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Under review as a conference paper at ICLR 2027

A Treatment-Anchored Proxy Diagnostic for Hidden Confounding

Abstract

Can indirect measurements of hidden factors help detect confounding between a treatment and an outcome? AO-CES measures how much these proxies change the predicted treatment. It then tests whether that change predicts the outcome after accounting for treatment and recorded covariates. We characterize misleading proxy mixtures in linear Gaussian models and correct the leading estimation bias under explicit learning conditions. In a controlled Gaussian study with 3,200 observations, correction reduces false positives from 90% to 5.5% while retaining 100% detection. Across 21 benchmark conditions, full-proxy prediction is competitive with five feature-learning variants, including variational autoencoders. As an application after Fast Causal Inference, AO-CES detects 93-100% of confounded pairs in structured graphs. These results show how proxy measurements can strengthen the assessment of hidden-confounding risks and guide closer causal scrutiny of observational findings.

Primary area:
causal reasoning
Keywords:
Hidden confounding, Causal Inference, Structure learning, Bayesian networks

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
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Paper summary

The paper proposes AO-CES, a diagnostic for hidden confounding of a specified treatment–outcome relation using pretreatment proxy measurements. It predicts T from contexts alone and again with W added; the difference, called the anchor, is then tested on held-out data for association with T beyond contexts and with Y beyond T and outcome contexts. A correction term removes the leading estimation bias introduced by the fitted anchor, and Theorem 1 gives an asymptotic false-positive guarantee under learning-rate conditions, while Proposition 1 characterizes when proxy mixtures create apparent confounding with no shared cause. Experiments cover 21 simulation conditions, a semi-synthetic use of WDBC covariates, a matched binary-treatment study, and an application that annotates FCI causal-discovery output with proxy-based confounding evidence under familywise-error control.

Critical strengths

1、The method achieves strong empirical performance across the reported simulation conditions and the FCI application.

2、The FCI application is sensible packaging that uses causal-discovery output to select candidates and adds confounding annotations with familywise-error control while reporting both the screening and multiplicity penalties.

Critical weaknesses
  1. All validation is synthetic or semi-synthetic, and the experiments repeat one narrow task across all 21 conditions rather than covering diverse tasks or any real observational study.

  2. The feature-learning comparison uses no variant newer than 2017, and binary-treatment power is near zero at n equals 800 and only 29 to 37 percent at n equals 3,200.

Questions for authors
  1. Proposition 1 and Figure 2a show that proxy mixtures violate the ideal outcome null even with no shared cause, and that the correction cannot repair this. Is there any data-driven check that flags when the proxy set itself violates the measurement conditions, or must a user simply assume validity?

  2. Is there any real observational dataset, with a plausible proxy and a ground truth or at least a benchmarked effect, on which AO-CES produces a sensible answer?

  3. Given 0 to 3 percent binary detection at n equals 800, what sample size would a practitioner need, and is there anything in the framework that can improve binary power beyond the prespecified logistic follow-up?

  4. In the FCI application, overall recall is 33.3 percent at low noise and 10.0 percent at high noise while precision is 99.3 percent, and the abstract reports only the 93 to 100 percent conditional recall. Can you reconcile these figures so that the practical recall of the pipeline is stated as prominently as its precision?

4 comments

Thank you for your comments and feedback.

Q1: Can data reveal invalid proxies?

Yes, some violations can be detected, but passing a check does not verify Assumption 2. Note that four linear measurements of one factor with mutually independent errors independent of that factor corresponds to σ12σ34=σ13σ24\sigma_{12}\sigma_{34}=\sigma_{13}\sigma_{24}, where σij=Cov⁡(Wi,Wj)\sigma_{ij}=\operatorname{Cov}(W_{i},W_{j}). Rejecting this covariance constraint provides evidence against that measurement model.

Passing can miss outcome information hidden in one measurement. For example, let all latent variables and errors be independent standard Gaussians:

T=U+εT,Y=βT+V+εY,W1=U+V+η1,Wj=U+ηj(∀j=2,3,4).T=U+\varepsilon_{T},\qquad Y=\beta T+V+\varepsilon_{Y},\qquad W_{1}=U+V+\eta_{1},\qquad W_{j}=U+\eta_{j}\\ (\forall j=2,3,4).

