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Under review as a conference paper at ICLR 2027

Large Language Models as Proxy Designers for Proximal Causal Inference

Abstract

Proximal causal inference (PCI) identifies causal effects under unmeasured confounding using two proxies for the latent confounder: a treatment control and an outcome control . Its practical bottleneck is the step before estimation, namely partitioning the covariates into , and observed confounders so that the identification conditions hold, a judgment that needs fluency in both PCI and the application domain. We show that large language models (LLMs) are increasingly capable of making this judgment. From the PCI conditions, a brief study context, and a description of each covariate, an LLM proposes what the latent confounder represents and assigns every covariate a role; a stratum-targeted outcome-bridge objective then yields conditional effects from one global bridge. We evaluate on three real cohorts with external checks. On a 10M-sample food-delivery corpus with a separate randomized price experiment, three LLM partitions give – error (relative to the randomized experiment), two of these are below and one is tied with the best baseline. In the Framingham Offspring study, every LLM partition that admits an estimate lands inside the range randomized trials report, where a third of random partitions and the published proximal split do not. In the SUPPORT study, all eight LLMs give estimates within the published confidence intervals and one reproduces the expert allocation exactly. For the (cardiovascular) Framingham and SUPPORT datasets, we also compare LLM covariate partitions to those from multiple Board-certified cardiologists.

Primary area:
causal reasoning
Keywords:
large language models, proximal causal inference, PCI

Reviews

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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_m6A9OpenReview ↗
Rating
2
Confidence
3
Informativeness
3
Presentation
2
Soundness
2
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Paper summary

This paper studies whether LLMs can assign covariates to the roles required by proximal causal inference (PCI): treatment proxies (Z), outcome proxies (W), observed confounders (X), or discarded variables (D). Given the PCI assumptions, study context, and variable descriptions, an LLM infers the latent confounder and proposes a partition, while the downstream bridge estimator is held fixed. The paper also introduces stratum-balanced bridge training to estimate conditional effects across observed strata. Experiments cover SUPPORT, Framingham Offspring, and a 10-million-sample food-delivery dataset evaluated against a separate randomized price experiment.

Critical strengths

The presentation of this paper is clear and easy to understand. The experiments are comprehensive by incorporating the randomized price experiment.

Critical weaknesses

The paper does not clarify how semantic plausibility from variable descriptions translates into PCI-valid proxy roles. In specific, A2/A3 require conditional independence given latent, and A4 requires completeness. Moreover, Framingham is relatively insensitive to proxy reassignment once is fixed, leaving the added value over general confounder identification unclear.

Questions for authors

Given A2–A4, how do the authors distinguish an LLM’s semantically plausible inference about (U) from evidence that the selected (Z/W) satisfy the identification conditions? What criterion can validate a partition beyond the plausibility of its causal explanation?

1 comment

We thank the reviewer for a thoughtful review that goes to the paper's central question. How plausibility relates to the identification conditions is the right question, and we try to answer it directly.

What cannot be verified. A2 and A3 are conditional independences given the latent U, and A4 is a completeness condition on the same latent variable; none is testable from observed data in general. This is the proximal counterpart of the untestability of ignorability, and it applies equally to every source of a partition: to the expert who supplied the SUPPORT allocation, to an association rule, and to a language model. So, to the reviewer's direct question, we know of no criterion that certifies a partition, and we will say this explicitly in Section 3 and the limitations. The paper's design follows from accepting it. The partition's only observable consequence is the estimate, so we hold the estimator fixed and judge each partition by whether its estimate agrees with a reference the model never saw: published confidence intervals on SUPPORT, a range bracketed by randomised trials on Framingham, and a separate randomised experiment on the waybill corpus. Random and perturbed partitions through the same pipeline show how far a wrong partition can move the estimate, so agreement with the reference is informative rather than automatic.

What can be checked. Two necessary conditions are testable from data: Z must carry information about U, which appears as first-stage strength, and Z and W must be dependent given X, since both are driven by U. These can rule a proxy out but cannot rule it in, and they cannot tell dependence through U from a direct channel between Z and W. The pH and PaCO2 case in Section 5.1 shows the limit: a first-stage F of about 1,100 says the two are tightly bound, but whether the binding runs through U or through the Henderson-Hasselbalch identity is a question of chemistry, not of the data, which is why the paper reports the models' reasoning on that pair alongside the statistic. We will state both checks and their limit in the revision.

