2024 and Zhang2025, and in each case by a single choice about which data to include (i.e., data filtering choice). Excluding these two datasets, both scores increase (outcome 0.711 → 0.730, process 0.888 → 0.901)

Hasnain2024 (outcome 0.79 → 0.33, process 0.75 → 0.74): All three GPT-5.6 trials kept only 12 of the 44 reference sessions, namely the two-context sessions. The agent’s notes stated that it did this deliberately, since the context variable was only meaningful in those sessions. This single decision caused nearly every outcome metric to fail. The numbers of sessions, trials, subjects, and neurons all fell to 23–50% of the reference, and with less data, decoder accuracy also dropped below the threshold for several variables. The process-based judges did catch this error, rating both the data-loading and session-split subtasks as incorrect in all three trials. Because these were only 2 of 29 rubric questions, this did not have a big effect on the process score.

Zhang2025 (outcome 1.00 → 0.74, process 0.74 → 0.91): Two of the three GPT-5.6 trials kept every Kilosort cluster without quality filtering, resulting in 8.3 times the reference number of neurons. This caused the neuron-count statistic to fail and lowered the accuracy of two decoders by about 10%.

More broadly, this example highlights that the two evaluations measure different aspects of a solution. Outcome-based metrics are highly sensitive to upstream choices about which data to include. A single decision at the data loading stage propagates to nearly every dataset statistic and decoder metric, so it can dominate the outcome score. The process-based rubric instead localizes such an error to the one or two subtasks where it occurs, while also crediting improvements in the many downstream decisions for the newer agents that outcome metrics do not directly measure. Neither score alone fully captures solution quality, which is why we report both. We will add this analysis to the revision.

Reviewer_eXeFOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper introduces a neuroscience specific task where an agent is asked to write code to process data from multiple papers on mouse neural recordings into one downstream format. The paper uses human evaluators for rubric-based scoring and find that prompt engineering and frontier models improve performance. The paper finds that agents mainly struggle with making processing decisions or scientific interpretations.

Critical strengths

The benchmark creates a new, interesting task in the field of neuroscience, which data is scarce and fragmented. In this regard, the paper expands the domain of impact that scientific agents can have.

The paper makes a good faith effort in analyzing the failure modes and analyzing variability. The experiments are done across models, prompts, and agent harnesses, contributing to the soundness of the results. The use of human evaluators is well motivated by showing that LLM-as-judge underperforms humans.

Critical weaknesses

The task is quite narrow in scope. The main concern is that the findings will not generalize and the sample size is too small to compare methods. Similarly, the task requires human evaluation, which introduces subjectivity and makes it hard to scale. Although this is an interesting task, it doesn't meet the paper's claim that this is a benchmark for scientific data reuse.

Since the papers come from public repositories, there are concerns with data contamination. The paper would benefit from making sure that the reference solutions are not contaminated in the models that were tested.

I didn't find the failure analysis too insightful. It doesn't seem surprising that the agents struggle with mistakes in scientific interpretation or processing decisions. It is mentioned in the paper that the tasks are open-ended and under-scoped. The main selling point of the paper was that it requires deep domain knowledge from the human evaluators, but many of the failure modes (e.g. TIME_RES, PROCESS, VARNAME) doesn't seem to require domain knowledge to pick out. Furthermore, as a result, the practical guidelines for data sharing mentioned in the paper are already pretty obvious ones.

Questions for authors

How does the minimum vs maximum vs new prompt compare? I think only one is given in the appendix.

How are ASSUME and VARNAME counted in the error taxonomy since one is a subset of the other?

How do the 8 papers compare with each other? In particular, some papers seem to have less errors. Why is this the case?

3 comments
AuthorsOpenReview ↗

On the scope of the benchmark

We thank the reviewer for their time and for recognizing the benchmark's novelty and the care taken in analyzing failure modes and variability. Several of the reviewer's concerns are addressed in the current manuscript, and we point to the specific sections below. We will make these points more prominent in the revision.

Data contamination. Data contamination from the original published work is not an issue for this task. We provide the agent with the data, published code, and paper in its Docker container. The task is not to reproduce the analysis of the original paper, but to reformat it for a new task. This mirrors the task computational neuroscientists need to do, which is use resources including the published code to understand a dataset they download. In our paper “reference solutions” refer to solutions we manually wrote when preparing the benchmark and “reference code” to refer to the original paper’s published code. We apologize for this confusing naming, and will rename these to “published code” and “manual solution”. In addition, each manual solution contains a unique canary string, and our verifier scans all agent outputs for it; no trial contained a canary.

