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Under review as a conference paper at ICLR 2027

Hidden Confounding Can Make CATE Validation Look Better as Causal Error Grows

Abstract

Because counterfactual outcomes are unavailable in observational data, conditional average treatment-effect (CATE) estimators are commonly developed and selected using observable held-out losses. A loss can rank candidates well without revealing whether any candidate remains causally accurate as the deployment environment changes. We uncover a systematic directional failure under hidden confounding: as confounding strengthens, causal error (oracle CATE root-PEHE) rises while held-out R-loss and a doubly robust pseudo-outcome loss improve. A population construction explains the direction: under hidden confounding, both losses reward movement toward the observed treated–untreated outcome difference rather than the CATE. Guided by this mechanism, we audit 24 structurally varied environments. Eight estimators spanning classical meta-learners, forests, orthogonal methods, and neural architectures exhibit this validation reversal in more than 92% of paired severity comparisons. Observable validation can still select a near-oracle-best member even as the best attainable CATE accuracy of the entire candidate pool deteriorates. We therefore propose severity-path validation audits as a new evaluation framework for causal-estimator development: developers should test whether observable model-selection criteria remain aligned with oracle causal accuracy as identification is progressively stressed.

Primary area:
causal reasoning
Keywords:
Causal inference, heterogeneous treatment effects, model selection, validation metrics, hidden confounding, overlap violations, robustness evaluation

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Reviewer_4usxOpenReview ↗
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Paper summary

This paper discusses whether commonly used R-loss and doubly robust loss for conditional average treatment effect (CATE) remain reliable under hidden confounding. The authors construct an example to demonstrate that as hidden confounding strengthens, the population minimizers of R-loss and DR loss become biased with respect to the true CATE, while the validation losses decrease. They also validate this phenomenon with synthetic experiments.

Critical strengths
  1. This paper explicitly constructs an example to demonstrate that hidden confounding can make CATE validation look better as causal error grows.

  2. The extensive experiments validate the theoretical observation across eight different CATE estimators and 24 synthetic environments, suggesting that the phenomenon is not specific to a particular estimator or data-generating process.

Critical weaknesses

1.The main finding is not entirely unexpected. Under unobserved confounding, the standard identification formula for CATE becomes invalid. Since both R-loss and DR-loss rely on the observed-data distribution, it is natural that they may favor an associational target rather than the true causal effect. A closely related omitted-variable-bias mechanism has already been extensively studied in [1]. Although the paper demonstrates the more specific phenomenon that validation loss can decrease as causal error increases, it is unclear how much additional theoretical insight this construction provides beyond existing omitted-variable-bias theory.

  1. In real observational studies, neither the unobserved confounders nor the true treatment effects are typically available. Consequently, it is unclear how practitioners could implement the proposed framework on real datasets. The paper would benefit from more concrete guidance on how to diagnose in practice.

[1] Chernozhukov, V., Cinelli, C., Newey, W., Sharma, A., and Syrgkanis, V. (2022). Long Story Short: Omitted Variable Bias in Causal Machine Learning. NBER Working Paper No. 30302. https://arxiv.org/abs/2112.13398

Questions for authors

Please see the weakness section.

4 comments
AuthorsOpenReview ↗

What the criterion-level results add beyond omitted-variable bias, and what practitioners can do

We thank the reviewer for recognizing the paper’s soundness and empirical breadth. We have uploaded a revised paper and supplementary ZIP that incorporate the new items summarized below. The revision clarifies that our contribution is not the existence of hidden-confounding bias, but that standard validation criteria can systematically reward it.

1. What is added beyond omitted-variable-bias theory?

Chernozhukov et al. bound omitted-variable bias for average causal parameters using the extent to which a latent variable explains treatment and outcome. Our complementary question is criterion-level: once hidden confounding displaces the causal target, what feedback does a held-out CATE validation loss provide?

Let τ(x)\tau(x) denote the CATE, gR(x)g_R(x) the observed treated–untreated conditional outcome difference, and B(x)=gR(x)−τ(x)B(x)=g_R(x)-\tau(x). Revised Section 3 and Appendix A establish

LR(τ)−LR(gR)=E[e(X)(1−e(X))B(X)2]L_R(\tau)-L_R(g_R)=E[e(X)(1-e(X))B(X)^2]

and

LDR(τ)−LDR(gR)=E[B(X)2]L_{DR}(\tau)-L_{DR}(g_R)=E[B(X)^2].