All off-diagonal proxy covariances equal one, so the constraints hold exactly. Yet A0=(W1+2W2+2W3+2W4)/9A_{0}=(W_{1}+2W_{2}+2W_{3}+2W_{4})/9 gives a nonzero outcome moment, θY,1=1/9\theta_{Y,1}=1/9, despite no hidden common cause.

We tested this check in 400 simulated datasets per setting, using 200 observations for checking and 800 others for AO-CES. With two strongly mixed measurements, 389 datasets failed the check. Withholding conclusions for them reduced false annotations from 241 to 6, but 6of the 11 passing datasets still produced false annotations. Thus the check cannot replace justification of how the measurements were collected.

Q2 and W1: Is there a real-data example with an external benchmark?

Yes: the Oregon Medicaid lottery provides randomized assignment alongside observational enrollment. We analyzed 22,188 households, holding out 4,438. The observational treatment was enrollment during days 1–180, and the outcome was emergency-department use during days 181–360. Five pre-lottery utilization indicators served as candidate proxies for health and care-seeking behavior, with demographic and lottery covariates adjusted for separately.

AO-CES rejected for enrollment (p=.002p=.002) but not randomized offer (p=.830p=.830); six further splits of the same records gave the same pattern. Taubman et al. (2014) supply an external randomized effect benchmark: approximately seven percentage points more emergency-department use over a different 18-month window.

This benchmark does not provide a ground-truth confounding label. Prior utilization may directly influence later use, so proxy validity still needs justification. Lottery non-rejection mainly reflects the absence of proxy information about randomized assignment, not a separate validation of the outcome test.

Q3: What sample size is needed, and how can binary power improve?

Sample size. In this simulation, 6,400 total observations, with 20% held out, was the first tested size that gave over 80% power for both confounding signs. With the improved fits described below, power was 97% for positive confounding and 91% for negative confounding. At n=800n=800, it remained 13% and 10%. These are design-specific results, not a universal sample-size requirement.

Improvement beyond logistic prediction. Keeping the logistic treatment predictor and relevance gate fixed, we simplified the downstream regressions to treatment-group means and main-effects ridge. At n=3,200n=3,200, power rose from 55% to 76% for positive confounding and from 37% to 67% for negative confounding (100 datasets per sign). The paired gains were 21 and 30%points, with 95% intervals of 12–30 and 21–40. These matched follow-up results are separate from the original experiment cited in the review.

At n=800n=800, the change reduced score standard deviations from about .20 to .08 while barely changing mean signals, explaining the power gain. At n=3,200n=3,200, false-positive rates were 0–4% across the three unconfounded settings, at nominal 5%. A fresh treatment-only null check at n=6,400n=6,400 gave 21/400 false positives.

Q4: Which FCI recall figures describe the full pipeline?

For the randomized graphs, full-pipeline recall is 33.3% at low noise and 10.0% at high noise. FCI retained 200 of 409 true confounded pairs. AO-CES detected 136 and 41 of those 200, respectively. Thus recall over all true targets is 136/409 and 41/409; precision is 99.3% and 97.6%.

The 93–100% figures come from separate structured graphs where FCI retained every target. The revised version will report the randomized graphs’ full-pipeline recall beside precision in the abstract and results, clearly distinguishing the benchmarks.

W2: Is there a comparison with a method newer than 2017?

Yes. We evaluated piecewise-linear encoding adapted from Gorishniy et al. (NeurIPS 2022). In the nonlinear-additive design at n=3,200n=3,200, corrected AO-CES achieved 70% power with this encoding and 67% with raw proxies. The three-point difference was uncertain (95% interval −2 to 8). Thus the comparison includes a recent encoding, without establishing that it outperforms raw proxies.

References: Gorishniy et al. (2022), NeurIPS; Taubman et al. (2014), Science; Oregon replication data.

Note the revised version will include all of this information, in an Appendix

Thank you for the detailed replies and the Oregon analysis. I read them carefully. The Oregon result is a useful illustration, but as you write yourselves it has no ground-truth label, so it does not really change my main concerns, which are the following.

