acceptodds
Under review as a conference paper at ICLR 2027

Learning Applicability Envelopes for Conditional Independence Testing

Abstract

Conditional independence (CI) testing is a foundational task in statistical inference, yet even for discrete data, classical CI-test methods fail in different and often incompatible regimes. This raises a practical question: *given a specific CI-testing instance, which test method should be trusted?* To study this question, we first synthesize verifiable data and post-train a large language model to combine the outputs of four representative CI-test methods, , Fisher's exact, mutual information (MI), and logistic regression, into a final CI decision, based on the outputs of the CI tests and a four-dimensional feature vector characterizing the difficulty of the instance through observable data-quality and conditioning properties. We then analyze the router's learned policy in method-disagreement regimes and extract quantitative decision thresholds over the feature space to analyze **applicability envelopes** of the different CI-test methods. We validate these thresholds against reference transitions in test error rates and examine their variation across data regimes. Overall, our LLM router achieves the highest F1 on our synthetic evaluation set and shows competitive transfer performance with matched non-LLM routers on three additional Bayesian networks and the Sachs dataset. Furthermore, our analyses identify boundaries consistent with changes in test reliability and connect an MI boundary to the treatment of collapsed strata in the tested implementation's degrees of freedom. Finally, we evaluate the router on the Sachs flow-cytometry dataset at both the CI-testing level and the downstream causal-discovery level, where it achieves the best skeleton recovery among the evaluated PC variants.

Primary area:
reinforcement learning
Keywords:
Conditional Independence Testing, Large Language Model, Reinforcement Learning, Causal Discovery.

Reviews

Among:
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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_VgKNOpenReview ↗
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1
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3
Informativeness
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Paper summary

This paper studies how to combine conflicting outputs from several classical discrete conditional-independence tests. It trains an LLM router using verifiable synthetic CI labels to predict a final independence/dependence decision from four test outputs and four hand-designed instance features, and then analyzes the router’s disagreement patterns to extract empirical applicability envelopes for the individual tests.

Critical strengths

(1) The paper studies a practically relevant problem. Classical CI tests can behave very differently across finite-sample regimes, and learning when particular tests become unreliable is potentially useful for causal discovery and other downstream applications.

(2) The applicability-envelope analysis leads to at least one concrete and useful diagnostic result. The learned MI boundary motivated an investigation of collapsed conditioning strata and revealed a degrees-of-freedom issue whose correction substantially improved CI accuracy.

Critical weaknesses

(1) The role of the 7B LLM in the proposed routing framework is not sufficiently justified. Although the router is described as reasoning over conflicting CI-test evidence, the RLVR objective supervises only the final independent/dependent decision; it does not explicitly train the model to select which CI test should be trusted, and the generated rationale is not part of the reward. The decision-relevant inputs are also largely structured numerical quantities, and it is unclear what additional information, pretrained knowledge, or reasoning capability of a 7B language model is expected to contribute beyond a standard tabular classifier. The empirical results reinforce this concern: RLVR achieves only a small average F1 gain over GBDT and random forest (0.725 vs. 0.717/0.716), and is slightly worse than GBDT on Sachs. Moreover, the LLM receives additional semantic prompt information beyond the twelve numerical inputs used by the tabular baselines, making the source of this small gain unclear despite substantially higher computational cost.

(2) The proposed applicability envelopes are inferred post hoc from the router’s binary decisions rather than learned directly. The model is trained only to predict independent/dependent, while “trust” in an individual CI test is subsequently inferred from whether the router overrules that test. The same envelope-extraction procedure is also applicable to non-LLM routers, with simpler models showing competitive or better boundary recovery on some metrics. This makes it unclear whether the main contribution is specifically an LLM-based applicability learner, or more generally a post-hoc analysis of ensemble decisions.

Questions for authors

(1) How were the four CI tests selected, and how sensitive is the method to the test library? Would the routing policy and learned applicability envelopes remain stable if tests were added, removed, or replaced?

(2) Why were conditioning order, evenness, sparsity, and degeneracy chosen as the four applicability features? Are they intended to sufficiently characterize CI-test difficulty, and how sensitive are the results to adding or removing features?

(3) What information does the LLM exploit beyond the twelve numerical inputs? Have the authors tested Qwen using only these numerical values, without method names, query identifiers, or natural-language formatting?

