acceptodds
Under review as a conference paper at ICLR 2027

Controlling False Discoveries via Auditing Scientific Agents

Abstract

Scientific discovery agents generate and test hundreds of hypotheses per dataset, and the agent that explores also decides which findings to report. Its internal scores and per-hypothesis tests do not bound the fraction of false reports: in environments with known ground truth, 18-66% of agents' reported discoveries are false. We introduce audited discovery, which separates exploration from reporting. An unmodified agent explores one data split and registers its candidate findings, and an independent audit tests each candidate once on a sealed holdout and reports only those selected by a false discovery rate (FDR) procedure. Across five agent systems in synthetic and semi-synthetic (plasmode) environments, auditing the same candidate lists brings FDR below 1% for every agent, whereas fresh data or FDR correction alone leaves up to 51%. Reliability has a price. Four agents report 6-35% fewer true discoveries than in their own reports, while the fifth gains 63% from truths it had withheld. At a matched 5% FDR, auditing yields up to 26% more true discoveries than correcting exploration evidence, with the largest gains for agents that find the most truths. On real neuroscience data, blinded experts believed 57% of audited findings to be real, against 21% of findings that passed only an individual holdout test. Audited discovery lets agents scale their search while scientists fix the reported error rate in advance.

Primary area:
foundation or frontier models, including LLMs
Keywords:
AI for Science, Agentic Discovery

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_nzeCOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces an Audited Discovery framework that separates the exploration process of AI scientific agents from statistical reporting.

Critical strengths
  1. The paper accurately identifies a fundamental weakness of current AI scientists: their tendency to produce false discoveries when evaluating their own findings. Introducing independent statistical auditing is a particularly insightful and elegant solution.

  2. The authors conduct extensive experiments across synthetic and semi-synthetic (plasmode) settings, complemented by blinded expert evaluations using real-world neuroscience data. This thorough evaluation provides compelling evidence for the effectiveness of the proposed approach.

Critical weaknesses
  1. The current framework only supports statistical hypotheses expressed in predefined structured templates, such as correlations and group differences. This limits its ability to handle free-form scientific claims or more complex scientific concepts.

  2. The improved reliability comes at the cost of missing some genuine scientific discoveries. Most agents experience a 6–35% drop in recall after auditing, highlighting a trade-off between statistical rigor and discovery yield.

Questions for authors

How do the authors plan to extend the auditing framework to more complex, non-standardized scientific claims that lack well-defined statistical testing procedures?

7 comments
AuthorsOpenReview ↗

Response to Reviewer nzeC (1/3)

Thank you for your thoughtful and constructive review. Your comments helped us strengthen the paper. We are glad you found the audit "a particularly insightful and elegant solution" and the evaluation thorough and compelling. Below we answer both concerns with new results.


W1 & Q1. Support for free-form and more complex scientific claims

"The current framework only supports statistical hypotheses expressed in predefined structured templates ... How do the authors plan to extend the auditing framework to more complex, non-standardized scientific claims that lack well-defined statistical testing procedures?"

Our supported claim types go well beyond correlations and group differences. They include effects that differ between groups or depend on a third variable, nonlinear effects such as thresholds, associations after controlling for other variables, and trends and delayed effects over time. These types follow the standard two-variable and adjusted analyses in two widely used test-selection guides (UCLA Statistical Consulting Group, n.d.; Motulsky, 2017), extended to data that follow the same units over time. Claims can also be restricted to a subgroup defined by up to two conditions and adjusted for up to three covariates (App. A.2), so on a table with 50 columns the claim types can express about 101310^{13} distinct claims [new].

What each claim needs. The audit needs a valid test for each claim, one that gives false positives no more often than its nominal level (e.g., at most 5% of the time at level 0.05) when there is no relationship. A new test can therefore be added to the audit once it shows this property on simulated data with no true relationship. This check uses only simulated data, so it is done before the test ever touches the holdout. Tests for non-standard claim types and for free-form claims can then be added with the same FDR control.

Complex hypotheses in practice. Agents in our runs proposed hypotheses that combine several of these features at once, such as the three below.

  1. Association controlling for three other variables. Among participants told they have high blood pressure, serum osmolality and red blood cell count are positively associated when controlling for body mass index, blood urea nitrogen and systolic blood pressure.
  2. Association that differs between groups. Among galaxies with a median r-band signal-to-noise ratio above 18, the correlation between i-band Petrosian magnitude and extinction-corrected u-band magnitude is higher in elliptical galaxies than in other galaxies.
  3. Association that changes when other variables are controlled for. Among superconducting compounds with five or more elements, the correlation between the weighted range of atomic mass and the weighted mean first ionization energy is lower when controlling for weighted mean atomic mass, atomic radius and density.