Thus omitted-variable bias becomes a validation advantage: whenever B≠0B\neq0, both criteria prefer the confounded observational target to the true CATE. They share that target but impose different geometries—propensity-weighted for R-loss and unweighted for DR loss.

The result extends beyond the balanced illustrative construction. For an additive latent outcome model and arbitrary propensity, Appendix A shows that, along paths holding the outcome model and distribution of (X,U)(X,U) fixed, the R-loss of the true CATE is invariant to the assignment mechanism. The attainable loss equals that constant minus E[e(1−e)B2]E[e(1-e)B^2]. Each unit of overlap-weighted squared bias is therefore one unit of apparent validation improvement.

These identities are short consequences of the standard R-loss decomposition; our claim is that their criterion-level consequence, to our knowledge, had not been articulated and tested as a validation failure. Omitted-variable-bias theory also does not address the distinction between relative selection and absolute monitoring. In our base families, selection regret remains only .006.006–.013.013, while the oracle-best candidate’s root-PEHE rises by approximately 1.051.05. A criterion can therefore select a near-best member of its pool while providing increasingly favorable feedback about a pool whose absolute causal accuracy is deteriorating.

The experiments establish that this mechanism appears at practical sample sizes with estimated nuisances, regularization, and heterogeneous learners. Across four EconML and four neural estimators, reversal occurs in 92–100% of paired hidden-confounding comparisons. Mechanistic controls in the EconML pool further show that systematic reversal disappears when either U→TU\to T or U→YU\to Y is absent. Under unconfounded sample-size degradation, causal error and both losses instead rise together.

We revised Section 2 to position Chernozhukov et al. as complementary sensitivity analysis. The introduction and Section 3 now credit the standard decomposition while identifying the criterion-gap, assignment-path, and selector-versus-monitor results as our contribution.

2. What can practitioners and model developers do?

We agree that one observational dataset cannot reveal its hidden confounders or oracle CATE. The proposed audit is therefore not a post hoc detector certifying that an estimate is unconfounded. Proposition 1 explains why: both losses are minimized by the observed conditional outcome contrast, so the losses alone cannot distinguish it from the CATE without additional structure such as credible proxies, negative controls, or sensitivity assumptions.

There is nevertheless an immediate practical implication: a lower held-out R-loss or DR loss across sites, time periods, or model revisions is not by itself evidence of improved causal accuracy. It can accompany causal deterioration when the identification environment changes.

The severity-path audit is primarily a development-time protocol:

  1. Use subject-matter knowledge to posit an omitted variable, proxy failure, or missing assignment link.
  2. Calibrate its strength through partial outcome variance, incremental treatment-prediction strength, proxy reliability, or established sensitivity parameters.
  3. Construct simulation or semi-synthetic paths anchored at an identified baseline.
  4. Track validation loss together with selected and oracle-best causal error.
  5. Include arrow-removal and non-confounding degradation controls to verify the mechanism.

The path can also support model development. An exposed failure mode defines a synthetic task family that could augment pretraining for a prior-fitted causal estimator such as CausalPFN; we leave this audit-guided adaptation to future work. For applied analyses without oracle outcomes, sensitivity analysis remains necessary. Our audit instead tests whether validation remains aligned with causal accuracy under plausible violations. Section 6 gives its scope, calibration anchors, and controls.

The clarification that the proposed audit is intended for development-time evaluation is helpful. However, in simulator-based evaluations where the true CATE is available, researchers can already assess estimator performance directly using the oracle group-truth CATE. I still have the following questions:

  1. Why is it meaningful to compare the numerical values of validation losses across different data-generating distributions? R-loss and DR loss are primarily designed to compare estimators under a fixed distribution. Their absolute values depend on distribution-specific quantities, including conditional outcome variance and propensity scores. Consequently, it is not clear why decreasing validation loss across different distributions should be interpreted as improving causal estimation accuracy in the first place.

  2. If the goal is to study robustness to hidden confounding, why not directly measure the sensitivity of each estimator's causal error to confounding severity? In the authors' simulation framework, the true CATE is available. They could evaluate how rapidly each estimator's PEHE deteriorates as confounding increases, and compare the resulting sensitivity curves. This seems more directly informative about robustness than comparing absolute validation losses across distributions.