(4) Why not learn each CI test’s reliability directly from the instance features and ground-truth labels? Since the synthetic data provide verifiable CI labels, what does the intermediate routing model add over directly estimating test error probabilities or applicability boundaries?

(5) How stable are the learned applicability boundaries across data-generating regimes? In particular, how do they change with graph density, variable cardinality, CPT/Dirichlet concentration, and sample size? And can the authors provide broader real-world validation beyond Sachs? The current real-data and downstream causal-discovery evaluation is limited to only one benchmark.

6 comments

We really appreciate reviewer's comments, and here we address each concern. Part 1 of our response:

The role of the 7B LLM is unclear. The reward only scores the final decision, test selection is not trained, the rationale does not enter the reward, the inputs are numeric, the gain over GBDT is minimal, and the LLM receives semantic information that the tabular baselines do not.

We agree that the motivation of using LLM should be supported by experiments stronger, and we emphasize that its output rationale can increase the explainability.

We first add modern baselines UCI and wUCI [1] and take them into the input method library, then retrain the LLM:

MethodSyntheticchildalarminsuranceSachsMean
χ²0.5410.5370.5600.6150.6260.576
Fisher0.6890.6760.6750.6690.6700.676
LR0.5200.4170.5280.4040.1630.407
MI0.6760.6780.6800.6690.6690.674
UCI (new)0.7170.6930.7550.7000.7090.715
wUCI (new)0.7240.6980.7590.6930.7110.717
RLVR0.7460.7210.7460.7400.6930.729
RouterBoundariesPrecisionRecallDirection agreementFalse alarmsGapNullGap/null
GBDT (same inputs)130.4620.20077.8%20%0.1890.2080.91
RLVR170.5880.35383.3%25%0.0960.2360.41

As we can see from the tables, after including more method into library, the advantages of RLVR become larger compare to the most competitive baseline GBDT on both boundary direction and location accuracy.

We also tried to extract boundaries from the rationales. For every rationale, we record which of the tests it follows and which it sets aside. We then fit the change-point model of the paper to the set-aside rate of each test along each structural feature. We compare this with the extraction from verdicts used in Table 2. On the 2,368 disagreement instances of the unfiltered pool, the two extractions are complementary. The rationales show the boundary of χ² far more clearly than the verdicts do. The rate at which χ² is set aside rises from 0.62 to 0.91 once the order exceeds 5 (ΔBIC = −216), while its overrule rate rises from 0.08 to 0.16 (ΔBIC = −10). The verdicts show the boundary of MI more clearly, its overrule rate rises from 0.46 to 0.71 once sparsity exceeds 0.3 (ΔBIC = −157), against 0.40 to 0.53 in the rationales (ΔBIC = −29). We observe:

  1. The rationale takes part in the decision. When the trained router is forced to answer without writing its rationale, accuracy falls by 0.020 [0.007, 0.034], with the same sign on all five datasets. The evidence in the rationale can also be checked , all 11,651 p-values cited belong to the test named.
  2. The rationale reflects the applicability boundaries. The router sets χ² aside in the region where its Type-I error rises from 0.050 to 0.109, including on instances where the final decision still agrees with χ². Training sharpens this pattern. For the untrained model the same rate rises from 0.63 to 0.81 (ΔBIC = −55).
  3. The router adapts to a changed test library without retraining. With the three asymptotic tests removed at inference, its accuracy is 0.662, while a GBDT trained on the same inputs falls to 0.593 (difference +0.070 [0.047, 0.094]). When a test never seen in training is added, 96.3% of the rationales use it and accuracy does not decrease. A tabular model has a fixed input layout and cannot do either.

Part 2 of our response:

The envelopes are derived after the fact from binary decisions rather than learned, and the same extraction applied to a non-LLM router gives comparable results.

As shown above, LLM's rationale can be taken as a more straight forward "learned envelopes" stated in natural language. Meanwhile, Reading learned structure from a model’s behaviour is the usual practice such as in algorithm selection [1] and interpretability [2].

How were the four tests chosen, and are the conclusions stable when tests are added, removed or replaced?

The four tests are the defaults of pcalg, bnlearn and causal-learn. We also evaluate removing the three asymptotic tests. RLVR loses 0.006 and GBDT loses 0.073 (difference between the two +0.070 [0.047, 0.094]).

Why these four features, and how sensitive are the results to them?