References

  • UCLA Statistical Consulting Group (n.d.). Choosing the correct statistical test in SAS, Stata, SPSS and R. https://stats.oarc.ucla.edu/other/mult-pkg/whatstat/.
  • Motulsky, H. (2017). Intuitive Biostatistics: A Nonmathematical Guide to Statistical Thinking (4th ed.). Oxford University Press.
AuthorsOpenReview ↗

Response to Reviewer nzeC (2/3)

W1 & Q1 (continued)

Why each claim type has a fixed test. We agree that fixed claim types are a limitation. We chose them because FDR control holds only when every claim's test is valid, and agents do not reliably write valid tests. Our experiments show three ways in which agent-written tests fail.

  • Tests that overstate the evidence. We reran POPPER with its default settings and found that 80% of its false acceptances rested on a single agent-written test with a very small pp-value, although our fixed test found no significant effect on the same holdout [new].
  • Running multiple tests until one passes. POPPER's agent writes up to ten tests per candidate and continues until their combined evidence crosses a threshold. We found that 95% of its false acceptances came after two or more tests in the paper's run [new].
  • Ignoring dependence between rows. When rows are related, for example repeated measurements of the same person, a valid test should account for this dependence. We ran POPPER with Claude Sonnet 5 as its backbone on such data, and none of the 191 tests its agent wrote accounted for the dependence [new]. When we reran these tests on new draws of the data, they found an effect for false claims 12.4% of the time at a stated rate of 5%, while the audit reported none of these false claims.

When we changed only the test, holding Opus's candidates, the holdout and the e-BH reporting rule fixed, FDR fell from 13.7% with POPPER's tests to 0.4% with our fixed tests (App. E.4). We therefore assign each claim type one prespecified test, a standard permutation or resampling test (Chung & Romano, 2013; DiCiccio & Romano, 2017; Freedman & Lane, 1983; Winkler et al., 2014; Wu, 1986), and check its validity once for the whole type (App. A.5).

Claims without a well-defined test [new]. For a claim type without a well-defined testing procedure, the literature or an agent can propose candidate procedures. The audit accepts a candidate only if its false-positive rate stays at the nominal level on simulated data with no true effect. Finding a valid test therefore becomes a program search with a verifiable objective, and the audit completes this search before reading the holdout.

As a proof of concept, we ran the search for two claim types outside our set, an indirect effect (xx affects yy through zz) and bimodality (a variable has two modes), with 10 and 6 candidate procedures. The search rejected several procedures that look reasonable. For example, one permutation test for the indirect effect found an effect in up to 84% of datasets that had none. With the procedures that passed, the audit reported 85% of the true new claims as discoveries and almost none of the false ones, and FDR over all reported claims stayed at 0.5%. The audit can therefore take on new claim types without weakening its control.

Free-form claims. The same search would support free-form claims. The agent writes each claim together with the code that tests it, using only the exploration split. The audit runs this code on simulated data with no true effect and returns the false-positive rate to the agent, which revises the code until it passes. The audit then freezes the code and runs it once on the holdout, under the same FDR control as every other claim. We will describe this extension in the revised paper.


References

  • Chung, E. & Romano, J. P. (2013). Exact and asymptotically robust permutation tests. The Annals of Statistics, 41(2), 484–507.
  • DiCiccio, C. J. & Romano, J. P. (2017). Robust permutation tests for correlation and regression coefficients. Journal of the American Statistical Association, 112(519), 1211–1220.
  • Freedman, D. & Lane, D. (1983). A nonstochastic interpretation of reported significance levels. Journal of Business & Economic Statistics, 1(4), 292–298.
  • Winkler, A. M., Ridgway, G. R., Webster, M. A., Smith, S. M. & Nichols, T. E. (2014). Permutation inference for the general linear model. NeuroImage, 92, 381–397.
  • Wu, C. F. J. (1986). Jackknife, bootstrap and other resampling methods in regression analysis. The Annals of Statistics, 14(4), 1261–1295.
AuthorsOpenReview ↗

Response to Reviewer nzeC (3/3)

W2. Trade-off between reliability and recall of true discoveries

"The improved reliability comes at the cost of missing some genuine scientific discoveries. Most agents experience a 6–35% drop in recall after auditing ..."

We agree that the guarantee costs recall, and every procedure that controls false discoveries pays this cost. With a fixed amount of data, a weak true effect and no effect can produce the same evidence, so a procedure that admits fewer false claims may also miss more true ones. Genovese & Wasserman (2002) characterize this trade-off between false and missed discoveries, and Rabinovich et al. (2020) derive the best trade-off that any procedure can achieve in a Gaussian model. In return for the 6–35% loss in recall, the audit cuts the share of false claims from 18–66% in the agents' own reports to at most 1.3%.