Beyond plausibility. Four observations bear on whether the models do more than produce a plausible story. First, Section 5.3: a judgment based on influence cannot produce a treatment proxy, because a valid Z does influence the outcome through U, and the six cardiologists left that role empty on both cohorts. Every admissible LLM vote fills it, with reasoning of the form A3 requires, no direct path to Y once U is fixed; the one vote with an empty Z (Claude Haiku 4.5 on Framingham) is reported as a completeness failure. This is evidence about the kind of reasoning, not that A3 holds. Second, Section 5.1: six of eight arms move arterial pH from the published W side to Z beside PaCO2, treating the two as readings of one acid-base state that should not sit on opposite sides; arms raise the Henderson-Hasselbalch relation unprompted, and Claude Opus 5, which keeps the published allocation, argues that given U the coupling is loose enough for pH to remain in W (Appendix A). The arms disagree about this pair, but about the right thing: the independence of Z and W given U and X, a condition on the pair (A3b in the prompt, part of A2 in Section 3), not the plausibility of either variable alone. Third, Appendix C.3: on SUPPORT, exchanging Z and W moves six of the eight allocations by 0.3 to 1.7 days, so the side matters on this cohort, and the models' choices keep all eight arms inside the published confidence intervals. Fourth, memorisation does not explain the Opus match: with variable names replaced by shuffled codes and the study's name and counts removed, Claude Opus 5 still returns the published allocation in all five replicates.

Framingham. We agree, and the paper reaches the same conclusion, though it buries it: with each partition's X held fixed, 27 of 30 random reassignments of the proxies stay in the trial range (Appendix C.2), so on this cohort the models' contribution is the choice of observed confounders, and the proximal step adds only a modest shift toward the HOPE-3 value of 0.75: the overlap-weighted Cox fit with all sixteen variables and no proxies gives 0.90, the LLM partitions 0.76 to 0.89. We will say so at the start of Section 5.2 and in the abstract. The proxy-specific evidence rests on SUPPORT and the waybill corpus, where the three treatment-proxy sets are disjoint and the size of the correction differs with them (Table 7). What Framingham does show is that the confounder decision is load-bearing: dropping four of an arm's chosen confounders moves the median hazard ratio to 0.94 with 9 of 20 perturbed partitions in range (Table 10).

The reviewer's distinction between a plausible account of U and evidence that the conditions hold is the one the revision should draw, and we will restructure Section 3 around it.

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

The paper presents an application of modern LLMs to a well-known causal inference problem, proximal causal inference (PCI). The main claimed contribution is that LLMs can partition the covariates into treatment proxies, outcome proxies and observed confounders. This step is argued to have so far required an expert in both the identification conditions and the domain. To validate it, the authors conduct a survey of cardiologists. They show that domain experts without PCI training cannot do this step, in particular for treatment proxies. So, arguing that LLMs are ideal choice here. The second claimed contribution is a stratum-balanced loss for training the bridge function. The claims are evaluated on two public datasets without ground truth (SUPPORT and Framingham), where the LLM partitions are compared with published allocations, random partitions and an association-based split. They are also evaluated on a large private dataset with a randomized experiment as ground truth, where PCI with the LLM partitions is compared with IPW, S-Learner and DML. The paper concludes that LLMs can perform the partition step, and that stratum-balanced training improves the population estimate.

Critical strengths
  1. The paper addresses a question in a timely manner. As LLMs' capability in mathematics increases, can we argue something similar about causality? In other words, whether current LLMs can perform a step of causal inference that usually requires expert knowledge. It evaluates a range of models under the same estimator, which gives a useful picture of their current capability.

  2. The evaluation on a large private dataset with a separate randomized experiment is the most informative part of the paper. It provides ground truth, which is rare in causal inference, and since the data is private, memorization is not a concern there.