Each feature corresponds to a known reason for a discrete CI test to fail. They are the coordinates in which the applicability boundaries are expressed. And as we shown in the paper and rebuttal, these features are sufficient to clearly delineate the differences between the various methods.

Why not estimate each test's reliability directly from features and ground-truth labels?

Direct estimation is how we obtain the reference boundaries of Table 2. It gives population-level boundaries and needs ground-truth labels. The router addresses the complementary task. On a new instance without a label it returns a decision, and its rationale names the tests it follows and the tests it sets aside. Table 2 and the rationale analysis above measure how far these instance-level decisions agree with the directly estimated boundaries.

How do the boundaries move with graph density, cardinality, Dirichlet concentration and sample size? Is there real data beyond Sachs?

Appendix F of the submission reports the varying of sample size and cardinality. Graph density and Dirichlet concentration act on a CI test only through the contingency table, which the four features describe. The synthetic graphs are sampled with varying edge density and the three expert networks have different conditional probability tables, so both factors vary in our data. On real data, we would like to argue that the evidence beyond synthetic DAGs also rests on the three expert networks (child, alarm, insurance). Their structures, cardinalities and conditional probability tables come from the application domain. The data are sampled from the networks, so every independence label is an exact d-separation statement. This is the property that the critique finds missing in Sachs, where the reference graph is itself uncertain. For evaluating a CI test, an exact label matters more than the provenance of the samples, because an error in the reference graph is counted as an error of the test. The three networks contribute 856 evaluation instances with real variable names.

[1] Smith-Miles, Kate, et al. "Towards objective measures of algorithm performance across instance space." Computers & Operations Research 45 (2014): 12-24.

[2] Craven, Mark, and Jude Shavlik. "Extracting tree-structured representations of trained networks." Advances in neural information processing systems 8 (1995).

Thank you for the response and additional experiments. After reading the rebuttal, some of my questions have been clarified, but I am still a bit confused about two points.

(1) For W1, I understand that the authors emphasize the usefulness of LLM-generated rationales. However, I am still not sure why we need to fine-tune a 7B LLM for this task. Since pretrained LLMs can already generate rationales, as also demonstrated by the Claude-generated rationales used for SFT, I wonder whether we could directly extract structured information from such rationales and use it to train a lightweight router. I think this would be a useful comparison to better understand the benefit of fine-tuning the entire 7B model. Also, for the changed test-library setting, wouldn't retraining a lightweight router be a relatively simple and inexpensive alternative?

(2) For W2, I agree that extracting learned structure from model behavior is common in interpretability research. However, at least from my understanding, the main task in this paper is to train a router that combines multiple CI tests to make a final decision, rather than using the LLM to systematically analyze the applicability of individual tests. The applicability envelopes seem to be a subsequent analysis of the router's behavior. Moreover, even for this analysis, the boundaries are characterized using only four pre-selected features, with limited consideration of other properties of the underlying distributions or dependence structures. I am therefore still unsure how much we can learn from these boundaries about the actual applicability of different CI tests, or whether they can provide more general insights beyond the selected features.

These are the two main points I remain uncertain about after reading the rebuttal. Thanks again for the additional clarifications.

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

This paper proposes using large language models (LLM) to make the decision in a conditional independence (CI) test when four traditional CI tests have inconsistent results, including Chi-square, Fisher's exact test, mutual information, and logistic regression. The authors first generate synthetic directed acyclic graphs (DAGs) and corresponding data. They then apply the four aforementioned CI tests to each CI query and retain instances where the four tests are inconsistent. These inconsistent CI instances are used to post-train a pretrained LLM to predict the final CI decision based on the test outputs and four features extracted from the data. During inference, if the four CI tests have inconsistent results, the four p-values and the features are input into the post-trained LLM, which determines the final CI decision. Finally, the authors analyze the LLM's decision patterns to extract empirical applicability boundaries for the individual CI tests.

Critical strengths
  1. The idea of using LLMs for CI test is novel.

  2. The experiment part is detailed.

  3. The authors provide an interpretable analysis of the LLM's decision patterns to investigate the applicability of different CI tests. The four proposed features could affect the reliability of different CI tests.