At equal FDR, the audit finds the most true discoveries. At a 5% FDR matched in hindsight, the audit finds 84.8 true discoveries per run for Opus, against 69.0 for correction on exploration evidence and 31.3 for Opus's own ranking (Fig. 4a). No other agent's own ranking reaches 5% FDR at all. The recall loss therefore comes from the lower FDR that the audit delivers.

Different FDR procedures trade recall for FDR differently. A procedure that makes fewer assumptions about the tests is more cautious and finds fewer true discoveries. Bonferroni is the most cautious. BY and e-BH stay valid however the tests depend on each other. BH finds the most true discoveries but assumes the tests are independent or positively related. We compared these procedures on the same holdout evidence as a practical guide for users. For Claude Code (Opus):

ProcedureFDR (target 5%)# TrueFDR (target 10%) [new]# True
Agent's own report17.9%77.717.9%77.7
Bonferroni0.3%61.00.9%64.4
e-BH0.6%69.21.0%72.0
BY (our default)1.0%73.41.5%76.3
BH3.3%81.76.7%85.9

BH finds more true discoveries than Opus's own report (81.7 against 77.7 per run) at a fifth of its FDR (Table 15). The revised paper will include this comparison for every procedure and agent.

The missed claims are weak effects [new]. The recall the audit gives up comes mostly from weak effects, which a holdout of limited size cannot reliably confirm. Our semi-synthetic environments plant true relationships at three strengths, so we can measure which ones the audit misses.

Effect strengthStrongMediumWeak
Percentage recovered81%70%49%

The audit's power rises with the size of the holdout, from 75% of true claims at 500 rows to 93% at 2,000 on the health survey data.

With FDR controlled, agents can explore more. The audit controls FDR over every candidate an agent registers, however many there are, so the agent's own cutoff no longer limits what is reported. ShinkaEvolve, for example, reports only a third of the true candidates it finds, and auditing its full list raises its true discoveries by 63% (Sec. 5.3).

We also tested whether a larger exploration budget pays off under the audit [new]. With 1,000 candidates in place of 300 and twice the time, Claude Code (Opus) doubled its audited true discoveries on the superconductor data, which contain many true relationships, and the audit kept FDR at or below 1.0%. At the same FDR, the audit found 2.6 times as many true discoveries as Opus's own ranking. The gain depends on the agent, and Sonnet and ShinkaEvolve did not gain consistently from the larger budget. Whatever the budget, the audit kept FDR controlled, so agents can explore further without reporting more false claims.


We hope these answers address your questions. Overall, our paper systematically measures how often discovery agents report false claims, identifies why their own checks fall short, and introduces an audit that controls the false discovery rate of existing agents without changing how they explore. We would be happy to continue the discussion. If these answers resolve your concerns, we would be grateful if you would consider raising your score.


References

  • Genovese, C. & Wasserman, L. (2002). Operating characteristics and extensions of the false discovery rate procedure. Journal of the Royal Statistical Society: Series B (Statistical Methodology), 64(3), 499–517.
  • Rabinovich, M., Ramdas, A., Jordan, M. I. & Wainwright, M. J. (2020). Optimal rates and trade-offs in multiple testing. Statistica Sinica, 30(2), 741–762.
Reviewer_66ZyOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
3(+1)
Read review
Paper summary

The paper investigates mitigation of the problem in agentic science where agents can be used to generate a lot of plausible "discoveries", which just shifts the burden of review to humans. The proposed solution is that an agent generates hypotheses on a subset of data, which is later tested on a holdout set with an applied False Discovery Rate correction to determine which findings are to be reported. The authors find that the procedure reduces FDR to, on average, below 1%.

Main contributions are:

  1. Workflow to reduce FDR in agentic systems
  2. Evaluation of FDR across models and agent harnesses

The authors provided the code and results for verifying the claims during the review period. They have also expanded the evaluation across models and agent harnesses. This resolves the issues with the soundness of the paper.

Critical strengths

Main strength is the practical focus on improving agentic scientific discovery. The workflow is easy to implement and from the reported results, it seems to be a meaningful improvement on the baseline agent performance. The paper also performs evaluation of some popular agent harnesses and their baseline performance.

Critical weaknesses
  1. The central workflow is what I would consider as common-knowledge good science, something that should be obvious to anyone in the field. Although the authors acknowledge this, the novelty of the central workflow and the main idea of the paper, is to me very lacking. However, since from experience we see that practitioners in all sorts of different fields of science do not adhere to these very basic scientific principles, there is a potential contribution on the educational and implementation side.

Note: I find the paper lacking in novelty with its current framing - centered around the workflow. What would make it stronger for me is evaluating how much of these discovery rates (false or otherwise) are attributable to model and harness effects. So expanding the scope of that evaluation to different model families and harnesses. Rather than presenting the workflow as something novel - present it as: You're using Claude Code/GPT Models/Gemini Models, you will have on average, on these tasks, X false discoveries; here is our workflow to reduce this rate.