Critical weaknesses
  1. The paper’s main weakness is that it has limited novelty and makes overstated claims. The core contribution is applying existing LLMs to the partition step of an existing problem, and then using an existing estimator. The paper does not propose a new framework or method for how LLMs should do this step; it mainly shows that current models can produce reasonable partitions in a few settings. Without a clear methodological contribution, the novelty depends on how strong and general the empirical evidence is, and in my opinion the evidence does not support claims such as that modern LLMs can do proxy design for PCI, or that PCI is validated on a large real-world dataset. The comparisons are also not strong enough to support these claims. On the public datasets, the LLM partitions are mainly compared with random partitions, which give similar median estimates, and a stronger baseline, such as standard confounder selection with association-based proxies, is missing. On the private dataset, the baselines neither use proxies nor stratum reweighting, so it is not clear how much of the gain comes from the LLM partitions. The stratum-balanced loss, presented as the second contribution, is also an application of existing reweighting ideas and is only evaluated against a global loss on one dataset.

  2. The paper is not clearly written, and the story is hard to follow. The setting is not properly introduced. It is not explained what treatment and outcome proxies are, why they work, or why finding them is hard, although this is the essence of the paper. Examples of LLMs' reasoning and results would be significantly helpful. The results are mostly reported rather than interpreted, so the takeaway of each experiment is often unclear. Positive and negative results are also not discussed consistently. For example, on the private dataset, the ATE result is presented as a clear win, while the worse CATE result is attributed to the noise of the experiment, although the same reasoning is not applied to the ATE result. And on Framingham, the finding that the gain comes from confounder selection rather than proxy assignment is not connected back to the main claim. The paper would benefit significantly from being written as a coherent story, with the setting defined first and the implications of each result discussed.

  3. In addition, the paper discusses the variation across prompts and seeds but not the statistical uncertainty of the estimates.

Questions for authors
  1. On the private dataset, the method is better on ATE but worse on avg-CATE. Since errors can cancel out when averaging, could the ATE improvement come from lower variance at the cost of bias in the stratum-level effects? What in the results rules this out?

  2. The paper suggests that this capability is new with recent models, but older models (e.g., GPT-4 Turbo, and the models used on the private dataset) also give reasonable results. Could you clarify which results support the claim that only recent models can do this step?

  3. Could you compare against a stronger baseline than random assignment, for example, one where the confounders are selected by the LLM or a standard selection method and the proxies are assigned by association? Given the Framingham analysis, this would show what the LLM adds specifically for proxy assignment.

  4. Could the stratum-balanced loss be applied to the baselines as well, so that its effect can be separated from the effect of the LLM partitions? Or is this even possible? If not, it is fine.

2 comments

We thank the reviewer for a careful and constructive review. We take the weaknesses first and then the questions; Q3 is answered with the baseline point and Q4 with the waybill point.

On novelty and the claims. We agree that two phrases overstate what the experiments show: "increasingly capable" in the abstract and "PCI validated on a large real-world dataset" in the second contribution. Both will go, and we will say from the start that this is an empirical study built around a control design rather than a new method, with the estimator of Meng et al. (2025) held fixed. We would push back gently on the question itself. The proximal literature takes the Z/W/X partition as given and does not ask how to obtain it. To our knowledge no prior work asks an LLM to supply it, and none we know of has checked a proximal analysis against a randomised experiment at this scale. Six board-certified cardiologists briefed on the conditions could not do it, and their influence-based placements leave the treatment-proxy role empty on both cohorts (Section 5.3). Whether a language model can fill that role seemed worth answering, and the paper's contribution is a design for doing so: eight models, three cohorts with external references, and five kinds of control.