Task narrowness. Our goal with this work was to intentionally choose a narrow task so that computational neuroscientists could assess whether this particular real problem -- reformatting neural activity and behavior data for reuse -- is solved well enough that they can trust automated results, as well as determine whether we should redirect efforts from data-format standardization (e.g. NWB format) toward more pressing problems now that agentic AI can partly solve the problem. Our choice of many instances of the same task was in contrast to many science benchmarks which instead try to broadly cover many fields in science to compare different AI models. The goal here is a benchmark for computational neuroscientists rather than for AI researchers, and we submitted to the ICLR neuroscience track accordingly. We agree that data reuse is more general than this particular neuroscience problem, and will reformulate the text to make it clear that extrapolation of our results to the more general data reuse problem is a hypothesis. Regarding sample size, eight datasets is in line with expert-curated agentic science benchmarks such as BLADE (12 datasets), and with this number we already observe several significant effects with relatively small changes (paired permutation tests, Figure 4).

On evaluation and scalability. Many recent works have noted the difficulty of automatically evaluating real science tasks [BLADE, DiscoveryBench, ScienceAgentBench, NeuroD2DEval, PaperBench]. We show that this is the case for our relatively well-defined task and expect it to be even harder for more open-ended tasks like hypothesis discovery [AutoDiscoveryBench]. This open-endedness is a factor that differentiates many science tasks from coding [SWEBench] or MLE tasks [MLEBench]. In science tasks, there are many possible valid solutions that can lead to different outcomes [BLADE, Botvinik-Nezer et al., 2020]. We therefore score the process (the decisions the agent made) in addition to the outcome. Our analysis shows the need for new evaluation methods for open-ended science tasks, and we provide evidence that automated supervised LLM-as-a-judge is a useful, scalable metric.

AuthorsOpenReview ↗

On the evaluation methods and domain knowledge

In this work, we compare four different evaluation methods based on: outcome, two human-expert scores, unsupervised LLM-as-a-judge, and LLM-as-a-judge supervised with a manual solution. The two human evaluators agreed on whether a decision was an error 90% of the time (d′ = 1.84; Section 4.2, Table 2), which we use as the reference level for the automated methods. We summarize comparisons between these metrics and the human-expert judgments:

  • Outcome-based. We compare each solution to the manual solution on dataset statistics (e.g., numbers of trials and neurons) and decoder accuracy (Table 1, Section 4.1, Appendix G), as in ScienceAgentBench and TerminalBenchScience. This approach can miss subtle errors. In Allen2P, for example, an overly coarse time binning removed neural dynamics yet raised decoder accuracy (Section 4.1, Table S3). As a result, the outcome-based evaluation can be less sensitive than the supervised judge (Figure S7 vs. Figure 4). To highlight this, we conducted additional analysis and found that 1) the outcome-based evaluation gave 11 trials a perfect score, but only 2 of those 11 also received a perfect score in the process-based evaluation; 2) the two scores are only weakly correlated (r = 0.3), suggesting that they capture different aspects of solution quality.

  • Unsupervised LLM-as-a-judge. We tested the standard LLM-as-a-judge framework for evaluation. Here, we give the judge agent the agent’s solution, a scoring rubric, and the dataset's paper and published code. In Section 4.4 (Table 2) we show that this has low agreement with human evaluation (d’ = 0.83, 0.93).

  • Supervised LLM-as-a-judge. We tested a supervised LLM-as-a-judge, in which we provide supervision in the form of a single manual solution and manual descriptions of the decisions made (Section 4.4; Appendix H). This produced scores that agreed more with human evaluation (d’ = 1.40, 1.58), approaching inter-human agreement (d’ = 1.84, Table 2). We thus argue that supervised LLM-as-a-judge is a useful automated evaluation metric. The comparisons of newer models, prompts, and harnesses were scored by supervised agent judges, where we show that they detected significant differences between them (Section 4.5, Figure 4).

On domain knowledge and task difficulty. The task is indeed under-specified, as real data reuse is: a scientist reusing a dataset must use their judgment to make reasonable choices where documentation is missing. The benchmark measures whether agents make educated guesses as an expert would. In Allen2P, the published code uses different time resolutions for different analyses, and six trials chose four different resolutions, up to 750 ms bins (Example 2). Domain knowledge includes knowing that for training a neural decoder, time bins of 750 ms discard much of the neural dynamics, and it is best to use the finest resolution that can reasonably be measured from the data. Evidence that this requires domain knowledge is the poor performance of the unsupervised LLM judges, which caught only 28–56% of the errors humans found even with the paper and published code (Table 2). A less obvious finding is that agents often bypassed the official APIs for standardized datasets and parsed the raw files directly, despite being instructed to read the released analysis code and having the APIs pre-installed (Section 4.2, Figure S2B). Requiring them to use the APIs did not improve performance (Figure S8). Our practical guidance is simple, but it differs from the current emphasis on data-format choice; our work shows that conforming to a task-specific data format does not remove such ambiguities.