Update (15 November 2026): Following the authors' response, I consider my original concern regarding novelty and framing substantially addressed. The clarification of the model and harness evaluation, together with the proposed reframing of the contributions around measuring false discoveries rather than introducing a novel workflow, strengthens the paper in my opinion. I have therefore increased my rating.

Questions for authors
  1. Is it possible to adjust your workflow to limited data regimes? Or can you provide an assessment how the data budget impacts the viability of your workflow? I didn't see this in the limitations section. What is the minimum sample size that makes this workflow possible?

  2. Can you provide the implementation on https://anonymous.4open.science/ before the end of the review period?

8 comments
AuthorsOpenReview ↗

Response to Reviewer 66Zy (1/4)

Thank you for your thoughtful review and helpful suggestions. Your feedback helped us improve the paper. We are glad you valued its practical focus and found the audit "a meaningful improvement on the baseline agent performance". We release the implementation for anonymous review at tinyurl.com/audited-discovery, and we will open-source and maintain it as a toolkit that the community can adapt to ensure the statistical validity of scientific discovery agents. We also agree that the principle behind the audit is a cornerstone of good science. Yet discovery agents rarely apply it on their own, so they report many false claims and shift the burden of checking them to scientists, as your summary notes. To our knowledge, our paper is the first to examine this gap systematically and to give discovery agents a standard way to close it. We answer each concern below.


W2 & Q2. Code availability

Note: anonymous.4open.science was down when we prepared this response, so the code is hosted in an anonymous OSF project.

We provide our implementation at tinyurl.com/audited-discovery for anonymous review and will release it publicly upon publication as a toolkit for false discovery control in AI-driven scientific discovery. The implementation covers the entire workflow of the paper.

  • Data with known ground truth. The toolkit generates simulated datasets, and semi-synthetic datasets that preserve real data from four domains and add relationships of known effect size. Users set the sample size, the number of variables, the number, strength and type of true relationships (three strengths, eight types), and the dependence between observations, such as repeated measurements of the same subject. Because the ground truth is known, the toolkit determines whether each claim an agent makes is true, including claims about relationships the generator did not add.
  • Claims and statistical tests. Agents state claims in standard forms, such as correlations, group differences, interactions and associations controlling for other variables. The toolkit assigns each form one prespecified permutation or resampling test, and verifies on null simulations that each test's false-positive rate stays close to its nominal level (App. A.5).
  • Multiple-testing corrections. The toolkit implements eight procedures that control the false discovery rate, including Bonferroni, BH (Benjamini & Hochberg, 1995) and BY (Benjamini & Yekutieli, 2001), e-value-based procedures (Wang & Ramdas, 2022), and online procedures that maintain control while an agent continues to propose claims (Xu & Ramdas, 2024; Fischer et al., 2024).
  • Agents. The toolkit integrates coding agents (Claude Code, Antigravity), evolutionary and tree-search agents, ShinkaEvolve (Lange et al., 2026) and AutoDiscovery (Agarwal et al., 2025), a minimal agent compatible with any language model, the hypothesis-validation agent POPPER (Huang et al., 2025), and scripted baselines such as random search. The LLM agents run on backbones from the Claude, Gemini and GPT families.
  • Extension and reproduction. The toolkit documents how to add new datasets and generate their ground truth, and how to add new agents and backbones. It also includes the configurations and scripts that run the paper’s main experiments.

References

  • Agarwal, D., Majumder, B. P., Adamson, R., Chakravorty, M., Gavireddy, S. R., Parashar, A., Surana, H., Dalvi Mishra, B., McCallum, A., Sabharwal, A. & Clark, P. (2025). AutoDiscovery: Open-ended scientific discovery via Bayesian surprise. Advances in Neural Information Processing Systems.
  • Benjamini, Y. & Hochberg, Y. (1995). Controlling the false discovery rate: A practical and powerful approach to multiple testing. Journal of the Royal Statistical Society: Series B (Methodological), 57(1), 289–300.
  • Benjamini, Y. & Yekutieli, D. (2001). The control of the false discovery rate in multiple testing under dependency. The Annals of Statistics, 29(4), 1165–1188.
  • Fischer, L., Xu, Z. & Ramdas, A. (2024). An online generalization of the (e-)Benjamini–Hochberg procedure. arXiv:2407.20683.
  • Huang, K., Jin, Y., Li, R., Li, M. Y., Candès, E. & Leskovec, J. (2025). Automated hypothesis validation with agentic sequential falsifications. Proceedings of the 42nd International Conference on Machine Learning, PMLR 267, 25372–25437.
  • Lange, R. T., Imajuku, Y. & Cetin, E. (2026). ShinkaEvolve: Towards open-ended and sample-efficient program evolution. International Conference on Learning Representations.
  • Wang, R. & Ramdas, A. (2022). False discovery rate control with e-values. Journal of the Royal Statistical Society: Series B (Statistical Methodology), 84(3), 822–852.
  • Xu, Z. & Ramdas, A. (2024). Online multiple testing with e-values. Proceedings of the 27th International Conference on Artificial Intelligence and Statistics, PMLR 238, 3997–4005.
AuthorsOpenReview ↗

