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Under review as a conference paper at ICLR 2027

Causal-Discovery-Bench: A Verifiable Sandbox for Diagnosing and Improving LLM Agents in Sequential Causal Discovery

Abstract

As large language model (LLM) agents get actively adopted for autonomous research, they must not only reason over existing evidence, but also design informative experiments, allocate resources, analyze sequential observations, and decide when to stop and make conclusions. Yet these capabilities remain poorly measured. We introduce Causal-Discovery-Bench, a verifiable sandbox with configurable structural equation models and resource constraints to evaluate sequential experimental design and causal discovery without domain-semantic cues. Across 2,842 episodes with 13 models from 5 vendors, we characterize task complexity and analyze agent behavior along more than 40 diverse metrics. Agents' performance exhibits a four-level difficulty hierarchy spanning single-experiment design, sequential exploration of causal relationships, resource-aware experimentation balancing cost and statistical power, and autonomous resolution of conflicting evidence. We identify a substantial performance gap between causal inference from correctly curated evidence and navigating causal discovery through autonomous experimentation: Analyzing agents’ action trajectory attributes 92% mistakes on experimental design rather than on inference, which is further consolidated with ablation studies. Relaxing resource constraints alone does not reliably resolve failures in sequential discovery. In contrast, basic statistical tools substantially improve performance across multiple model families, while advanced tools provide little additional benefit when models lack prerequisite lower-level capabilities.

Primary area:
datasets and benchmarks
Keywords:
causal discovery, sequential experiment, LLM benchmark, agent evaluation.

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_6kMeOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper introduces CAUSAL-DISCOVERY-BENCH, a suite of sandbox environments designed to evaluate LLM agents on interactive, sequential experimental design and causal discovery under resource constraints. Operating on linear Structural Equation Models (SEMs) with randomized variable names to eliminate domain-semantic priors, agents must allocate finite budgets between observational sampling and experimental dodo-interventions to identify direct causal parents of an outcome variable YY and estimate their direct treatment effects. Empirically, the benchmark tracks agent behavior using 40 metrics across 7 families, establishing a four-level difficulty hierarchy: single-experiment design, sequential hypothesis coverage, resource-aware sample sizing, and resolving conflicting evidence.
The paper demonstrates a fundamental gap between causal inference and sequential experimentation: 93.9% of agent errors stem from experimental design failures, specifically failing to run properly controlled experiments. Furthermore, increasing action budgets merely increases candidate coverage without inducing controlled experimentation. In contrast, hard interface constraints (such as capping the per-call sample purchase size) successfully force controlled experimentation and yield far larger performance gains than prompt engineering alone.

Critical strengths

S1 Actionable Error-Attribution Methodology: By charging every wrong conclusion back to the agent's evidentiary state via four ordered levels and cross-validating with targeted ablations, the paper provides a much denser, more actionable diagnostic signal than existing benchmarks. This cleanly proves that failures stem from experimental design rather than downstream inference.

S2 Rigorous Measurement Validity: The authors thoroughly stress-test their benchmark using IRT-based ability fits and bootstrap-bounded sampler robustness checks. This rigor ensures that reported cross-model performance differences reflect genuine agent capabilities rather than benchmark artifacts.

Critical weaknesses

W1 Key diagnostic claims rely on a single-model ablation. Although the broad benchmark evaluates 13 models, the specific ablation experiments producing the headline finding (~94% of errors caused by experimental design) were conducted exclusively on Claude Sonnet 4.6. Because default controlled-experiment behavior varies widely across model families, generalizing this single-model error-distribution ratio to LLM agents as a class lacks broader empirical validation.

W2 Scope Restricted to Unconfounded Linear Models. While assuming fully observed variables and linear structural equations enables clean closed-form ground truth and exact budget derivations, it limits the benchmark's realism. Real-world scientific discovery frequently involves non-linear dynamics and unobserved confounders, which this idealized setup does not test.

Questions for authors
  1. Clarification Can the central ~94% design-vs-inference error-attribution claim be replicated on at least 2–3 additional models spanning the performance range already shown in the cross-model comparison?
  2. Clarification How does this benchmark's design relate mechanistically to [1,2] and other closely-dated 2026 agentic causal-discovery benchmarks — specifically, what differentiates it beyond the error-attribution ladder and remediation ablations?
  3. Suggestion for future work Is there a plan to extend the sandbox to full DAG/skeleton recovery rather than single-outcome parent identification, and would the design-vs-inference conclusion be expected to hold at that scale?