AuthorsOpenReview ↗

Why is it meaningful to compare the numerical values of validation losses across different data-generating distributions?

Comparing validation losses along a controlled shift tells us what feedback practitioners would receive as causal accuracy changes. Consider a hospital that refits a CATE estimator after new clinicians begin relying more on an unrecorded frailty assessment when assigning treatment. The team can observe the held-out loss but cannot observe the true treatment effects. A falling loss could reassure them just when there is reason to revisit their assumptions about treatment assignment.

We simulate this scenario by strengthening the influence of an unobserved factor on treatment assignment while holding covariates and potential outcomes fixed. Across 24 structurally varied environments, the pattern appears at intermediate severities as well as at the endpoints. As suggested, we track each estimator’s oracle root-PEHE to measure how much accuracy it loses. Tracking R-loss and DR loss alongside it shows whether the observable feedback reflects that deterioration. Chernozhukov et al. bound the omitted-variable bias, leaving open the direction of validation losses. That direction matters in the hospital example because falling R-loss or DR loss could reassure clinicians even as CATE estimates worsen.

On your second question, we use oracle root-PEHE to measure robustness in simulation, and the hospital example illustrates why we also track validation loss in settings where practitioners cannot compute PEHE because the true CATE is unknown.

AuthorsOpenReview ↗

Regarding "Consequently, it is not clear why decreasing validation loss across different distributions should be interpreted as improving causal estimation accuracy in the first place.

We agree that a decrease in loss alone does not establish an improvement in causal accuracy. Your question prompted a related check. Can the validation loss at baseline help identify which estimator will be most accurate after confounding increases?

Within each pool and simulated environment, we compared the estimator with the lowest mean validation loss at severity zero with the estimator with the lowest mean root-PEHE at severity one, averaging over 20 seeds. The two matched in 91.7% of EconML environments (22/24) but only in 66.7% of neural environments (16/24). The counts were the same for R-loss and DR loss.

These results suggest that baseline validation can help choose among candidates under a specified shift, even when a subsequent decrease in loss gives misleading feedback about whether their causal accuracy improved. Future work could test whether baseline scores reliably guide that choice across other shifts. Understanding the gap we observed between the EconML and neural pools could also shed light on which modeling and training choices help baseline scores remain informative as hidden confounding increases.

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

The paper studies how observable CATE validation losses behave as hidden confounding increases. A population construction and synthetic experiments show that R-loss and DR pseudo-outcome loss can decrease while causal error increases, even when model selection remains competitive within the candidate pool. The paper proposes paired severity-path audits to expose this distinction.

Critical strengths

The distinction between relative selection quality and absolute causal accuracy is useful and clearly demonstrated. The population calculation supports the claimed example. Independent selection and monitoring splits, paired seeds, multiple estimator classes, and nuisance and score-scale controls strengthen the empirical evidence.

Critical weaknesses

The scope of the empirical breadth claim needs care: despite varying 24 environments, the experiments retain an additive latent outcome contribution and treatment effects that do not depend on the hidden variable (Section 4.1; Appendix D). The reported reversal frequency therefore describes this tested family rather than hidden confounding generally. The value of the proposed audit also depends on choosing scientifically plausible severity paths, for which practical guidance remains limited.

The incremental contribution could be positioned more precisely against existing surrogate-risk and oracle-selection results. This does not invalidate the observed reversal, but matters to assessing its novelty.

Questions for authors
  1. Can you clarify when reversal might disappear, particularly if the hidden variable also modifies treatment effects?
  2. What should guide the choice and calibration of a severity path for the audit's intended development setting?
  3. How does the audit extend the perspectives in Doutreligne and Varoquaux (2025) on surrogate risks and Lan and Syrgkanis (2024) on relative oracle selection guarantees? These papers address different questions and assumptions; neither is being claimed to establish the same severity-path result.
1 comment
AuthorsOpenReview ↗

When reversal disappears, how to calibrate a severity path, and relation to prior selection results

We thank the reviewer for the positive assessment and for identifying where the scope and positioning could be sharper. The uploaded revision incorporates the analyses below, but we summarize them here so the response is self-contained.