Response to Reviewer 66Zy (2/4)

W1. A well-known principle that discovery agents overlook

"The central workflow is what I would consider as common-knowledge good science, something that should be obvious to anyone in the field."

We fully agree. Controlling false discoveries through rigorous statistical testing is an established principle of good science, well known to scientists. Discovery agents should follow the same practice, yet we found that they do not by default. In a new survey of 210 discovery agents and harnesses published since November 2023, 168 (80%) run no statistical test on what they report, 27 (13%) test each claim without correcting for multiple tests, and 12 (6%) correct only within a single step. Only 3 (1%) control error over everything they report, and all 3 are fixed pipelines in which no LLM agent chooses what is tested. Agents in our runs rarely add the control themselves, and a multiple-testing correction decided what an agent reported in only 2 of 534 runs (App. E.2).

Agents do not apply it reliably. When we left error control to the agent, we observed three failure modes.

  • Ignoring the correction. When an agent computed corrected p-values but then chose its own cutoff for what to report, 48.5% of its reported claims were false (App. E.2).
  • Reusing the evidence. Correction on the exploration split still left 21–51% false claims, because the agent chose its claims on the same data (Table 1). Given the holdout, Opus also used it to choose claims, and its FDR rose from 25% to 72% (App. E.6).
  • Writing invalid tests. Given the holdout and the exact procedure, Opus followed the procedure but treated related rows as independent, and 39% of its claims were false (App. E.6). Of the hypotheses that POPPER (Huang et al., 2025) validated with tests written by its agent, 27.5% were false (Table 2).

The audit removes all three failures by design. It runs outside the agent and tests each candidate once on a holdout the agent never sees, using one prespecified valid test per claim type. FDR stays at or below 1.3% for every agent (Table 1).

Further observations. Our results also reveal broader patterns in how discovery agents behave, and several of them can guide how these agents are built and used.

  • A stronger model does not replace error control. With the same harness, the FDR of Opus's own report is lower than that of Sonnet's (17.9% against 44.8%, Table 15). Across datasets, however, the FDR of the agents' own reports ranges from 0.4% to 95% (Table 13), so it depends on the data as much as on the model. Only control outside the agent holds in every setting.
  • Agents should explore broadly and leave reporting to the audit. An agent's own cutoff both admits false claims and discards true ones. ShinkaEvolve reports only a third of the true candidates it finds, and auditing its full list raises its true discoveries by 63% (Sec. 5.3).
  • Different FDR procedures balance reliability and recall differently. A procedure that makes fewer assumptions about how the tests depend on each other is more cautious. BY makes no such assumption and keeps FDR at or below 1.3%, while BH assumes independent or positively related tests and recovers more true discoveries at 2.5–5.0% FDR (App. E.3). Users can therefore choose the procedure that fits their data and the error rate they accept.

Educational and practical value. We agree that this work matters for education and implementation, as you note. Our analysis shows that false discoveries from discovery agents are common, large, and beyond the agent's own control. We hope the audit becomes a standard reporting step for discovery agents, and the released toolkit lets any agent adopt it.


References

  • Huang, K., Jin, Y., Li, R., Li, M. Y., Candès, E. & Leskovec, J. (2025). Automated hypothesis validation with agentic sequential falsifications. Proceedings of the 42nd International Conference on Machine Learning, PMLR 267, 25372–25437.
AuthorsOpenReview ↗

Response to Reviewer 66Zy (3/4)

Suggested stronger framing

"You're using Claude Code/GPT Models/Gemini Models, you will have on average, on these tasks, X false discoveries; here is our workflow to reduce this rate."

Thank you for this suggestion, and we apologize for the confusion. Your framing is exactly part of what we intended. The audit is a reporting step that works with any discovery agent. Sec. 5 reports how often each combination of backbone model and harness makes false discoveries, and how much the audit reduces them. Our experiments cover three model families and four harness designs. For this rebuttal, we also ran ShinkaEvolve with a second backbone, Gemini 3.8 Flash, on all 13 settings. We will make this framing explicit and open Sec. 5 with the table below.