My biggest concern is still that the experiments are one task with different settings. The 21 conditions are essentially the same procedure with switched parameters, so the diversity of what is actually tested is limited. I know the number of experiments alone does not decide novelty, but to me the experimental methods and the tasks are too simple. I also notice my W1 was only half answered in the rebuttal: the Oregon analysis covers the part about real observational data, but the part about one narrow task repeated across all 21 conditions was not addressed. Many methods discussed in the related work never appear in the experiments. I would add at least some of them as baselines, for example sensitivity-type checks such as Oster's coefficient stability (JBES 2019) or the robustness value of Cinelli and Hazlett (Political Analysis 2020), Rosenbaum bounds, negative-control-outcome tests in the sense of Lipsitch et al. (2010) and the proxy line of Miao et al. (Biometrika 2018), and CI-test based confounding detection like Entner et al. (2013). Without any of these comparisons it is hard for me to see where AO-CES stands among the tools people already use.

Second, the exposition of the method is confusing. The paper puts most of its weight on the task and on when existing approaches fail, while the core methodological contribution itself is not stated clearly. After reading it, it is still not easy for me to say in one sentence what the real innovation of AO-CES is. A paragraph that states this plainly would help the paper a lot.

Third, please add figures. A schematic of the anchor construction and of how the correction enters the test would help reviewers much more than another half page of formulas. In the AI era text is cheap, one clear figure is worth a lot.

Last small point, and this is only my personal impression: the style of subsection titles like 3.1, 3.2, 4.1 reads to me like AI-organized writing. Maybe it is just my preference, but together with the writing style of the text it made the paper feel less carefully prepared.

For these reasons I keep my score.

Thank you for clarifying the remaining concerns. We have revised the comparisons and presentation to address them directly.

1. Comparisons and broader evaluation. We added negative-control regression, a two-proxy bridge, Oster's coefficient stability, Cinelli–Hazlett robustness values, Rosenbaum bounds, and an Entner R1 adjustment-witness check, preserving their different targets and assumptions.

In 400 paired datasets per confounding condition, AO-CES and the designated negative-control test both achieved 100% detection, with 5% versus 6% null rejection. AO-CES received measurements without designated control roles.

We also evaluated adjustment and bias prioritization. Recording and adjusting for the omitted common cause removed AO-CES evidence in 393/400 datasets. Across 100 IHDP semi-synthetic replications, diagnostic strength tracked known selection bias (ρ=.72\rho=.72, 95% interval [.61, .79]), calculated from potential-outcome means. These replications reuse a cohort; this is benchmark evidence, not independent clinical validation.

2. Methodological contribution. AO-CES corrects the leading false outcome association introduced by estimating a treatment-predictive proxy score, with a validity guarantee under explicit measurement and learning conditions. Section 3 now states this directly.

3. Figures. Figure 2 shows anchor construction and where the correction enters; Figure 3 displays the empirical gains.

4. Presentation. We simplified the subsection titles and clarified the method explanation. Manuscript changes are marked in red; complete comparisons appear in Section 5 and Appendices M–O.

We would appreciate your reassessment in light of these comparisons, practical evaluations, and presentation changes.

Reviewer_NGXCOpenReview ↗
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Paper summary

This paper proposes AO-CES, a proxy-based diagnostic for hidden confounding that constructs a treatment-prediction anchor and tests its association with the outcome after adjusting for treatment and recorded covariates. It introduces an orthogonal correction for anchor-estimation error and establishes asymptotic false-positive control under measurement and learning assumptions.

Critical strengths

The paper clearly distinguishes misleading proxy measurement structure from contamination introduced by estimating the treatment anchor. Its population analysis identifies cases where even perfect prediction yields misleading confounding evidence, while its orthogonal correction addresses first-order estimation bias under explicit conditions. This separation clarifies both what the correction achieves and which causal limitations it cannot resolve.

Critical weaknesses
  1. There seems to be limited practical justification of the causal assumptions. The confounding interpretation relies on Assumption 2, which is not guaranteed by pretreatment timing or proxy mean exclusion, as the paper’s mixed-measurement counterexamples demonstrate. Although the paper provides sufficient measurement conditions, it offers limited guidance for justifying them in a broader proxy collection. More concrete scientific examples and guidance on proxy selection would strengthen the connection between the theoretical diagnostic and its intended applications.