1. When does reversal disappear?

We added an effect-modification experiment:

Y(1)−Y(0)=τk(X)+κhk(U),κ∈{0,.25,.5,1},Y(1)-Y(0)=\tau_k(X)+\kappa h_k(U),\qquad \kappa\in\{0,.25,.5,1\},

with hk(U)h_k(U) conditionally centered so that the CATE remains τk(X)\tau_k(X). Across 24 environments and 20 paired seeds per environment, reversal attenuates as effect modification strengthens but remains widespread:

κ\kappaR-loss reversalDR-loss reversal
099.0%95.8%
.2597.5%95.0%
.593.5%93.8%
186.0%89.2%

The theoretical decomposition provides the boundary condition: neither criterion can favor a confounding-biased target when the observational displacement B=gR−τB=g_R-\tau is zero. This occurs when either latent arrow is absent. With U→TU \to T but no U→YU \to Y, root-PEHE and R-loss are essentially unchanged (−.004-.004 and −.001-.001). With U→YU \to Y but T⊥U∣XT\perp U\mid X, root-PEHE changes by +.061+.061, while R-loss and DR loss increase by +1.769+1.769 and +7.554+7.554; reversal occurs in 0% of pairs. Under effect modification, reversal may disappear if selection on the effect-modifying component offsets selection on the additive latent-outcome component. Our sweep through κ=1\kappa=1 attenuates the phenomenon but does not reach that case.

An additional unconfounded sample-size stress makes causal error and both losses rise together. These controls establish that reversal is not a generic consequence of latent outcome variation or a harder estimation problem. It arises from treatment selection on outcome-relevant latent variation. We now describe the empirical claim accordingly: it holds broadly across the tested latent-confounding families, rather than for hidden confounding generally.

2. Choosing and calibrating a severity path

A useful path should encode a scientifically plausible identification threat. Our recommended protocol is:

  1. Identify the omitted variable, proxy failure, or assignment link to stress using domain knowledge.
  2. Anchor severity zero at a process satisfying the relevant identifying assumption.
  3. Calibrate the upper endpoint through interpretable quantities such as partial outcome variance, incremental treatment-prediction strength, proxy reliability, or parameters from an established sensitivity model.
  4. Reuse the same exogenous draws across severities and vary one causal mechanism at a time.
  5. Include arrow-removal and non-confounding degradation controls to verify the proposed mechanism.

This is a benchmark-development audit: simulation or semi-synthetic models supply oracle effects, allowing researchers to test an observable criterion before using it to guide development on real observational data. Section 6 gives the calibration anchors and accompanying controls; the valid severity-zero baseline and paired-draw construction are specified in Section 4.2.

3. Relation to prior work

Doutreligne and Varoquaux study how observable surrogate risks rank causal estimators. Lan and Syrgkanis establish relative oracle guarantees for selecting or aggregating candidates. Both address an important relative question: how close is the selected candidate to the best candidate available in the pool?

Our audit asks a complementary absolute question: as identification weakens, does the observable score remain aligned with causal accuracy, and does the best candidate in the pool remain accurate? In the base families, within-pool selection regret remains only .006.006–.013.013, yet oracle-best root-PEHE rises by approximately 1.051.05 while the observable validation losses improve. Low within-pool regret can therefore coexist with a pool that has moved away from the causal target. Lan and Syrgkanis’ guarantees are stated under identification, which our severity path deliberately relaxes.

The revision now makes this distinction explicit in Section 2 and credits the standard surrogate-risk geometry. It additionally derives criterion-level gap identities (Eq. 5) showing how movement toward the confounded observational target is rewarded. The broader contribution is the severity-path audit and its joint tracking of three trajectories: observable validation score, selected causal error, and oracle-best causal error.

Reviewer_Q6o6OpenReview ↗
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2
Confidence
3
Informativeness
2
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2
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Paper summary

The paper shows that under hidden confounding, two standard observable CATE validation criteria — Robinson/R-loss and the DR pseudo-outcome loss — can improve while oracle CATE error (root-PEHE) worsens. Section 3 gives a population construction with binary U ⊥ X, Pr_s(T=1|X,U) = (1+sU)/2, and Y(t) = b(X) + a(X)U + tτ(X) + ε. Then the R-loss population minimizer is g_{R,s} = τ + 2sa, so CATE error is 4s²A while L_R,s(g_s) = σ² + (1−s²)A and L_DR,s = 4L_R,s; at every s > 0 both losses strictly prefer the biased g_s to the true τ (Prop. 1, Cor. 2). The empirical study instantiates this with continuous U, X-dependent logistic assignment, and estimated nuisances: two base families plus a pre-specified balanced bank of 24 environments × 11 severities × 20 paired seeds, across four EconML and four neural estimators. Reversal occurs in 92–100% of paired endpoint comparisons. A proxy study (CEVAE, CausalPFN, causal forest, DRLearner with Z_k = U + ε_k) shows the reversal scales with proxy informativeness. The recommendation is a "severity-path validation audit" reporting three trajectories: selected causal error, oracle-best error in the pool, and the observable score.