BackboneHarnessOwn-report FDRAudit FDR
Claude Opus 5.5Claude Code (coding agent)17.9%0.49%
Claude Sonnet 5Claude Code (coding agent)44.8%0.46%
Gemini 3.8 FlashAntigravity (agent with built-in tools)63.5%0.57%
Gemini 3.8 FlashShinkaEvolve (evolutionary search) [new]53.1%0.49%
GPT-5.4-miniShinkaEvolve (evolutionary search)45.0%0.53%
GPT-5.4-miniAutoDiscovery (tree search)66.3%0.36%

Backbone and harness. In the same harness, Opus reports far fewer false claims than Sonnet. With the same backbone, the FDR of the agent's own report changes with the harness, for both GPT-5.4-mini and Gemini.

Distinct failure patterns. Antigravity reports almost every true candidate it finds but also many false claims, while ShinkaEvolve reports fewer claims and leaves out most of its true candidates (Sec. 5.1).

Control in every configuration. The agents' own reports stay far above 5% FDR in every configuration, while the audit keeps FDR below 0.6% in all of them without changing how any agent explores.

Reviewer_NHGQOpenReview ↗
Rating
3
Confidence
2
Informativeness
1
Presentation
2
Soundness
3
Read review
Paper summary

This paper focuses on characterizing the false discovery rate of agentic scientific discovery agents. This is a fairly timely topic as AI for science is now a sort of increasingly popular topic. What the authors do in particular is that they do a pretty systematic evaluation of the existing scientific agents on various tasks.The authors also build this careful synthetic benchmarks that can in a precise controlled way measure things like the false discovery rate and true discovery rate. The paper also evaluates several agent systems .

Critical strengths

I think the key strength of this paper is just that the empirical breadth is pretty impressive, and then the construction of the synthetic benchmarks to really carefully study this was a nice conceptual idea. Empirical breadth is important because it establishes that the results are robust across many of the different scientific agent scaffold systems that have been developed. And it's kind of nice to see how these different systems behave and have a precise, statistically grounded principled characterization of their performance. I also like the construction of the synthetic data sets because you can actually really be precise about whether the auditing behaves as expected in these controlled settings

Critical weaknesses

My largest concern is this idea that this doesn't really introduce anything new relative to kind of the existing methods and frameworks that have been developed in this space. For example Huang et al already perform this analysis (albeit with older models). Also, this idea of using carefully constructed synthetic benchmarks to measure statistical properties was also explored in a paper from 2024, Critical: Critic Automation of Language Models (which is not cited).

I think the tasks are a bit too toy relative to what these systems are capable of doing. And I think to some extent the more interesting applications of these scientific discovery agents are probably situations that can't really be cleanly characterized in the traditional statistical framework of whether this discovery is true or not. In particular, by restricting scientific discoveries to simple statistical claims, the authors make rigorous FDR control possible but this is also what makes things restrictive and not clear how to extend to other parts of the scientific pipelines that are more subjective like developing explanations or proposing experiments or synthetic info across many sources.

Questions for authors

How would you articulate the difference between your work and prior work in this space?

5 comments
AuthorsOpenReview ↗

Response to Reviewer NHGQ (1/4)

Thank you for your careful and detailed review. Your feedback helped us clarify the paper. We are glad you found the topic timely and the empirical breadth impressive, and that you saw the results as "robust" across many agent systems, with a "principled characterization" of how each one performs. To our knowledge, our paper is the first to measure systematically how often discovery agents report false claims, and the problem persists even when agents run their own statistical tests. We control these false discoveries with an audit that works with existing agents without changing how they explore. We answer each concern below.


W1 & Q1. Difference from prior work

Thank you for raising this point of clarification. Prior work, including POPPER and CriticAL, adds statistical checks to specific systems, and each check covers one hypothesis, one model or one step at a time. Our paper studies the problem across agents. We measure how often a wide range of existing discovery agents report false claims, using environments with known ground truth, and we diagnose why. The failure modes we find, such as testing claims on the data used to find them, testing each claim without correcting for multiple tests, and relying on tests that the agent writes, also appear in the designs of prior methods, and our audit fixes each of them by design. We also want to clarify that the audit is a reporting protocol for existing agents, for example agents that use POPPER. Below we compare our work with POPPER and CriticAL in detail.

POPPER (Huang et al., 2025). POPPER validates one supplied hypothesis with a sequence of falsification tests that LLM agents design and run, and it controls the Type-I error for that hypothesis, the chance of accepting it when it is false. A discovery agent proposes many claims as it explores the data, and each choice depends on what it has already seen. The agent's report therefore needs error control over the entire set of claims it proposes, through the false discovery rate (FDR), the share of reported claims that are false. POPPER leaves FDR control to future work, and it runs the tests that LLM agents write without a held-out split. Our experiments show that POPPER accepts many false claims even on held-out data, and that applying our audit on top of POPPER removes nearly all of them while keeping most of POPPER's true discoveries.