  2. Also, I feel that there’s a gap between statistical guarantees and implementation. The required learning conditions are verified for Gaussian OLS but not for the nonlinear learners used in the broader experiments, and the reported calibration seems imperfect. These results do not necessarily contradict the asymptotic theorem, but leave uncertainty about when the implemented procedure provides reliable error control. More systematic calibration results across sample sizes and learner specifications would help establish its practical reliability.

  3. The experiments provide useful controlled demonstrations, but I find the strongest reported results offer limited evidence of practical generalizability. Specifically:

    • The reduction from 90% to 5.5% false positives comes from adding outcome-only information to treatment predictions in a setting where the proxy vector directly contains the latent factors. This validates the intended correction mechanism, but does not establish how frequently comparable contamination arises with naturally fitted predictors and noisy measurements.
    • The 93 - 100% recall in Appendix H is obtained in structured graphs where FCI retains the relevant confounded pairs. In the randomized graphs of Appendix K, candidate recall falls to 48.9%, and overall corrected recall is only 33.3% with lower proxy noise and 10.0% with higher noise. These results imply a substantial dependence on candidate coverage and measurement quality.
Questions for authors
  1. I appreciate the authors’ explicit acknowledgment that non-rejection does not establish absence of confounding. Beyond this general limitation of hypothesis testing, could the authors characterize when hidden confounding produces a nonzero ideal-anchor outcome moment?

  2. For full-proxy corrected tests, Tables 8 and 9 show nonlinear-additive detection increasing from 16% with the identity test to 40% with smooth8, whereas independent-factor detection decreases from 63% to 35%. What explains these different patterns?

  3. Based on the available comparisons, under what conditions should practitioners prefer AO-CES over alternative diagnostics?

3 comments

Thank you for your comments and feedback.

Q1: When does confounding produce a nonzero outcome moment?

Yes. The linear Gaussian model admits a necessary-and-sufficient population condition for multiple latent factors and both test banks.

Proposition R3 (exact Gaussian detectability). With constant contexts, consider

T = a⊤U+εT,Y = βT+b⊤U+εY,W=LU+e.T\ =\ a^\top\mathbf U+\varepsilon_{T},\qquad Y\ =\ \beta T+b^\top\mathbf U+\varepsilon_{Y},\qquad \mathbf W=L\mathbf U+\mathbf e.

Let U∼N(0,I)\mathbf U\sim N(0,I), with centered Gaussian errors εT,εY,e\varepsilon_{T},\varepsilon_{Y},\mathbf e mutually independent and independent of U\mathbf U. Assume Var⁡(W)\operatorname{Var}(\mathbf W) is nonsingular. Define D=Var⁡(T)>0D=\operatorname{Var}(T)>0, Q=Var⁡(E[U∣W])Q=\operatorname{Var}(\mathbb{E}[\mathbf U\mid \mathbf W]), and

v=a⊤Qa,Δ=b⊤Qa−a⊤bDv.v=a^\top Qa,\qquad \Delta =b^\top Qa-\frac{a^\top b}{D}v.

If v>0v>0, every square-integrable transformed anchor H(A0)H(A_{0}) satisfies

θT,H=Cov⁡(A0,H(A0)),θY,H=ΔvθT,H.\theta_{T,H}=\operatorname{Cov}(A_{0},H(A_{0})),\qquad \theta_{Y,H}=\frac{\Delta }{v}\theta_{T,H}.

Both banks have signals on both branches if and only if Δ≠0\Delta \ne0: identity and smooth8’s saturated-linear coordinate are strictly increasing. If Δ=0\Delta =0, every transformation’s outcome moment vanishes; if v=0v=0, the anchor is constant.

Proof. Projection gives the first identity; Gaussian regression gives E[Y−E[Y∣T]∣A0]=(Δ/v)A0\mathbb{E}[Y-\mathbb{E}[Y\mid T]\mid A_{0}]=(\Delta /v)A_{0}, hence the second. Strictly increasing transformations have positive covariance with a nonconstant anchor.