Critical weaknesses
  1. The advantage of using an LLM over GBDT is not significant. In Table 1, the F1 improvement is +0.008, while the improvement in Table 3is +0.0212. Such small improvements hardly justify the substantial computational cost and inference time of a LLM. As reported in line 748, post-training the LLM takes approximately 3 hours on 8 NVIDIA A100 GPUs, while evaluating 320 CI instances takes approximately 1.5 hours on 4 NVIDIA T4 GPUs. In contrast, the cost of GBDT on the same tasks is nearly ignorable.

  2. Simpler alternatives, such as p-value aggregation methods, are not considered. Efficient Ensemble Conditional Independence Test Framework for Causal Discovery, ICLR2026 discusses several classical p-value aggregation methods in its Table 1. These p-value aggregation methods could serve as additional baselines.

  3. The four classical CI tests themselves exhibit substantial reliability issues. As shown in Table 11, 54.9% of the unanimous independence verdicts are incorrect, and 34.5% of all unanimous decisions are incorrect. Since the proposed LLM is only used when the four CI tests disagree, it cannot correct errors shared by all four tests. This raises concerns about the reliability of the overall framework.

  4. The proposed method is not a new statistically valid CI test. Instead, it learns to aggregate the outputs of existing CI tests. More importantly, the proposed aggregation does not provide any theoretical guarantee of Type-I error control. The empirical evaluation also does not assess whether the nominal significance level is maintained, which is a fundamental requirement for reliable CI testing.

  5. The experiments only consider four classical CI tests, while several more recent methods applicable to categorical data are not considered. See Conditional independence testing for discrete distributions: Beyond 𝜒2- and G-tests and A Simple Unified Approach to Testing High-Dimensional Conditional Independences for Categorical and Ordinal Data etc.

Questions for authors
  1. Can you transfer this method to CITs on continuous data?

  2. Would like to do some input-feature ablation? E.g. only using four p values / only using four features.

5 comments

We really appreciate reviewer's comments, and here we address each concern. Part 1 of our response:

The gain over GBDT is small (Table 1: +0.008; Table 3: +0.021) and does not justify training and deploying an LLM.

We first add modern baselines UCI and wUCI [1] and take them into the input method library.

MethodSyntheticchildalarminsuranceSachsMean
χ²0.5410.5370.5600.6150.6260.576
Fisher0.6890.6760.6750.6690.6700.676
LR0.5200.4170.5280.4040.1630.407
MI0.6760.6780.6800.6690.6690.674
UCI (new)0.7170.6930.7550.7000.7090.715
wUCI (new)0.7240.6980.7590.6930.7110.717
RLVR0.7460.7210.7460.7400.6930.729
RouterBoundariesPrecisionRecallDirection agreementFalse alarmsGapNullGap/null
GBDT (same inputs)130.4620.20077.8%20%0.1890.2080.91
RLVR170.5880.35383.3%25%0.0960.2360.41

As we can see from the tables, after including more method into library, the advantages of RLVR become larger compare to the most competitive baseline GBDT on both boundary direction and location accuracy.

Furthermore, we would like to emphasize that the advantage of the LLM also lies in its rationales, which make each decision explainable. We extract boundaries from the rationales as follows. For every rationale, we record which of the tests it follows and which it sets aside. We then fit the change-point model of the paper to the set-aside rate of each test along each structural feature. We compare this with the extraction from verdicts used in Table 2. On the 2,368 disagreement instances of the unfiltered pool, the two extractions are complementary. The rationales show the boundary of χ² far more clearly than the verdicts do. The rate at which χ² is set aside rises from 0.62 to 0.91 once the order exceeds 5 (ΔBIC = −216), while its overrule rate rises from 0.08 to 0.16 (ΔBIC = −10). The verdicts show the boundary of MI more clearly, its overrule rate rises from 0.46 to 0.71 once sparsity exceeds 0.3 (ΔBIC = −157), against 0.40 to 0.53 in the rationales (ΔBIC = −29). Three observations follow:

  1. The rationale takes part in the decision. When the trained router is forced to answer without writing its rationale, accuracy falls by 0.020 [0.007, 0.034], with the same sign on all five datasets. The evidence in the rationale can also be checked , all 11,651 p-values cited belong to the test named.
  2. The rationale reflects the applicability boundaries. The router sets χ² aside in the region where its Type-I error rises from 0.050 to 0.109, including on instances where the final decision still agrees with χ². Training sharpens this pattern. For the untrained model the same rate rises from 0.63 to 0.81 (ΔBIC = −55).
  3. The router adapts to a changed test library without retraining. With the three asymptotic tests removed at inference, its accuracy is 0.662, while a GBDT trained on the same inputs falls to 0.593 (difference +0.070 [0.047, 0.094]). When a test never seen in training is added, 96.3% of the rationales use it and accuracy does not decrease. A tabular model has a fixed input layout and cannot do either.

