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Under review as a conference paper at ICLR 2027

Causal Matching with a Rank-Learned Prognostic Score

Abstract

Can pairwise outcome order suffice to learn useful causal matches? We answer this question by fitting a scalar prognostic score from binary comparisons of observed historical control outcomes, then using it for matching in an independent future cohort. This learner discards outcome magnitudes and is invariant to strictly increasing transformations of historical outcomes, with the fitting procedure fixed. Under a Gumbel location model, comparison probabilities calibrate prognosis differences up to scale. Our matching-specific bound transfers score error to mean squared error (MSE) of the average treatment effect on the treated (ATT), accounting for future support, adaptive donor selection and reuse. Standard ranking theory provides individual-level learning guarantees under explicit finite-class conditions. Six outcome-noise settings and an independently seeded sample-size study delimit the empirical benefit. In simulation study, increasing historical fitting size from 300 to 2400 changes RankNet from nearly tied with the state of art method to up to 90.0% lower mean conditional design MSE. The results establish effective matching from coarsened outcome supervision in this setting, while also showing the advantage of flexible full-outcome regression.

Primary area:
causal reasoning
Keywords:
causal inference, matching, metric learning, learning to rank, pairwise learning, prognostic scores, representation learning

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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_qU8GOpenReview ↗
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Paper summary

The paper introduces a new idea that we could use pairwise outcome order to fulfill the causal matching work instead of relying on outcome magnitudes. Its assumption of a Gumbel location model successfully builds the bridge between order and magnitude that makes the ATT estimation mathematically plausible. Besides, the author also tries to define the bound by linking score-learning error, future donor availability, and donor reuse to ATT MSE, making the error of ATT estimation explainable by errors from RankNet's prediction. The paper validates the method using several synthetic settings, a sample-size study, and a semi-synthetic LaLonde experiment. RankNet is compared with different matching methods such as full-outcome regression methods, BART, and causal forest. The experiments try to cover different outcome structures and noise settings and also report cases where RankNet does not outperform the alternatives.

Critical strengths
  1. The author brings a new idea that pairwise outcome order could replace the raw outcome magnitudes for control selection in a causal problem. This helps to understand how much outcome information is actually needed for learning useful matches from a different angle
  2. The math proof is concise and straightforward, as it builds the connection between order and prognostic distance under Gumble assumption.
Critical weaknesses
  1. The practical motivation of the proposed method could not be clearly detected. The method is developed and tested under lots of assumptions. And I don't know why or when I need to choose the method over other methods when the historical outcome is available. Especially, the experiments show that full-outcome learners can perform substantially better than RankNet.

  2. The empirical evaluation relies heavily on ATT MSE. Instead of evaluating it like a predictive model, I think more metrics for evaluating causal matching methods should be considered. We also care about the matching quality instead of the final ATT estimation.

Questions for authors
  1. In what practical setting should we use pairwise outcome order instead of the original historical outcome values? If the numerical outcomes are already available, especially given that full-outcome methods such as Huber regression perform better in some experiments, what is the main benefit of discarding the outcome magnitudes?

  2. What is the main new contribution of Theorem 1 compared with existing matching theory? The connection between score error and matching error could also apply to a prognostic score learned directly from numerical outcomes, so how would you attribute the contribution to pairwise order comparison?

  3. How do we know that RankNet's improvement over MALTS comes from using pairwise-order information but not from RankNet trained with a more flexible neural network? This is particularly important for the folded prognosis experiment, where the chosen setting appears to favor RankNet's nonlinear representation.

  4. Beyond overall ATT MSE, can the authors provide additional evidence that RankNet actually produces good causal matches? For example, metrics such as ATT bias and variance, matching quality, donor reuse, and post-matching balance could help validate the method and explain why it succeeds or fails in different settings.

  5. Related work mentioned Li and Fu (2017) as its closest ordinal matching precedent, but does not include it in the experiments. Is possible, it would also be great to compare RankNet with this method in experiments.

1 comment

Thank you for the constructive review. We have made substantial changes in the revision. Below is our point-by-point response. Our general response (the Official Comment by the authors) addresses novelty and clarifies when rank methods help.