Critical strengths

S1. The population construction is correct and I verified it end to end. E[U|T=1,X] = s, g_{R,s} = τ + 2sa, E[(g_s−τ)²] = 4s²A, and the residual a(U − sW) + ε giving σ² + (1−s²)A all check out. The identity φ_DR,s − g = 2W(Y − m_s − (T−½)g), hence L_DR = 4L_R exactly, is a clean and correctly derived consequence of balanced assignment. Corollary 2's quadratic-in-s advantage of the biased target is exact. S2. The absolute-versus-relative decomposition is a genuine conceptual contribution. Separating (i) selected causal error, (ii) oracle-best error in the pool, and (iii) selection regret lets the paper state something the CATE-evaluation literature usually conflates: a score can be a good selector and a bad monitor. Table 1 makes this vivid — regret .006–.013 while oracle-best risk rises by ~1.05.

Critical weaknesses

W1 (major). The empirical direction is guaranteed by the design, not discovered. In every environment π_{k,s} = logit⁻¹(a_k q_k(X) + d_k s ℓ_kᵀU) with h_k(U) entering the outcome: severity raises both confounding and outcome-relevant variation, so root-PEHE must rise and R-loss must fall. The 24 environments therefore test the robustness of the magnitude and prevalence of a built-in effect, not whether the effect occurs. The decisive missing experiment is a 2×2 control on the two arrows U→T and U→Y: (a) U→T only (a valid instrument: confounding absent, reversal should vanish), (b) U→Y only at fixed assignment (no confounding), (c) both (reversal), (d) neither. Without this, the title's attribution to hidden confounding rather than to generic estimator degradation is not empirically isolated. Similarly, a stress that degrades the estimator without confounding (larger σ, smaller n, covariate shift) is needed to show R-loss moves in the correct direction there. W2 (moderate). The theory does not provide independent insight into DR loss. Under balanced assignment and exact nuisances, L_DR = 4L_R for every candidate, so the Section 3 result for DR is a rescaling of the R-loss result, not a second mechanism. The paper is explicit about this, but the abstract's "both losses reward movement toward the observed treated–untreated outcome difference" reads as two findings when the theory delivers one. The DR claim is carried entirely by the empirical section.

Questions for authors

Q1. Please run the 2×2 arrow control (U→T only / U→Y only / both / neither). If the reversal is absent when U→T is removed, the causal attribution is established; if it persists under U→Y only, the mechanism is broader than confounding and the framing needs revision. Q2. Please run one negative-control stress without confounding (increased σ, reduced n, or covariate shift) and confirm that R-loss moves in the correct direction there. This is what separates "hidden confounding breaks validation" from "any degradation breaks validation."

1 comment
AuthorsOpenReview ↗

New arrow controls attribute the reversal to hidden confounding; theory extended beyond balanced assignment

We thank the reviewer for verifying the construction and specifying the decisive controls. We have uploaded a revised paper and supplementary package incorporating these experiments and the expanded theory. We summarize the evidence here so the response is self-contained.

W1/Q1: what the theory does and does not settle. Section 3 and Appendix A characterize the observed-data target and validation geometry, including arbitrary propensities. What remains empirical is whether trained estimators exhibit reversal at practical sample sizes with regularization and estimated nuisances, and whether the effect is attributable specifically to confounding rather than generic degradation. The controls below test that attribution.

A second premise in W1 merits clarification: along our main severity path, only treatment assignment changes; the latent outcome contribution and potential outcomes remain fixed. Increasing severity strengthens confounding without increasing outcome-relevant variation. We nevertheless tested outcome variation separately.

We refitted all four EconML candidates in every control cell and recomputed both losses on an untouched monitoring split. Below are severity-one minus severity-zero changes for the R-loss-selected candidate across 24 environments and 20 paired seeds each. The first three rows are medians of environment-level means. Reversal means root-PEHE rises while loss falls.