Part 2 of our response:

Classical p-value combination rules are missing as baselines.

We added 5 rules as baselines:

MethodSyntheticchildalarminsuranceSachsMean
Fisher combination0.4660.4650.6040.6260.4950.531
Stouffer0.5350.7340.6810.6670.6880.661
Harmonic mean p0.6250.4190.6120.5950.4740.545
Bonferroni0.7070.4890.6420.6270.5660.606
Cauchy combination0.6780.6920.6980.6620.6940.685
RLVR0.7460.7210.7460.7400.6930.729 (+4.4)
From the table we can see, RLVR still has the highest mean F1, no rules are as unstable as RLVR across datasets.

The procedure is not a valid CI test: no Type-I guarantee and no empirical evaluation at the nominal level.

Here we add type-I error and power for every method on the unfiltered pool:

MethodType-I errorPower
χ²0.069 [0.057, 0.080]0.624
MI0.020 [0.014, 0.026]0.486
LR0.062 [0.052, 0.073]0.468
UCI0.037 [0.028, 0.046]0.559
wUCI0.035 [0.027, 0.044]0.563
RLVR0.038 [0.029, 0.047]0.603 [0.591, 0.614]

As we can see, RLVR holds the nominal level. Two valid tests have nearly the same empirical size, which gives a comparison at matched size. Against wUCI, RLVR's power is higher by 0.040 [0.034, 0.047].

[1] Kim et al. Conditional independence testing for discrete distributions: Beyond chi-2 and G-tests. Electronic Journal of Statistics 2024

Thanks for the rebuttal and extra experiments. My concerns about 1. advantage of RLVR, 2. p-value aggregation methods, and 5. more CIT baselines have been addressed. My concerns about 3. incorrect CITs and 4. lack of theoretical guarantee have been partly addressed by the extra experiments. However, my two questions about 1. same method on continuous CITs and 2. feature ablation remain unanswered, and I strongly request a theoretical guarantee of Type-I error control, although I acknowledge that establishing such a guarantee is indeed challenging.

Reviewer_mK8jOpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
3
Soundness
3
Read review
Paper summary

The paper fine-tunes an LLM to combine the outputs of four classical CI tests: χ2\chi^2, Fisher exact, mutual information, and logistic regression. They then use the LLM to analyze the failure modes of the tests by extracting applicability envelopes and comparing them against changes in test error rates. They compare against other non-LLM classifiers that receive the same numerical inputs as the LLM. They also apply the same approach to causal discovery on the Sachs dataset and report structural metrics.

Critical strengths

None

Critical weaknesses

The paper ignores major advances in CI testing for discrete distributions since the foundational work of Canonne et al. (2018), combining the output of 4 classical tests without comparing them with the modern tests introduced in (Kim et al., 2024) or establishing finite-sample validity of their methodology.

In particular, Kim et al. (2024) introduce practical tests with finite-sample validity that are minimax rate optimal in many scenarios, including the boolean setting of the synthetic experiments in the present paper.

From a theoretical point of view, the current paper provides nothing new. From an applied point of view, its added value remains unclear because it omits the most directly relevant baselines. In particular, the practical value of the applicability envelopes is unclear without checking whether modern CI tests already perform reliably in the identified failure regimes.

If the present LLM approach were instead applied to high-dimensional continuous CI testing instances, I would see greater potential value, as there achieving calibration and power against broad sets of alternatives and null distributions remains a key challenge. For discrete data, the existence of practical tests with strong theoretical guarantees significantly diminishes the motivation of the current paper, unless large empirical evidence over those tests is provided.

The real-world and downstream causal discovery experiments rely on the limited Sachs dataset. Brouillard et al. (2025) discuss the limitations of evaluating against Sachs based on structural metrics, particularly about uncertainty on the graph structure. Please consider additional datasets and graph settings:

  • Canonne et al. Testing Conditional Independence of Discrete Distributions. STOC 2018
  • Kim et al. Conditional independence testing for discrete distributions: Beyond chi-2 and G-tests. Electronic Journal of Statistics 2024
  • Brouillard et al. The Landscape of Causal Discovery Data: Grounding Causal Discovery in Real-World Applications. CLeaR 2025
Questions for authors
  1. How does the proposed test compare against the tests of Kim et al. (2024)?