W1 / Q1. Practical motivation: why discard magnitudes when outcome is available? In short, we discard magnitudes only when they are on the wrong scale so regression on them then learns the wrong conditional mean, while ranks still encode the outcome distribution (Figure 1, Section 3.1). In an applied example, a device or assay changes, as with the NHANES serum-folate assay, historical outcomes may not share the future scale. When values are reliable, regression should be used, and the paper shows this (Section 4.4; Section 4.2 in the original submission).

Q2. Contribution of Theorem 1. We address your second point first. Theorems 1 and 2 now share one framework for comparing learners: the affine calibration error a(g^)a(\hat{g}), a quantity that works for any learner, so RankNet and regression are judged on the same scale. That the bound also applies to regression is therefore deliberate.

On your first point, what is new relative to existing matching theory is when RankNet wins. Under a measurement transformation, ranks still encode the outcome distribution (Proposition 1), while outcome regression learns the transformed, and therefore biased, conditional mean. In the toy example, a=0a=0 for RankNet versus a≈0.122a \approx 0.122 for regression (Section 3.3). Theorem 2 characterizes the conditions under which RankNet is better in general, and the simulations confirm this (Section 4.3).

Q3. Ordinal information vs network flexibility. Note that MALTS is an outcome-based method, and the Huber MLP is a more flexible outcome-based method with the same two-layer network as RankNet. The gain over Huber is therefore a gain over outcome-based learning at equal flexibility: under distortion, Huber degrades while RankNet does not. We also added a normal-rank MLP with RankNet’s architecture, bounded head, initialization and assignment rule, trained on rank-derived targets. It is equally invariant and has similar MSE (paired difference −0.126 (0.284), Appendix B.8). The benefit thus comes from ordinal supervision, not from network flexibility or the pairwise loss.

W2 / Q4. Matching quality beyond ATT MSE. Good point. We agree that ATT MSE alone hides how the matches are formed. We now report the individual matching discrepancy DqD_q, a closeness measure, together with BqB_q, a bias measure (Section 4.2, Figure 2). BqB_q and DqD_q are related: since Bq2≤DqB_q^2 \leq D_q, a small DqD_q is the stronger result, because a small bias can come from cancellation, while a small discrepancy cannot. The results show that RankNet is better in MSE, bias and matching discrepancy, though the bias advantage holds at every transformation level, while the MSE and matching-discrepancy advantages appear under a moderate transformation of the outcome.

Q5. Li and Fu. We added it to the benchmark (Section 4.4, Figure 3; Appendix B.11). It is an outcome-based method, so we fit it on both historical arms and then match the future cohort. It does not perform as well: it is worse than RankNet in the linear, folded and KS designs and similar in the nonlinear design.

Reviewer_3KGxOpenReview ↗
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Paper summary

The authors study prognostic score matching to estimate the average treatment effect among the treated (ATT), a standard approach in which one uses data from a control or historical cohort to learn the conditional mean of the untreated outcome given covariates, m0(x)=E[Y(0)∣X=x]m_0(x)=E[Y(0)\mid X=x]. One can then match treated units to control units with similar prognostic scores and estimate the ATT by averaging the observed outcome differences between matched units.

The authors propose to learn the prognostic score m0m_0 using pairwise comparisons of outcomes in the control arm. To link these pairwise comparisons to the prognostic score, they assume a Gumbel location model with independent errors of constant scale ss, which implies that P(Yi>Yj∣Xi,Xj)=sigmoid((m0(Xi)−m0(Xj))/s)P(Y_i>Y_j\mid X_i,X_j)=\mathrm{sigmoid}((m_0(X_i)-m_0(X_j))/s). Under this assumption, the population-optimal RankNet score recovers m0m_0 up to scale and an additive constant, allowing it to be used for prognostic score matching.

The authors then evaluate the proposed method in simulations and find mixed performance relative to existing approaches.

Critical strengths

None

Critical weaknesses

The paper is poorly written and organized.