AuthorsOpenReview ↗

Reply to questions

Q1. Minimal vs. maximal vs. new prompt. The minimal prompt specifies only the task and the output format, in enough detail for the result to be evaluated. The maximal prompt (reproduced in Appendix D) adds a structured workflow. It requires the agent to inspect the code, data, and methods text, document its findings in a worksheet, check for consistency across sources, and validate on a small sample before converting the full dataset. The new prompt is a revision of the maximal prompt that we wrote after observing the agents’ failure modes. We agree that the minimal and new prompts should be included, and we will add both to the appendix.

Q2. Errors are not double-counted. As described in Section 4.3, each trial × subtask pair rated incorrect or concerning was assigned to a single category. VARNAME is a special case of ASSUME, but we observed several notable errors caused specifically by ambiguous variable names, so we gave them their own category to make this failure mode visible. Instances counted as VARNAME are therefore not also counted as ASSUME.

Q3. Differences across the eight datasets. Our framework allows us to answer this question directly, which we see as one of its strengths. The process-based rubric localizes each error to a specific subtask and category, so we can attribute differences in dataset difficulty to particular processing steps rather than only observing that some datasets score lower. Datasets requiring fewer intermediate processing steps and with unambiguous variable names produced the fewest mistakes. Lee2025 and Majnik2025 each have a single decoder output variable and scored highest (Figure 2). Hasnain2024, by contrast, requires deriving six output variables from a raw MATLAB struct, including tongue and paw velocity from tracking data and lick direction from a misleadingly named field. It scored lowest, and most of its errors fall into PROCESS (Figure 3A). This suggests that what makes a dataset hard for agents to reuse is the amount of processing and the clarity of its semantics, not its file format. Outcome-based metrics alone could not reveal this. We will highlight this point in the revision.

Reviewer_H5woOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper benchmarks scientific data reuse using eight neuroscience datasets. Coding agents convert heterogeneous recordings into a shared format for neural decoding. Outcome checks are complemented by two human evaluators independently rating 1,236 decisions each. The study also evaluates reference-assisted judges and the effects of models, prompts, and harnesses.

Critical strengths
  1. The benchmark targets an important gap between executable code and scientifically valid data processing. Detailed reference solutions, decision records, and blinded human ratings expose errors that aggregate statistics and decoder accuracy can miss.

  2. The comparison between human and automated evaluation is informative. It quantifies both the benefits of reference access and the judges’ remaining false alarms, providing useful evidence about the limits of automated scientific evaluation.

Critical weaknesses
  1. The model and prompt comparisons in Section 4.5 rely on automated judges whose error-detection precision is only 0.292–0.342 against the first human evaluator (Table 2). Human validation is reported for the original configurations, leaving the reliability of the later performance differences uncertain.

  2. The revised prompt was developed after observing failures on the same eight datasets used for evaluation. Its gains therefore establish adaptation to this benchmark, but do not yet establish that the prompting improvements transfer to unseen datasets.

Questions for authors
  1. Do the model and prompt improvements in Figure 4 persist under blinded human evaluation of a representative sample from the newer configurations?
1 comment

We thank the reviewer for their positive assessment and focused questions. Their point about validating the newer configurations directly led to the human evaluation we are now running, which will strengthen the paper.

Weakness 1 and Question 1:

We agree that the comparisons in Section 4.5 rely on supervised agent judges, and the conclusion based on the agent judge is less certain than the human-rated results. Our goal in Section 4.5 was to build a reasonable automated pipeline that makes it practical to evaluate new models, prompts, and harnesses without a full round of human rating each time.

That said, we believe the supervised judge provides a useful overall score, even if individual ratings are noisy. At the level of per-trial scores, the combined supervised judge correlates with the human evaluator at r = 0.47, compared with r = 0.63 between the two human evaluators (Figure S3). The comparisons in Figure 4 are further averaged over 24 trials per configuration, which reduces the impact of noise in individual judgments. Averaging does not rule out systematic judge biases, so we do agree with the reviewer that human validation is needed to confirm the Figure 4 trends. We are therefore running a blinded human evaluation of the Claude Code configuration with Opus 5 and the revised prompt. Because each configuration involves rating several hundred individual decisions against the manual solutions, this evaluation requires additional time and will not be complete within the discussion period. We will report the results in the revision.

Lastly, we would like to emphasize that manual evaluation takes substantial time, and repeating it for every new model and prompt is not feasible. We therefore see developing a more reliable automated process judge as the key next step. Our human ratings of 1,236 decisions from two independent evaluators provide both a baseline and a benchmark for developing and validating better agentic judges.

Weakness 2:

We agree. Our intention with the revised prompt was to see how much performance on these eight datasets could be improved with a single prompt targeted at the failure modes we observed. We fully acknowledge that these gains may not generalize to unseen datasets, and we will state this explicitly in the revision. Testing whether such prompt improvements transfer to new datasets is an important direction for future work.

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

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