Stress conditionΔ root-PEHEΔ R-lossΔ DR lossR/DR reversal
Hidden confounding: strengthen U→TU\to T, with U→YU\to Y active+1.111−.509−4.41499.0% / 95.8%
Treatment-only control: strengthen U→TU\to T, with U→YU\to Y absent−.004−.001−.45120.0% / 35.2%
Outcome-only control: strengthen U→YU\to Y, with T⊥U∣XT\perp U\mid X+.061+1.769+7.5540% / 0%
Null control: no arrow changes.000.000.0000% / 0%

The outcome-only control directly tests the reviewer’s concern that greater outcome-relevant latent variation might itself produce reversal. It does the opposite: both losses rise. The null row is zero by construction because severity changes neither arrow.

The treatment-only pair rates do not indicate a residual joint pattern. Root-PEHE rises in 45.0% of pairs, while R-loss and DR loss fall in 52.7% and 81.3%. Products of these sign marginals are 23.7% and 36.6%, close to the observed joint rates of 20.0% and 35.2%. The small DR drift follows an overlap change: mean ∣e(X)−.5∣|e(X)-.5| falls from .110 to .050, reducing its inverse-propensity variance term without increasing causal error.

The population decomposition predicts the control directions: when U→YU\to Y is absent or T⊥U∣XT\perp U\mid X, B=gR−τ=0B=g_R-\tau=0, so neither loss can reward confounding-induced bias. The experiments confirm these predictions for the trained estimators. Removing U→TU\to T eliminates reversal, satisfying the attribution criterion in Q1.

W1/Q2: degradation without confounding. We reduced candidate training size from 1,500 to 188 under unconfounded assignment while holding validation nuisances at their full-sample fits. Mean environment-level changes were +.175 root-PEHE, +.054 R-loss, and +.234 DR loss. Loss and causal error both rose in 80.4% (R-loss) and 80.0% (DR loss) of 480 paired comparisons; strict reversal occurred in only 7.5% and 7.9%. Every fixed candidate had positive mean changes in all three quantities. Observable validation therefore responds in the expected direction to estimator degradation without confounding.

These controls show that generic difficulty and latent outcome variation do not generate the reported pattern; within the tested designs, it arises from the omitted variable’s joint relevance to treatment and outcome.

W2: R-loss and DR loss. We agree that the balanced construction has one confounded target under two proportional losses, rather than two theoretical mechanisms. The abstract now states that “the losses share a confounded observed-data target but weight candidate errors differently.” The revision adds

L_{DR}(g)=C_{DR}+\mathbb E[(g-g_R)^2].$$ Both target $g_R=\mu_1-\mu_0$, but weight candidate errors differently. Equality $L_{DR}(g)=4L_R(g)$ for every candidate holds iff $e(X)=1/2$ almost surely; with nonconstant propensity they can rank candidates differently. The revision presents the controls in Section 5.3 and Table 3, full pairwise results in Appendix F, and the general geometry and proofs in Section 3 and Appendix A.

Comments on the paper

3 comments
AuthorsOpenReview ↗

Revised paper and responses available for discussion

We thank the reviewers again for their detailed feedback. Because some Outlook users may not have received recent OpenReview email notifications, we are posting this consolidated note to ensure that our responses are visible.

We have uploaded a revised paper and supplementary package and posted self-contained responses to each review. The revision includes the requested arrow-removal controls, unconfounded degradation control, effect-modification analysis, expanded theory, and practical severity-path guidance.

We would be grateful if you could review the revisions and responses at your convenience. We remain available for follow-up questions or additional clarification before the discussion period closes on November 18 AoE.

Area_Chair_MQrnOpenReview ↗

Reminder to engage in the discussion with Authors

Dear Reviewers,

Thank you for your effort in reviewing this submission. The authors’ responses to your comments have been available since November 10. Please take the time to read them and engage in the discussion. In particular, please indicate whether your main concerns have been adequately addressed and raise any remaining questions as soon as possible, so that the authors have an opportunity to reply before the rebuttal period ends on November 18.

Best regards

AC of Submission 30914

Dear Reviewers,

The rebuttal period ends in less than two days. If you have not already done so, I kindly ask you to acknowledge the authors’ responses, and indicate whether your main concerns have been adequately addressed or further clarification is needed.

Thank you.

AC

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