The introduction provides little motivation or context for the problem and instead jumps into vaguely describing the method in the second paragraph, which uses pairwise outcome orderings from a "completed historical cohort" (a term that is not explained at this point) to learn a RankNet score for matching. The final paragraph then discusses comparisons with baseline methods and experimental results. The paper appears to be concerned with using pairwise comparisons between observations to learn a score for matching, but the motivation and setup are not clearly explained in the introduction.

Section 2.2 discusses baselines and comparison methods before introducing the proposed method in Sections 2.3–2.4. This makes the presentation difficult to follow, as the reader has not yet been given a clear explanation of the method.

Why is Section 3.2 included in the main paper? It seems to do little beyond referring to a theoretical result in the appendix, which the authors acknowledge does not directly apply to the fitted neural network.

My main concerns are the following:

  1. Limited novelty. The proposed method is essentially prognostic score matching, where the prognostic score is learned using RankNet on pairwise comparisons of historical control outcomes rather than ordinary outcome regression. It is unclear what the methodological contribution is beyond combining these existing approaches.

  2. Strong and poorly motivated assumptions. Proposition 1 assumes that historical control outcomes follow a location model with i.i.d. Gumbel errors of constant scale. This assumption ensures that pairwise comparison probabilities follow a logistic model and that the learned RankNet score is proportional to the prognostic score. Why is this assumption reasonable? Without it, pairwise comparisons generally do not identify prognostic distances, which are essential for matching.

  3. Unclear advantage over ordinary prognostic score regression. The pairwise comparisons are constructed from observed historical outcomes, so the method deliberately discards information about outcome magnitudes. Why would this be preferable to simply estimating the prognostic score using a flexible regression model? The claimed invariance to monotone outcome transformations does not establish an advantage in treatment effect estimation.

  4. Limited theoretical guarantees. The learning guarantee discussed in Section 3.2 applies to finite function classes and does not directly cover the fitted neural network. Theorem 1 assumes a bound on the learned score's estimation error but does not establish that the proposed RankNet implementation achieves such a bound. It is therefore unclear what the theory establishes about the actual method.

  5. Unconvincing empirical results. The reported 90% improvement over MALTS occurs in a deliberately chosen folded prognosis setting where diagonal-distance matching is disadvantaged. In the same experiment, ordinary Huber regression substantially outperforms RankNet (MSE 0.048 versus 0.271). The experiments therefore do not convincingly demonstrate an advantage over standard prognostic score matching with flexible regression.

Questions for authors

None

1 comment

Thank you for the honest review. We have made substantial changes in the revision; below is our point-by-point response. Our general response (the Official Comment by the authors) addresses novelty and clarifies when rank methods help.

Presentation. The Introduction now opens with a concrete measurement problem, the NHANES serum-folate assay change, and defines the historical and future cohorts. Section 2 introduces the method before any baseline. The old Section 3.2 learning bound is replaced by a simpler theory that applies across methods. We illustrate the gain with a three-patient example in Section 3.1 and generalize in theory (Section 3.2) and simulation (section 4.3).

1. Novelty. We agree that RankNet and prognostic-score matching are established components. What is new is estimating treatment effects by matching on a RankNet-learned score, and showing when this beats matching on an outcome-learned prognostic score. Under a measurement transformation, ranks still encode the outcome distribution, while outcome regression learns the transformed, and therefore biased, conditional mean. Theorem 2 states when the rank-learned score has the smaller error bound, and the simulations confirm this (Section 4.3).

2. Why a Gumbel/logistic model? In short, it is a convenient choice in theory: it makes the optimum of the RankNet score identifiable in closed form (Proposition 1). The same probability argument works beyond Gumbel. For any i.i.d. noise independent of covariates, an increasing transformation leaves every comparison unchanged, and the comparison probability is an increasing function of the prognosis gap. So the right ordering is still learned after a monotone transformation of the outcome. In addition, Theorem 1 needs no Gumbel law, and the simulations show the same behaviour beyond the Gumbel model, under Gaussian noise.

3. Unclear advantage over ordinary prognostic-score regression. We hear this concern, and the revision now shows a clear advantage. When the historical scale is distorted, regression learns the wrong conditional mean, while ranks still encode the outcome distribution (Figure 1, Section 3.1). Section 3.2 generalizes this. The main experiment (Section 4.3) shows that RankNet is clearly better: at the strongest distortion, Huber's MSE reaches 8.833, while RankNet's stays at 1.614. The NHANES-covariate study in the appendix shows similar results.