For a concrete interpretation, take separate equally noisy measurements W=U+e\mathbf W=\mathbf U+\mathbf e, with independent e∼N(0,τ2I)\mathbf e\sim N(0,\tau ^2I) and σT2=Var⁡(εT)>0\sigma_{T}^2=\operatorname{Var}(\varepsilon_{T})>0. Then

Δ = σT2(1+τ2)D∑jajbj.\Delta\ =\ \frac{\sigma_{T}^2}{(1+\tau ^2)D}\sum_{j} a_{j} b_{j}.

Detection is therefore equivalent to ∑jajbj≠0\sum_{j} a_{j} b_{j}\ne0. One shared factor suffices if all nonzero contributions ajbja_{j} b_{j} have the same sign; opposing contributions can cancel. Equal measurement noise is substantive here. Interpreting a nonzero signal as confounding still requires justified measurements.

Q2: Why does smooth8 help one setting but hurt another?

Nonlinear transformations can reveal signals missed by identity, but smooth8 excludes identity and pays a larger multiple-testing penalty. Proposition R3 also shows that transformations cannot recover a missing Gaussian population signal when Δ=0\Delta =0. In a matched follow-up to Tables 8–9, cosine alone detected 38/100 nonlinear-additive alternatives at the stricter cutoff. In independent-factor data, identity detected 61/100; saturated-linear detected 55/100 at cutoff 1.960 but only 27/100 at cutoff 2.734. Other coordinates recovered 12, giving 39/100.

Q3: When should practitioners choose AO-CES?

Prefer corrected AO-CES for a specified treatment–outcome relation with justified proxies and a learned anchor. Theorem 1 explains why: correction changes first-order anchor bias into products of fitting errors, protecting inference even when both predictors are consistent.

Illustration with noisy proxies. Let all latent factors and errors below be independent standard Gaussians:

T=UT+εT,Y=βT+UY+εY,WT=UT+ηT,WY=UY+ηY.T=U_{T}+\varepsilon_{T},\qquad Y=\beta T+U_{Y}+\varepsilon_{Y},\qquad W_{T}=U_{T}+\eta_{T},\qquad W_{Y}=U_{Y}+\eta_{Y}.

There is no hidden common cause. For the identity test, the true anchor and correction regression are A0=WT/2A_{0}=W_{T}/2 and q0=WY/2q_{0}=W_{Y}/2. Consider constructed estimates A^0=(WT+δWY)/2\widehat A_{0}=(W_{T}+\delta W_{Y})/2 and q^=(1+ε)WY/2\widehat q=(1+\varepsilon )W_{Y}/2, with other regressions correct. The uncorrected outcome mean is δ/2\delta /2; the corrected mean is −εδ/2-\varepsilon \delta /2. With δ=ε=n−1/3\delta =\varepsilon =n^{-1/3}, where nn is the independent test size, both errors vanish, yet the uncorrected outcome test’s false-rejection probability tends to one. The corrected test retains asymptotic false-positive control under the stated calibration. Good prediction and independent test data alone are therefore insufficient.

This comparison is with uncorrected identity testing. HOLS, KRCD, and effect-identification methods address different hypotheses; these results do not establish a universal ranking.

W1: How can the measurement assumptions be justified?

Separate treatment-side and outcome-side measurement channels, with their latent/error blocks independent conditional on recorded context, imply Assumption 2 even for nonlinear mechanisms. We will give the derivation and a noisy-proxy example. In applications, assess how measurements were acquired, whether errors mix the two channels, and whether measurements directly influence outcomes. Pretreatment timing alone is insufficient.

W2–W3: Naturally fitted predictors and nonlinear calibration

Yes, the correction also helped without injected error. With cross-validated ridge predictors, four noisy readings per factor, and identical test observations, false positives fell from 10.0% to 4.25% at n=400n=400 and lower noise (400 cohorts; paired reduction 5.75 points, 95% interval 2.25–9.25); power was 57.25% versus 56.5%.

The benefit has limits. At n=1,600n=1,600 and higher noise, false positives fell from 9.0% to 5.5%, but power fell from 83.25% to 69.25%. At n=400n=400 and higher noise, corrected false positives were 7.75% (95% interval 5.5–10.8%). In a nonlinear-additive follow-up at n=3,200n=3,200, correction increased power from 54% to 67% with raw proxies and 61% to 70% with piecewise-linear embeddings; corrected false positives were 5%/4%. These are empirical results: the learning-rate conditions remain verified for Gaussian OLS, but this is not necessarily true for all nonlinear learners.