On a stronger baseline, and Q3. We agree that random partitions are a weak comparison. The association-based split of Meng et al. (2025) gives 0.91 through the same pipeline, and the overlap-weighted Cox fit of the source analysis, with all sixteen variables and no proxies, gives 0.90, against 0.76 to 0.89 for the LLM partitions (Table 2). The difference is modest, and it is one cohort. Appendix C.2 keeps each LLM partition's X and reassigns the proxies at random: thirty draws give 0.75 to 0.94, 27 in range. These belong side by side in Section 5.2, and we should have put them there. The exact control the reviewer asks for, LLM-chosen X with association-assigned proxies, is not in the paper; the X-fixed control is the closest we have, and on SUPPORT, where proxy assignment matters, there is no association-based allocation to compare. So on Framingham the model's contribution is confounder selection, as the reviewer says; we will say so in the abstract and at the head of Section 5.2. On SUPPORT, with the 43 non-panel covariates always in X, exchanging Z and W moves six of eight allocations by 0.3 to 1.7 days, while all eight arms stay inside the published intervals (Appendix C.3).

On the gain on the waybill, and Q4. The last row of Table 4 separates the two factors; Section 5.4 draws the conclusion in one sentence, which we will make prominent. Under the global loss (4) the Opus partition's median error is 16.0% over five runs, already below the best ignorability baseline at 21.1%, though two runs exceed 20%. The balanced loss brings the median to 12.0% and leaves one run in fifteen above 20%. The two contribute about equally, and with the balanced objective the Opus partition beats the best baseline in all ten seeds (Table 7). Reweighting the baselines would be the clean test; we no longer have access to the corpus, and will say so in Section 5.4.

On ATE versus CATE. Section 5.4 gives the noise floor at both levels, but we agree the reading is one-sided: we used it to say the Opus partition cannot be improved on at the population level, and to set aside a worse result within tiers. We will present both the same way. An exact estimator would still score about 12% at the population level, where the Opus partition sits, and about 31% on average within city tiers, where all methods lie between 34% and 42%, so none is distinguishable there, and the Opus partition is 3.2 points behind DML.

On statistical uncertainty. The reviewer is right. The intervals in Tables 1, 2 and 4 are ranges over runs, seeds or partitions, not sampling uncertainty. We will label every interval for what it is and note the limitation.

On Q1. We cannot rule it out, but Table 7 argues against it. The baselines understate the effect, with slopes of 0.68 to 0.80 against the experiment, the direction confounding predicts. The Opus partition gives 0.95 (0.84 to 1.01 over ten seeds) and is closer to one than every baseline in four of the five city tiers. Errors cancelling at the population level would not be expected to come with better calibration within most strata, so this looks like a correction in one direction, though it is not conclusive.

On Q2. No result supports the claim that only recent models can do this; we will withdraw it. Newer models are more self-consistent (pairwise agreement 0.86 against 0.64 on Framingham, Appendix B), but GPT-4 Turbo does well, and the two completeness failures on Framingham are one newer model and one older (Table 5). Capability shows up as reliability, not as a threshold.

On writing. We will define proxies and explain why treatment proxies are hard to find in Section 1, add a worked example to Section 4, and end each experiment with its takeaway.

Thank you for your responses to my concerns. I appreciate the honesty and acknowledgement.

In terms of writing, softening the claims, as acknowledged, or discussing the good and bad results equally would be the easiest part to change, and it would improve the paper's written quality. However, the paper's coherence, how it identifies gaps in the literature and what novelty it provides requires more significant changes in the writing. I don't see how it can be done eloquently before the camera-ready deadline or how it can be approved by a third party. Hence, I will keep my score for presentation.

In my comments, I mentioned that for such a paper, quality depends on the empirical results. In the rebuttal, the authors highlighted the part that supports the main claim more clearly. Based on the comments, I will improve my score on informativeness and keep the soundness.

Reviewer_ZGFfOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper is on causal effect estimation under unmeasured confounding with proxies. The paper proposes to use LLMs to split the covariates into Z, W and observed confounders X so that the identification conditions hold. The proposed method employs LLMs to analyze a brief study context and a description of each covariate, and then decide the role of each variables. The experiments are right heart catheterisation and Framingham Offspring.