Per-hypothesis control does not bound FDR. We ran POPPER on the claims that Claude Code (Opus) proposed, using held-out data. Of the claims POPPER accepted, 27.5% were false, and the e-BH procedure that the POPPER paper suggests for FDR control lowered this share only to 13.7% (Table 2). POPPER's error control also depends on its backbone, because its LLM agents must write valid tests, and the POPPER paper reports that "higher-capability models are critical" (Huang et al., 2025, Table 4). A newer backbone did not close the gap in our runs. With GPT-5.6 Luna and the same settings as in our paper, POPPER still accepted 15% of claims on data with no true relationships, close to the 16.5% with GPT-5.4-mini (App. E.4). On the other datasets, 10–76% of the claims it accepted were false [new].

The audit applies on top of POPPER [new]. The audit is a reporting protocol that works with existing agents, including POPPER. Because the audit tests each claim with its own valid test, its FDR control is a guarantee that holds whatever backbone POPPER uses, whereas POPPER's own error control depends on the capability of its backbone. We applied the audit to the claims POPPER accepted, and it controlled FDR while keeping most of POPPER's true discoveries.

DataFDR, POPPERFDR, POPPER + auditTrue discoveries kept
Synthetic32.4%0.07%95%
Semi-synthetic24.4%0.33%74%
No true relationships100%0%–

With GPT-5.6 Luna as POPPER's backbone, the audit again kept FDR at or below 0.7% on the claims POPPER accepted, and reported none of them on data with no true relationships [new].


References

  • Huang, K., Jin, Y., Li, R., Li, M. Y., Candès, E. & Leskovec, J. (2025). Automated hypothesis validation with agentic sequential falsifications. Proceedings of the 42nd International Conference on Machine Learning, PMLR 267, 25372–25437.
AuthorsOpenReview ↗

Response to Reviewer NHGQ (2/4)

W1 & Q1 (continued)

CriticAL (Li et al., 2024). Thank you for this pointer. We will cite CriticAL and add it to our discussion. CriticAL addresses a related problem, the criticism of one scientific model, such as a Bayesian model, against data. An LLM proposes test statistics that capture where the model's predictions disagree with the data, and a Bonferroni correction controls false alarms across them. Our work differs in two ways.

  • Setting. CriticAL's LLM designs its checks from a description of the data, one model at a time, while a discovery agent chooses its claims by exploring the data and then reports many of them. We show that controlling false discoveries in this setting requires two fixes together, testing each claim on held-out data and correcting over all reported claims. Each fix alone leaves up to 51% false claims, while both together keep FDR at or below 1.3% (Table 1).
  • Ground truth. CriticAL evaluates its method on a small fixed set of planted cases, such as six model-dataset pairs. A discovery agent can claim any relationship in the data, so our environments grade every claim it makes against the true data-generating process.

Both works build on planted ground truth, and our environments follow established guidelines for simulation studies in statistics (Morris et al., 2019).

Survey of discovery agents [new]. We surveyed 210 discovery agents and harnesses published since November 2023. Of these, 168 (80%) run no statistical test on what they report. Another 39 (19%) control error only partly, testing each claim without correcting for multiple tests or correcting within a single step, and our results show that such partial control leaves many false claims (Table 1). The remaining 3 control error over everything they report, but only for hypotheses that a fixed pipeline sets. None of the 210 controls error when an LLM agent chooses its own claims while exploring, which is the setting of open-ended discovery that our audit addresses. To our knowledge, our paper is the first to analyze systematically how often agents in open-ended discovery report false claims, across four harnesses and three model families. Based on this analysis, we propose a protocol that controls these false discoveries on top of existing agents while leaving their exploration free to adapt to the data.


References

  • Li, M. Y., Vajipey, V., Goodman, N. D. & Fox, E. B. (2024). CriticAL: Critic automation with language models. arXiv:2411.06590.
  • Morris, T. P., White, I. R. & Crowther, M. J. (2019). Using simulation studies to evaluate statistical methods. Statistics in Medicine, 38(11), 2074–2102.
AuthorsOpenReview ↗

Response to Reviewer NHGQ (3/4)

W2. Task complexity

"I think the tasks are a bit too toy relative to what these systems are capable of doing."

We agree that statistical claims are a subset of scientific discovery, as our limitations section states. Within this subset, the audit supports a wide range of claims, and our evaluation is designed to carry over to real scientific data.

Complex claims. Our claim types include effects that differ between groups or depend on a third variable, nonlinear effects such as thresholds, associations after controlling for other variables, and trends and delayed effects over time. Claims can also be restricted to a subgroup defined by up to two conditions and can control for up to three other variables (App. A.2), so on a table with 50 columns the claim types can express about 101310^{13} distinct claims [new]. For example, one agent proposed the following claim on health survey data, which combines a subgroup, an association and three control variables: "Among participants told they have high blood pressure, serum osmolality and red blood cell count are positively associated when controlling for body mass index, blood urea nitrogen and systolic blood pressure."