W3: FCI candidate coverage

We agree that candidate coverage and proxy quality materially limit the pipeline. Structured graphs retained every target and achieved 93–100% end-to-end recall. Randomized graphs retained only 200/409 targets (48.9%); end-to-end recall was 33.3%/10.0% at low/high noise, with precision 99.3%/97.6%. We will give these end-to-end results equal prominence in the abstract and results.

Thank you for your thorough response. Your clarifications and the revisions to the manuscript have sufficiently addressed my previous concerns. I will maintain my score.

Reviewer_JopROpenReview ↗
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Paper summary

The paper considers causal inference in settings where there is possibly unmeasured confounding. however, some proxies are available for confounding factors (specifically, some variables caused by the unobserved confounding factors). The paper suggests methods for detecting the presence of such hidden confounding using the proxies. Two simple approaches are to (a) asses whether (possibly after controlling for some pre-treatment covariates) the proxies are predicting of both treatments and outcomes (the latter after also controlling for treatment), (b) assess whether controlling for the proxies leads to changes in the estimated causal effect. The paper points out that these approaches could be misleading: suppose two independent sets of unobserved factors impact treatment and outcomes so that there is in fact no confounding, but the proxies are impacted by all of these factors, then approaches (a) and (b) will detect confounding when there is none. Motivated by this, the paper suggests an alternative approach. In short, one estimates an "anchor" that captures the associated between the proxies and the treatment, this has formula A0(W,CT):=E[T∣W,CT]−E[T∣CT]A_0(W,C_T):=E[T|W,C_T]-E[T|C_T], where TT is treatment, WW are the proxies, and CTC_T are some pre-treatment covariates. Then one assesses whether the revisualized outcome is mean-independent of this anchor. Under certain conditions this approach is valid.

The authors suggest a statistical method based on the arguments above. They estimate correlations between the residualized outcome and a fixed vector of transformations of the anchor. The anchor is estimated in a first-stage, and so they de-bias by orthogonalizing and applying cross-fitting in-line with the literature on Double/De-Biased Machine learning. This allows for root-nn consistency and simply inference. The authors provide simulation evidence of the efficacy of their method and apply it to real data.

Critical strengths

The paper is clearly written. I think the main idea is intuitive and mostly well-motivated. Detecting unmeasured confounding using proxies is an important topic.

Critical weaknesses

The key weakness, as I see it, is the high-level Assumption 2. The condition comes very close to directly assuming the validity of the approach. The linear Gaussian example in Section 4.1 seems to demonstrate one case in which the approach may be valid, but even then I do not see why the term a′Qba'Qb would be zero when the non-zero entries of aa and bb do not overlap. Am I correct in concluding Assumption 2 does not hold even in this case?

In short, while the paper has convinced me alternative methods may detect confounding that is not there, it seems that the methods in the present paper may do likewise, and the authors simply assume away this possibility by invoking Assumption 2.

Questions for authors

Can you construct an example in which Assumption 2 holds? Are there reasonable primitive conditions on the joint distributions of the variables under which it holds?

If there is confounding, could there be some guarantee that the test will detect it (at least in an infinite population)?

5 comments

Thank you for your comments and feedback.

First weakness: does Assumption 2 hold when the latent factors are disjoint?

Not in general. You are correct that disjoint coefficient supports imply a⊤b=0a^\top b=0, but do not force b⊤Qa=0b^\top Qa=0. The matrix QQ in Section 4.1 measures covariance between proxy-based predictions of the latent factors; these predictions need not be independent. For an explicit counterexample, take U,V,εT,εY,ηU,V,\varepsilon_{T},\varepsilon_{Y},\eta to be independent standard Gaussian variables and let

T=U+εT,Y=β,T+V+εY,W=U+V+η.T=U+\varepsilon_{T},\qquad Y=\beta\\, T+V+\varepsilon_{Y},\qquad W=U+V+\eta .

In this counterexample, A0 = W/3A_{0}\,=\,W/3 and θY,1=1/3\theta_{Y,1}=1/3, despite no hidden common cause. Assumption 2 fails here even with the exact population anchor. Q1(a) gives a noisy-proxy example where Assumption 2 holds; Proposition R1 in Q1(b) establishes a broader nonlinear class where it holds.