Critical strengths
  • The paper investigates the proxy design ability for PCI setting. It explains how LLMs could infer a form for the latent confounder and partitions the covariates into Z, W and X.
  • The experiment with 10M-sample food-delivery corpus demonstrates the performance of the proposed method.
Critical weaknesses
  • In section 3, the paper presents some theoretical analysis. It is unclear to readers: how these theories are used in the proxy selection process. It looks like a background introduction instead of a part of proposed method. Is there any new theoretical challenges, like identification, need to be established in proxy designing with LLMs?
  • In section 4, it lacks details on the proxy selection process.
  • In section 5, how well the LLM could do during each proxy selection step? The evaluation setting is not clear. For example, the baselines and the metrics.
Questions for authors

Please see the weakness part.

1 comment

We thank the reviewer for the clear summary and for pointing to three places where the paper does not explain itself. We take each in turn and set out how we would address it in the text.

On the role of Section 3. We agree that as written it reads as background. It has two roles that the text does not make explicit. The first is that the DAG of Figure 1 and conditions equivalent to A1 to A4, posed as per-variable checks, are the task specification given to the language model. The model is not asked to label variables by intuition. It is asked to state what the latent confounder U represents and then, for each covariate, to argue whether placing it in Z would violate A3, whether placing it in W would violate A2, or whether it has a channel to treatment and outcome of its own and belongs in X. The excerpts in Appendix A show this reasoning, including arguments about the chemical dependence between candidate proxies that bear directly on the independence the conditions require. Section 3 is therefore the specification of the task, and we will retitle and introduce it as such. The second role is Proposition 1, the only new statement in the section: once the bridge is fitted, the effect within any stratum of the observed covariates follows from the same bridge with no second inverse problem, which is what Section 5.4 uses to report effects by city tier.

On whether new identification theory is needed. We do not think proxy design with LLMs raises a new identification question, and we should have said so directly. Identification rests on the partition satisfying A2 to A4, whoever supplies the partition, whether an expert, an association rule, or a model. Whether a given partition satisfies them is not testable from observed data in general, the proximal counterpart of the untestability of ignorability. That is why the paper evaluates empirically against external references rather than attempting a guarantee, and we will state this in Section 3 and in the limitations.

On the proxy selection process. Section 4 is too compressed, and we will expand it with a worked example. The model receives the treatment and outcome definitions, a short study context, a name and short description for each covariate, and the DAG and conditions of Section 3 restated as per-variable checks; it is never told what U is, and no variable's role is suggested. It first states its inferred U, then reasons about each covariate individually, and finally returns a JSON partition into Z, W, X and discarded variables. The decision order is fixed in the prompt: a covariate is X if it has direct paths to both treatment and outcome not fully mediated by U; otherwise Z if it reflects U, predicts treatment and satisfies A3; otherwise W if it reflects U, predicts the outcome and satisfies A2; otherwise discarded. Each model is called five times with the vendor's default decoding, and the partition credited to it is the per-variable majority vote. A vote with an empty Z or W violates completeness and carries no estimate, and we report such cases rather than drop them. The estimator and its hyperparameters are identical across arms, so the only thing that changes between the rows of any table is the partition.

On the evaluation setting. We agree it is not laid out in one place, and we will add a summary table at the start of Section 5. On SUPPORT the reference is the expert allocation of Tchetgen Tchetgen et al. (2020) together with three published confidence intervals for the effect; the controls are thirty random allocations and the exchange of Z and W. On Framingham the reference is a range of 0.70 to 0.90 bracketed by randomised trials of statins; the controls are uniform random partitions, size-matched random partitions, the association-based split of Meng et al. (2025), an X-fixed control that randomises only the proxies, and a perturbation control that removes confounders. On the waybill corpus the reference is a separate randomised price experiment, the metric is the relative error of the estimated dose-response curve against it, and the baselines are IPW, an S-Learner and DML, each given more covariates than any bridge. Per step, inferring U is reported qualitatively: on the waybill all three models read U as zone-level supply-demand tension, and the excerpted clinical responses in Appendix A give the same reading within each cohort. The partition is compared with the expert allocation on SUPPORT, where Claude Opus 5 reproduces it on all ten variables, scored by self-consistency across replicates on both cohorts (Table 5), and compared with six cardiologists' influence-based placements in Section 5.3 (Table 3). The estimate is scored as above.

We hope these clarifications make the paper easier to read as a whole, and we are grateful for the prompt to reorganise it.

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

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