[1] Sagar Deb et al. "Active Causal Discovery Benchmark: Evaluating LLM Agents Under Budgeted Interventions, 2026."

[2] Zi-Rong Li et al. "CausalArena: Benchmarking Causal Discovery in the Foundation Model Era, 2026."

2 comments
AuthorsOpenReview ↗

Replication across models, literature comparison and future work

Thank you for the comments.

Replication across models. It replicates. The ablations that motivate the ladder were run on claude-sonnet-4-6, which carries most of the attributed errors. Appendix G now reads the same ladder on every model carrying at least twenty attributed errors.

modelattributed errorsshare on the design side
claude-sonnet-53096.7% (29/30)
claude-sonnet-4-62,87694.2%
qwen3.7-plus5192.2% (47/51)
gpt-5.6-terra13485.8% (115/134)

Each row is that model's own attributed errors split by the ladder, so these are the per-model version of the 94.4% in the body and not a ranking of the models. Across three vendors the share runs from 85.8% to 96.7%, with an unweighted median of 93.2% over the four.

Relation to the concurrent benchmarks. This is answered in our general comment on distinction from relevant concurrent works, which sets out what the ablations test that the four benchmarks do not.

Full DAG and skeleton recovery. That is the extension we would build next. It has two problems that the single-outcome task does not. The agent would have to split one budget across many targets, and it would have to work out which way each edge points, which is free now because every edge runs into the one outcome. Whether the design-versus-inference split survives there is exactly what we would want to measure. We would like to measure and experiment first before extrapolating from the single-outcome result.

Dear Reviewer 6kMe,

Thank you very much for your encouraging score and detailed review! We would be very happy to clarify any concerns that you may have.

Best, The Authors

Reviewer_ejQaOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces Causal-Discovery-Bench, an interactive benchmark for evaluating LLM agents on budget-constrained causal discovery and effect estimation. Using hidden linear structural equation models, agents can acquire observational or interventional data under a limited budget, with the goal of identifying the direct parents of a target outcome and estimating their average direct effects. The authors evaluate 13 models across 3,322 episodes, examining both final performance and intermediate decision-making through trajectory-level diagnostics. The results suggest that major challenges arise during evidence collection and experimental design rather than final inference, while procedural guidance and interface improvements can help agents conduct more effective causal investigations.

Critical strengths

a. The benchmark combines causal ground truth, budget-constrained data acquisition, and interaction trajectories to assess not only final accuracy but also how agents gather and use evidence. This provides a useful setting for evaluating LLM agents' causal reasoning and experimental decision-making.

b. The paper systematically examines the effects of evidence availability, budgets, tools, and prompting strategies on agent performance. The inclusion of a non-LLM reference statistician further demonstrates the feasibility of the benchmark and provides a useful point of comparison.

Critical weaknesses

a. The diagnostic framework primarily considers interventional evidence and may overlook valid observational approaches to causal estimation.

b. There appears to be an inconsistency in how outcome variance is calculated under the random-coefficient SEM, which may affect statistical power and budget calibration (See Question b below). Additionally, the differing reported episode counts (3,322 vs. 3,779) and failure attribution rates (93.9% vs. 94.5%) would benefit from clarification to better support the main conclusions.

Questions for authors

a. Could the authors clarify which experimental conditions contribute to the reported 93.9% failure attribution? How does the framework distinguish insufficient evidence from incorrect inference, particularly when valid observational evidence is available, and does the main conclusion hold when such evidence is considered?

b. Could the authors clarify which variance estimate is used for power calculations, diagnostic labels, and purchase caps, given the differences between Appendices A and B? It would also be helpful to clarify the sample-size conventions, whether hidden parameters are used, and whether these choices affect the reported results.

c. Could the authors reconcile the reported episode counts (3,322 vs. 3,779) and failure attribution rates (93.9% vs. 94.5%), including the relevant experimental conditions and exclusions? Additional details on the diagnostic decision rules and uncertainty estimates would help assess the robustness and generalizability of the findings.