  2. Please include a deeper discussion on the type I error of the resulting LLM procedure. In particular, what is the type I error of the decisions of the LLM and how does it fair against methods at the same size?

2 comments

We really appreciate reviewer's comments, and here we address each concern:

The paper motivates routing by the failure of four textbook tests, but modern tests with finite-sample guarantees exist for discrete CI. Without them the premise that no single test is reliable everywhere is not established.

We agree modern baselines are valuable, and we implemented UCI and wUCI (Kim et al.). Tables 1 and 2 of the paper are repeated below with the new tests added.

MethodSyntheticchildalarminsuranceSachsMean
χ²0.5410.5370.5600.6150.6260.576
Fisher0.6890.6760.6750.6690.6700.676
LR0.5200.4170.5280.4040.1630.407
MI0.6760.6780.6800.6690.6690.674
UCI (new)0.7170.6930.7550.7000.7090.715
wUCI (new)0.7240.6980.7590.6930.7110.717
RLVR0.7460.7210.7460.7400.6930.729
RouterBoundariesPrecisionRecallDirection agreementFalse alarmsGapNullGap/null
GBDT (same inputs)130.4620.20077.8%20%0.1890.2080.91
RLVR170.5880.35383.3%25%0.0960.2360.41

And we observe:

  1. The modern tests improve on the textbook tests.
  2. Still no single test is the best choice on every dataset.
  3. After adding UCIand wUCI to library, the advantages of RLVR become larger compare to the most competitive baseline GBDT on both boundary direction and location accuracy. Canonne et al. (2018) will be discussed in the related work.

No Type-I error is reported and methods are not compared at the same size. F1 on a balanced disagreement set does not show that the procedure is a usable test.

Here we add both quantities for every method on the unfiltered pool:

MethodType-I errorPower
χ²0.069 [0.057, 0.080]0.624
MI0.020 [0.014, 0.026]0.486
LR0.062 [0.052, 0.073]0.468
UCI0.037 [0.028, 0.046]0.559
wUCI0.035 [0.027, 0.044]0.563
RLVR0.038 [0.029, 0.047]0.603 [0.591, 0.614]

As we can see, RLVR holds the nominal level. Two valid tests have nearly the same empirical size, which gives a comparison at matched size. Against wUCI, RLVR's power is higher by 0.040 [0.034, 0.047].

Sachs is the only real dataset, and structural metrics on Sachs have been criticised (Brouillard et al., 2025).

We agree with this critique of Sachs dataset. We would like to argue that the evidence beyond synthetic DAGs also rests on the three expert networks (child, alarm, insurance). Their structures, cardinalities and conditional probability tables come from the application domain. The data are sampled from the networks, so every independence label is an exact d-separation statement. This is the property that the critique finds missing in Sachs, where the reference graph is itself uncertain. For evaluating a CI test, an exact label matters more than the provenance of the samples, because an error in the reference graph is counted as an error of the test. The three networks contribute 856 evaluation instances with real variable names.

The learned router has no finite-sample guarantee, unlike the tests it is compared with.

We agree that theoretically, the router doesn't carriy finite-sample guarantee, so we measured the level of the whole pipeline directly. As shown in previous table, on the 8,000 unfiltered queries, its Type-I error is 0.038 [0.029, 0.047], which is significantly below 0.05.

It is unclear who would use this.

The default discrete CI tests in pcalg, bnlearn and causal-learn are asymptotic χ² and G² tests. Constraint-based discovery reaches conditioning sets of size 6 and 7, and our measurements show what these defaults cost there. Meanwhile, LLM will not only output verdict but also the rationale of decision. This will provide explainability that classical methods don't have.

The more interesting setting is high-dimensional or continuous data, where test choice matters more.

Indeed, our experiment results shows promising on high-dimensional discrete data. Since continuous data requires completely different sets of methods and training, we will treat it as the future direction.

I thank the Authors for the their replies, their rebuttals and extra experiments. I have read all of the reviews and replies. While I find that the additional material improved the paper's indicated weaknesses, I remain unconvinced about the practical significance and impact of the work in its current form. Therefore, I raise my score to 2, still leaning towards reject.

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

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