4. What does the theory cover for the fitted method? Theorem 1 now uses a quantity that works for any learner, the affine calibration error a(g^)a(\hat{g}). It therefore applies directly to the actual frozen network, and equally to its probability limit. The paper mainly discusses the probability limit, which is the population target of each learner: m0/sm_0 / s up to a shift for RankNet (Proposition 1), and the conditional mean of the recorded outcome for regression. In the toy example, we use aa to show why RankNet is better ( a=0a=0 for RankNet versus a≈0.122a \approx 0.122 for regression), and Theorem 2 characterizes the conditions under which RankNet is better in general. A sufficiently flexible neural network can approximate these targets. Therefore, when the fitted networks are close to their targets, so that the same comparison holds for the fitted networks.

5.Unconvincing empirical results Our main simulation now addresses this: the main evidence is the distortion study in Section 4.3. The original folded benchmark is now a secondary experiment (Section 4.4). There, Huber is indeed better, both in the submission (0.048 vs 0.271) and now (0.086 vs 0.412), and the paper says so.

Reviewer_fJtWOpenReview ↗
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Paper summary

This paper studies whether pairwise outcome comparisons from historical controls can support prognostic matching in a future cohort. The proposed framework trains and freezes a RankNet score, and then uses it in reuse-capped linear assignment to estimate the sample conditional ATT. Under homoscedastic Gumbel noise, the authors show that pairwise rankings can recover the true outcome scale (up to an affine shift) and derive a finite-sample conditional MSE bound. Synthetic and semi-synthetic experiments show advantages over diagonal distance learning in "folded" prognostic settings. At the same time, the results show that standard robust regression (Huber-MLP) generally works better when reliable numerical historical outcomes are available.

Critical strengths
  1. The paper is honest about negative and mixed results, including weaker performance on the LaLonde benchmark and under 1NN axis-aligned perturbations. It also openly acknowledges that Huber-MLP performs better when historical numerical outcomes can be trusted.

  2. Folded response surfaces, such as $ m_0(x)=4|u| $, provide a clear and intuitive motivation: two units that are far apart in covariate space can share the same baseline prognosis, which standard coordinate-wise distance metrics fail to capture.

  3. Freezing the prognostic score before seeing future outcomes maintains an outcome-blind design, prevents outcome-driven tuning, and produces transparent, auditable matched pairs.

Critical weaknesses
  1. Good rankings do not guarantee good matching distances. Monotone invariance and robustness to extreme outcome values are standard properties of RankNet, rather than new causal insights. More importantly, getting the patient order right does not mean the score preserves true differences in $ m_0(X) $, which is what actually matters for reducing matching bias. The calibration proof relies heavily on homoscedastic Gumbel noise (A5); if the noise is heteroskedastic, asymmetric, or non-Gumbel, the spacing between scores can be distorted even when the ranking is accurate. Also, monotone invariance can throw away scale information that is needed to estimate ATT on the original outcome scale.

  2. The practical use case for ordinal-only history is quite narrow. When continuous historical outcomes are available, converting them into pairwise comparisons throws away useful information. Huber-MLP outperforms RankNet across the sample-size study, on LaLonde (on the dollar scale), and under 5% heavy-tailed linear contamination, while needing far fewer samples. In the folded sample-size study, RankNet needs large historical datasets (scaling from $ n=300 $ up to $ n=2400 $) to show large gains over MALTS, yet it still lags behind Huber-MLP. This leaves the paper's target scenario—where historical numerical outcomes are unusable, but future numerical outcomes are completely reliable—somewhat hard to justify in practice.