3 comments
AuthorsOpenReview ↗

Experimental condition clarification, variance estimate, and episode count alignment

Thank you for the comments. We answer the three points in order.

Wa, Qa. Observational evidence, and whether the conclusion holds.

You were right that the ladder read interventional contrasts only. A direct effect can be identified in two ways in the sandbox, by a controlled contrast or by regressing the outcome on the remaining candidates, and the submitted ladder credited only the first. We did not change the environment, only the scoring. Appendix G recomputes the attribution with the first level crediting either route.

levelcontrast onlycontrast or adjustment
no identifying evidence obtained20.5%1.0%
candidate never touched62.3%19.2%
obtained but underpowered11.2%11.2%
evidence in hand, no answer drawn from it2.4%65.0%
submitted while still unresolved3.6%3.6%
first three levels combined94.0%31.3%

Under either reading, the conclusion holds. The level the paper defines as inference, resolving conflicting evidence, is 2.4% in both columns.

The 65.0% comes from a regression we ran after the fact, not from the agent. For each candidate we took the rows the agent had already bought, ran the adjustment ourselves, and credited the candidate whenever our regression got the answer right. The agent never ran that regression, so the second column is an upper bound rather than a corrected attribution.

Wb, Qb. The variances.

Three different quantities go by the name variance in the paper, doing three jobs. Appendix B now has a table separating them.

used forquantity
the power formula n* = 16 sigma^2 / delta_min^2sigma^2 = Var(eps_Y), the variance left in Y once every other parent is pinned, derived in Appendix A
normalising the budget across instances, B_test = 10(p+1) c_o + min(2k,p) * 16 sigma_ref^2 / delta_min^2 * c_esigma_ref^2, the largest empirical variance of the per-unit coefficient deviations on an edge into Y, plus the optional extra outcome noise, defined in Appendix B
diagnostic labels and the per-call purchase capthe empirical standard error of the agent's own inverse-variance pooled estimate, compared against the fixed constants `

The first two enter formulas and both were already defined in the submitted version. The third enters no formula. The default budget is 5 B_test, so every budget-scaled study depends on sigma_ref^2, and that dependence is unchanged. None of the three involves a hidden or a fitted parameter. Nothing was recomputed and no reported number changed.

Wb, Qc. The counts.

This was our error and we have corrected it. Thank you for pointing it out. The corpus contains 3,802 episodes: the 2,842 that reached a terminal state, plus two 480-episode runs of the crossed budget and toolbox sweep. 3,322 omitted one of those two runs, and 93.9% is the attribution on that smaller subset. 3,779 excluded 23 episodes scored from stored records, and including them moves the attribution by 0.1 points. One denominator is now used throughout the paper and the attribution is 94.4%. The definition is in Section 5.

This was our error and we have corrected it. Thank you for pointing it out. The corpus contains 3,802 episodes: the 2,842 that reached a terminal state, plus two 480-episode runs of the crossed budget and toolbox sweep. 3,322 omitted one of those two runs, and 93.9% is the attribution on that smaller subset. 3,779 excluded 23 episodes scored from stored records, and including them moves the attribution by 0.1 points. One denominator is now used throughout the paper and the attribution is 94.4%. The definition is in Section 5.

The decision rules are now stated in Appendix G as an ordered list of five mutually exclusive states, with each error charged to the first step it failed. Robust and classical standard errors pick the same parent set in 99.7% of fits at one B_test and in all of them at the default budget, so the uncertainty estimates do not drive the attribution.

AuthorsOpenReview ↗

Regarding "The diagnostic framework primarily considers interventional evidence and may overlook valid observational approaches to causal estimation"

Regarding the comment "The diagnostic framework primarily considers interventional evidence and may overlook valid observational approaches to causal estimation", we fully agree that observational approaches can provide valid causal estimates when the relevant identification assumptions hold. Our evaluations already include regression and causal-discovery tools, allowing agents to use observational evidence in their analyses.

We would likely to remark that there is a distinction between access to an estimation method and whether the available data can identify the target direct effects. When observationally indistinguishable models imply different parent sets or direct effects, additional observational samples or more sophisticated estimation tools cannot resolve that ambiguity. In this case, appropriately designed interventions are needed for the identification.