Q1(a): An example where Assumption 2 holds

Yes. Let U,V,εT,εY,ηT,ηYU,V,\varepsilon_{T},\varepsilon_{Y},\eta_{T},\eta_{Y} be independent standard Gaussian variables and set

T=U+εT,Y=βT+V+εY,W=(U+ηT,V+ηY).T=U+\varepsilon_{T},\qquad Y=\beta T+V+\varepsilon_{Y},\qquad W=(U+\eta_{T},V+\eta_{Y}).

There is no hidden common cause: UU influences treatment, while VV influences the outcome. The anchor is A0=W1/2A_{0}=W_{1}/2. Since V+εYV+\varepsilon_{Y} is independent of (T,A0)(T,A_{0}), E[Y∣T,A0]=βT=E[Y∣T]\mathbb{E}[Y\mid T,A_{0}]=\beta T=\mathbb{E}[Y\mid T], which exactly matches Assumption 2. Both proxy measurements are noisy; neither reveals its latent factor.

Q1(b): Sufficient conditions beyond the example in Q1(a) above

Yes. The following proposition gives sufficient conditions on the measurement mechanisms, allowing nonlinear functions and noisy measurements.

Proposition R1 (sufficient conditions for Assumption 2). With CT = CY = CC_{T}\ =\ C_{Y}\ =\ C, suppose

T=fT(C,UT,εT),Y = fY(T,C,UY,εY),T=f_{T}(C,U_{T},\varepsilon_{T}),\qquad Y\ =\ f_{Y}(T,C,U_{Y},\varepsilon_{Y}),

WT=hT(C,UT,ηT),WY=hY(C,UY,ηY).W_{T}=h_{T}(C,U_{T},\eta_{T}),\qquad W_{Y}=h_{Y}(C,U_{Y},\eta_{Y}).

Assume (,UT,,εT,,ηT)(\\,U_{T},\\,\varepsilon_{T},\\,\eta_{T}) and (UY,εY,ηY)(U_{Y},\varepsilon_{Y},\eta_{Y}) are independent conditional on CC. Also assume T,Y,WT,WYT,Y,W_{T},W_{Y} have finite second moments. The functions fT,fY,hT,hYf_{T},f_{Y},h_{T},h_{Y} are measurable and may be nonlinear; no linearity or Gaussian-distribution assumption is required. Then E[Y∣T,C,A0]=E[Y∣T,C]\mathbb{E}[Y\mid T,C,A_{0}]=\mathbb{E}[Y\mid T,C]: that is, Assumption 2 holds.

Proof. Block independence gives E[T∣WT,WY,C]=E[T∣WT,C]\mathbb{E}[T\mid W_{T},W_{Y},C] = \mathbb{E}[T\mid W_{T},C], so A0A_{0} is a function of (WT,C)(W_{T},C). It also gives Y⊥WT∣(T,C)Y \perp W_{T} \mid (T,C), which implies the stated equality. Thus the anchor retains treatment-side information without introducing the independent outcome-side information.

Note the Appendix will include these examples, and proposition.. and the main text will point to this clarifying material.

Q2: A guarantee of detecting confounding

Yes. Below is a sufficient guarantee for a nonlinear class having one shared cause. Other models can also be detectable; we are not claiming the conditions below are necessary.

Proposition R2 (detection of a monotone shared cause). Take the recorded covariates CTC_{T} and CYC_{Y} to be fixed constants, so they can be omitted below, and let

T=f(U)+εT,Y=r(T)+g(U)+εY,W=U+η.T=f(U)+\varepsilon_{T},\qquad Y=r(T)+g(U)+\varepsilon_{Y},\qquad W=U+\eta .

Assume U,εT,εY,ηU,\varepsilon_{T},\varepsilon_{Y},\eta are mutually independent; UU is nondegenerate; the errors are centered; and εT,η\varepsilon_{T},\eta are Gaussian with positive variances, and U,f(U),g(U),r(T),εYU,f(U),g(U),r(T),\varepsilon_{Y} have finite second moments. If ff and gg are strictly monotone, the ideal anchor has a positive treatment moment and a nonzero outcome moment. The outcome moment is positive when their directions agree and negative otherwise. This holds for identity and smooth8’s saturated-linear transformation.