Known ground truth. We agree that non-verifiability is one of the biggest challenges in open-ended scientific discovery. We built our environments with known ground truth precisely for this reason, so that we can measure the share of false claims an agent reports. We structure our evaluation in three levels of realism, from fully controlled data to real data judged by scientists.

  • Synthetic data give exact truth and let us vary sample size, effect strength and dependence between rows.
  • Semi-synthetic data keep the real variables and distributions of four scientific datasets, on fly neuronal connectivity, health measurements (NHANES), galaxies (SDSS) and superconductors (SuperCon), and add relationships of known strength (Sec. 4.3).
  • Real neuroscience data test whether the audit agrees with scientists where no ground truth exists. Three blinded neuroscientists judged 57% of the claims the audit kept to be real, against 21% of the claims that passed only an individual held-out test (Sec. 5.4).

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of the Discussion

We thank the reviewers for their careful reviews and the discussion. The reviewers found that our paper "accurately identifies a fundamental weakness of current AI scientists" (nzeC). They saw independent statistical auditing as "a particularly insightful and elegant solution" (nzeC) and "a meaningful improvement on the baseline agent performance" (66Zy). They valued the breadth of our evaluation, which "establishes that the results are robust" across agent systems and gives "a precise, statistically grounded principled characterization of their performance" (NHGQ). Across synthetic and semi-synthetic settings, together with blinded expert evaluations on real neuroscience data, these "extensive experiments" provide "compelling evidence for the effectiveness of the proposed approach" (nzeC). After the discussion, Reviewers 66Zy and nzeC wrote that our responses addressed their concerns, and all three reviewers now support the paper. Below we summarize our answers to the comments and suggestions across reviews.


What is new (NHGQ, 66Zy, nzeC). Our paper shows what happens when discovery agents are left to control their own errors, and provides a control that works outside the agent.

  • Agents report many false claims. Across five agent systems, 18–66% of the claims the agents reported were false, even though they found many true candidates.
  • The obvious fixes fail, even with instructions. Given a holdout and the exact testing procedure, Claude Code (Opus) still reported many false claims. POPPER, which validates each hypothesis with tests an agent writes, also accepted many false claims.
  • None of the agents we surveyed fixes this. In our survey of 210 discovery agents published since November 2023, none controls error when an LLM chooses its own claims.
  • The problem was not measurable before. Existing benchmarks check whether an agent recovers known targets, and they have no ground truth for the other claims it reports. Our synthetic environments and plasmodes give ground truth for every claim.
  • The audit restores control outside the agent. It keeps the false discovery rate (FDR) at or below 1.3% for every agent, without changing how agents explore. Applied on top of POPPER, it removed nearly all of POPPER's false claims and kept most of its true ones.

Following 66Zy's suggestion, we reorder the contributions so that the measurement comes first and the audit follows as the fix.


Claims beyond the structured claim types (NHGQ, nzeC). The audit needs only a valid test for each claim, a holdout that exploration never touched, and correction for multiple testing over all reported claims. New results extend it in three ways.

  • Free-form claims. Agents wrote claims in their own words and tested them with their own code. The audit kept FDR at or below 0.7% and confirmed 87–88% of the true claims. When an agent wrote invalid tests, the audit lowered FDR from 10.9% to 0.8%.
  • New claim types. The audit supports a new claim type once we show that its test keeps the false-positive rate at the stated level on data with no true effect. We did this for an indirect effect and bimodality, two types outside our set, and the audit kept FDR at 0.5%.
  • Proposed experiments. The agent proposed new experiments and predicted their outcomes, and we ran the experiments to test the predictions. In the agent's own report, 68–74% of the predictions were false, and the audit kept FDR at or below 1.1% on average.

Recall and data size (nzeC, 66Zy). The audit controls FDR even with limited data, and its recall grows as more data become available.

  • Missed claims are mostly weak effects. The audit recovers 81% of strong, 70% of medium and 49% of weak planted effects.
  • Recall grows with the holdout. The audit recovers more true claims as the holdout grows, up to 93% at 2,000 rows, with FDR below 0.8% at every size.
  • Splitting pays off even when data are scarce. On a small dataset, splitting the data between the agent and the audit gave 0.24% false discoveries, against 92% when the agent used all the data and reported on its own.

Together, these results show that error control outside the agent is a necessary part of AI-driven discovery. As AI scientists propose claims faster than people can check them, the reliability of what they report will decide how far their discoveries can be trusted. Our paper measures that reliability, shows that agents fall short even when instructed, and gives a fix that any agent can use today.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.