In fact, our results suggest that agents can analyze evidence effectively (including using some observational study analysis tools) but can be improved in the evidence acquisition part: recognizing when the available evidence is insufficient and selecting additional observations or interventions that address the unresolved causal questions.

Dear Reviewer ejQa,

Thank you very much for your thoughtful review and follow up questions! As the discussion period is approaching the end, we would be happy to clarify any points or concerns that you may have. Thank you again!

Best, The Authors

Reviewer_MVYGOpenReview ↗
Rating
3(+1)
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposed Causal-Discovery-Bench, a sandbox environment where an LLM agent needs to identify the direct outcome Y and estimate their effects with no hidden variables. Each env the agent buys observations and do experiments though four priced actions under a total budget.

Critical strengths
  1. The motivation sounds and implemented well I perceive the importance on LLM for experiment design evaluation, and authors' diganostic design with exact ground truth (known SEM without LLM judge) makes budge an effective control variable, and both estimation only and inference-only ablations are informative.

  2. Informative and actionable findings The findings that budge and tool increase raise coverage but not controlled testing, and prompt wording is less effective compared to capping purchase size is actionable result on why current LLM fail.

Critical weaknesses
  1. The setting is narrow on linear SEM where a script can succeed The sandbox is a fully observable linear SEM with a single outcome and no hidden confounding where a linear procedure solves it well. Here the setting makes the optimal strategy relatively simple w/ a two-arm contrast makes the causal discovery slightly over-stated.

  2. The contribution beyond prior work needs to be clearly stated The work extends CausalProfiler and identify CausalLab as closest work (no empirical comparison) from my read I want to understand what is the additional part and why these components matters.

Questions for authors
  1. How do agent results compare with the scripted solver at equal budget
  2. Do the findings hold or extensible for nonlinear mechanisms, hidden confounders, or settings where conditioning on observational data is optimal?
  3. also there is an Outline before the introduction, is that a typo needs to be clean up?
2 comments
AuthorsOpenReview ↗

Scripted solver comparison, hidden confounder generalisability and typo fixing

Thank you for the comments.

  • For Q1 comparison with scripted solver, the scripted solver (linear part, we will update non-linear experiment results soon) reaches 98.7% (296/300) at one B_test and 100% (300/300) at five. Agent budgets run from 5 to 43.6 B_test, median 8.6, so every agent episode had at least the budget at which the script is perfect, and the agents reach 33.3% (16/48). What we found is that the gap does not come from the budget. More details can be found in Appendix B.
solverbudgetexact recovery
scripted, observational conditioning1x B_test98.7% (296/300)
scripted, observational conditioning5x B_test100% (300/300)
LLM agents, six models5 to 43.6x B_test, median 8.633.3% (16/48)
  • For hidden confounder generalisability in Q2 (we will address non-linear in updated design and update separately), we would respectfully push back. The ladder charges the first step an agent failed, so the right answer has to have been reachable. Where the agent can intervene, a hidden cause is harmless and our findings carry over. Where it cannot, adjustment is biased and a wrong edge no longer says whether a step existed, so the attribution is undefined. Our general comment on unobserved confounding has the argument, and the revision states this as a scope limitation in the Conclusion. Please also refer to Observational evidence & Unobserved confounding in the general comment for more details.

  • Typo in introduction. Thank you for kindly pointing that out, we've fixed it in the revision.

Dear Reviewer MVYG,

Thank you very much for your detailed feedback, especially your question, “Do the findings hold or extend to nonlinear mechanisms, hidden confounders, or settings where conditioning on observational data is optimal?” We have shown that similar patterns hold under nonlinear mechanisms and discussed why settings with hidden confounding may not be the most suitable for our causal tasks.

If there is anything we can further clarify, please let us know.

Best, The Authors

Comments on the paper

2 comments
Area_Chair_qAiGOpenReview ↗

Please take a look at the general response

Dear reviewers,

As the rebuttal period is about to end, please take a look at the authors' general responses.

Best,

AC

AuthorsOpenReview ↗

Non-linear mechanism study (2)

Detailed results of Non-linear mechanism study (1)

1. More budget buys both more controlled experiments and better performance

budgetcontrolled experiments (median)controlled ratecurve error (median)paired vs 1×
1×40.530.1866—
5×50.550.09810.58
25×80.640.07430.38
125×140.700.05340.28

Over the 125× span the agent runs 3.5× as many controlled experiments (4 → 14), its controlled rate rises from 0.53 to 0.70, and median curve error falls 3.5-fold (0.1866 → 0.0534). More budget buys more controlled experimentation and better performance together, monotonically at every rung.