Proof. Gaussian measurement noise makes m(w)=E[,f(U)∣W=w,]m(w)=\mathbb{E}[\\,f(U)\mid W=w\\,] strictly monotone in the direction of ff: m′(w)=Cov⁡(f(U),U∣W=w)/Var⁡(η)m^{\prime}(w)=\operatorname{Cov}(f(U),U\mid W=w)/\operatorname{Var}(\eta ). For H(a)=aH(a)=a or H(a)=4tanh⁡(a/4)H(a)=4\tanh(a/4), k(u)=E[,H(A0)∣U=u,]k(u)=\mathbb{E}[\\,H(A_{0})\mid U=u\\,] has that same direction. Conditional independence of WW and TT given UU yields

θY,H=E[Cov⁡(g(U),k(U)∣T)],θT,H=Cov⁡(A0,H(A0))>0.\theta_{Y,H}=\mathbb{E}[\operatorname{Cov}(g(U),k(U)\mid T)],\qquad \theta_{T,H}=\operatorname{Cov}(A_{0},H(A_{0}))>0.

Treatment noise keeps U∣TU\mid T nondegenerate, so the first covariance has the asserted strict sign. Intuitively, adjusting for TT removes r(T)r(T), but does not reveal UU completely; the proxy retains outcome information. With the paper’s learning, moment, and calibration conditions, growing development/test samples, and a vanishing relevance threshold, power against each fixed alternative in this class tends to one. However, this is not a guarantee for arbitrary, potentially cancelling confounder effects.

Final weakness: does Assumption 2 assume away the failure AO-CES is meant to address?

We agree that simply invoking Assumption 2 does not resolve this objection. AO-CES cannot repair measurements that already mix unrelated treatment and outcome causes. Proposition R1 starts from separate measurement channels and independent latent/error blocks. It then proves that adding A0A_{0} to (T,C)(T,C) does not change the conditional mean of YY, which is the equality required by Assumption 2. In an application, knowledge of how the measurements were collected must support those channel and independence assumptions.

Within this class, anchoring makes a concrete difference. In Q1(a), Z=W1+W2Z=W_{1}+W_{2} has treatment and adjusted-outcome moments both equal to 1 despite no hidden common cause; the anchor’s outcome moment is 0. The fitting correction then addresses estimation error under the stated learning conditions. We will make this scope explicit: anchoring avoids misleading summaries of valid measurement channels; it does not make arbitrary measurements valid.

Again, the Appendix of the revised version will include these examples; and the main text will point to this, where appropriate.

Okay, but in the case of R1, there is a simpler solution: just check if both WTW_T and WYW_Y are associated with both TT and YY. If there is confounding (the CC argument in both TT and YY is non-trivial) assessing whether both of WTW_T and WYW_Y are associated with both TT and YY would detect that confounding, and when there is no confounding (CC doesn't actually enter into both of TT and YY) then either WTW_T is independent of YY or WYW_Y is independent of TT.

Comments on the paper

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Thank you for the discussion. Three findings clarify what AO-CES contributes:

1. Anchoring can succeed where separate proxy tests fail. Our 13 November example shows that both observed proxies can predict treatment and adjusted outcome even without confounding. Joint anchoring removes this false signal without knowing the separating coordinates. The example uses an information-preserving mixture of valid, noisy measurements.

2. We give explicit conditions for validity and detection. R1 derives the required outcome null from measurement mechanisms. R2 guarantees a nonzero population signal for a nonlinear class of shared causes. These results specify when the diagnostic works, rather than claiming validity for arbitrary proxies.

3. The benefits extend beyond injected errors. With naturally fitted predictors and noisy proxies, false positives fell from 10.0% to 4.25% across 400 simulated datasets, with power essentially unchanged. At n=3,200, simpler downstream fits improved binary-treatment power by 21–30 percentage points, with false-positive rates of 0–4% across the tested nulls. The Oregon analysis adds a real-data comparison with randomized assignment, without treating it as ground-truth confounding validation.

We would appreciate feedback on which substantive concerns remain after these results, so we can address them before the discussion closes.

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

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