2. A written procedure installs controlled experimentation; the behaviour is installable, the capability is not

prompt variantcontrolled experiments (median)controlled rateepisodes fully controlledcurve error (median)paired vs V0
V0 baseline (no guidance)40.5432/1950.1017—
V1 objective module50.5948/1940.10891.02
V2 strategy module90.97178/1950.07790.80
V3 combined90.95167/1950.07840.89

The strategy module more than doubles controlled experiments (4 → 9), lifts the controlled rate from 0.54 to 0.97 and the share of fully controlled episodes from 32/195 to 178/195, and cuts median curve error from 0.1017 to 0.0779, paired ratio 0.80. V1 moves neither behaviour nor accuracy; V3 matches V2 and adds nothing to it.

The guidance works on the models that do not plan for themselves. Three models run essentially no controlled experiment without being told to. Given the procedure, all three run them and all three get better:

model (no controlled experiments unprompted)controlled exps V0 → V2curve error V0 → V2
claude-sonnet-4-60 → 90.5029 → 0.2457
claude-sonnet-4-6-thinking0 → 80.4452 → 0.3652
qwen3.7-plus1 → 70.5981 → 0.1618
all three pooled0 → 80.5077 → 0.2457

But it does not make them competitive. Against the eight models that run controlled experiments unprompted — compared at their baseline, with no guidance at all — every one of the three still loses:

modelconditioncontrolled exps (median)curve error (median)
gpt-6-astraV0, no guidance90.0512
gemini-4-argonV0, no guidance120.0549
qwen3.8-maxV0, no guidance100.0695
claude-fable-5-1V0, no guidance80.0735
claude-sonnet-5V0, no guidance80.0825
gpt-5.6-solV0, no guidance60.0902
gemini-3.8-flashV0, no guidance50.1047
deepseek-v4-proV0, no guidance70.1195
qwen3.7-plusV2, procedure given70.1618
claude-sonnet-4-6V2, procedure given90.2457
claude-sonnet-4-6-thinkingV2, procedure given80.3652

The two blocks do not overlap: the weakest unprompted planner (0.1195) beats the strongest guided model (0.1618), and pooled the guided group is 3.1× worse (0.2457 against 0.0790, Mann-Whitney p=3.8×10−11p = 3.8\times10^{-11}, 45 against 120 episodes). The behaviour is installable; the capability is not. The guidance is not a weak-model-only effect either — the two middle models, at a V0 median of 3 controlled experiments, go 3 → 8 in behaviour and 0.1075 → 0.0713 in accuracy.

| arm | optional tools offered | curve error (median) | geometric mean | paired vs A0 (mean) | --- | --- | --- | --- | --- | --- | | A0 core only | 0 | 0.0941 | 0.1007 | 1 | | A4 shape fitting | 1 | 0.0761 | 0.066 | 0.66 | | A5 curve toolkit | 2 | 0.0814 | 0.0877 | 0.87 | | A2 stats basic | 3 | 0.1063 | 0.0927 | 0.92 | | A3 causal structure | 4 | 0.1107 | 0.1352 | 1.34 | | A1 all tools | 16 | 0.1017 | 0.0886 | 0.88 |

A4 offers one tool — regress_basis, the basis regression this estimand requires — and leads on the median, the geometric mean and the catastrophic-cell count, while the sixteen-tool arm lands with the zero-tool arm. A1 is a superset of A4: the same regress_basis is on both menus, which is what makes the next table a measurement of dilution rather than of two different toolkits. Measured on the all 390 instances:

optional tools offeredregress_basis total callsmedian per episodeepisodes using it
A4 (sole option)12,1354.5377/390
A1 (one of sixteen)161,5493.7374/390

A4 draws more regress_basis calls than A1 on the same instance in a 27.5% reduction in total use of the effective tool when it is one of sixteen rather than the only option. Adoption is reduced (377 vs 374 of 390): the agent never abandons the right tool, it uses it less intensively. The accuracy consequence the single-model study inferred from this is not there.

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

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