  3. Distribution shift and poor overlap remain major practical risks. The frozen ranker is trained on the historical control distribution $ P $, but applied to future treated and control groups. Its error bound scales with $ C_r=\omega_1+\frac{rN_0}{N_1}\omega_0 $, which can blow up under distribution shift. In addition, random pair sampling may miss comparisons within rare patient subgroups, and the bounded output layer $ 8\tanh(\cdot) $ can saturate at the extremes. Compressing covariates into a single 1D score can also create false overlap between regions that actually have no common support. When the unavoidable matching gap $ A_r $ is large, allowing more donor reuse $ r $ does not fix the overlap problem and only makes the variance and error bounds worse.

  4. The theoretical bounds are loose and do not fully match the implementation. In the score-error step (Eq. 5), the proof bounds every control unit's weight by the reuse cap $ K_j \le r $ across all $ N_0 $ controls. Because it does not use the total match constraint $ \sum_j K_j = N_1 $ in this step, the bound gets inflated by a factor of $ rN_0/N_1 .Relyingonworst−casedensityratios(. Relying on worst-case density ratios ( \omega_1, \omega_0 $) is also very conservative. Finally, the finite-class generalization analysis in Appendix A.2 does not directly apply to the continuous-weight MLP trained with early stopping used in the experiments.

Questions for authors
  1. Can you give a concrete real-world example where historical numerical outcomes are unusable or unavailable, yet future numerical outcomes are reliable enough to estimate the ATT? In that setting, why would pairwise ranking be better than simply using robust regression?

  2. How sensitive are the score calibration and final ATT estimates when Assumption A5 fails—for instance, under heteroskedastic or skewed historical noise?

  3. In practice, how should users detect when historical support is violated or when future treated and control groups lack overlap? How can we prevent bad matches instead of forcing the algorithm to match every treated unit?

2 comments

Thank you for the detailed review. We have made substantial changes in the revision; below is our point-by-point response, in two parts. Our general response (the Official Comment by the authors) addresses novelty and clarifies when rank methods help.

W1. Gain of using ranking.

Correct order does not preserve differences in m0(X)m_0(X). We agree, and Section 3 is now built on this point. In the three-patient example (Figure 1, Section 3.1), every score keeps the same order, yet squared-loss regression picks the wrong donor (matching discrepancy 1.44 vs 1). RankNet uses the comparison probability, whose log odds equal the prognosis gap under the Gumbel model (Proposition 1). Section 4 shows the same in simulation: under strong distortion, RankNet's matching bias is far smaller than Huber's (mean squared conditional bias 1.555 vs 8.793), and so is its matching discrepancy (Section 4.3).

Invariance and robustness are standard properties of RankNet. We agree. Our case is that in matching they give an advantage over outcome-learned scores. Under a measurement transformation, ranks still encode the outcome distribution, while regression learns the transformed, and therefore biased, conditional mean (Theorem 2, Section 4.3).

Scale information for the ATT. Invariance concerns only the historical data used to learn the score. The ATT is still estimated from future outcomes on the original scale, so no scale information is lost there.

Reliance on Gumbel noise (A5). We answer this together with your Q2 in part 2.

W2. Narrow use case; strength of Huber. Your reading is right: when values are reliable, that is, when the transformation is mild, regression should be used. The paper keeps every such result (Section 4.4; Appendices B.6–B.7; NHANES without distortion). Our target case is a historical scale that is unknown and nonlinear. There, regression learns the wrong conditional mean, and RankNet is clearly better (Section 4.3).

W3. Distribution shift and overlap. In short, we removed the density-ratio inflation, but the transfer risk remains. Theorem 1 replaces the density-ratio transfer step and CrC_r with a deterministic comparison on the future pool through a(g^)a(\hat g). This does not make shift harmless: a(g^)a(\hat g) is not certified by historical fitting, and D(J0)D(J_0) stays large if comparable future donors are missing. More reuse cannot create such donors. Our response to Q3 discusses how to detect this.

W4. Loose bounds and the fitted MLP. The rN0/N1rN_0/N_1 factor came from bounding every control's reuse separately. The new proof averages over the N1N_1 actual matched pairs, so the factor disappears, and reuse enters only the variance, through Kj2K_j^2. We also removed the finite-class and sampled-pair bounds. Theorem 1 instead uses a(g^)a(\hat g), which works for any learner, so it applies to the frozen MLP and to its probability limit, each learner's population target. A flexible network can approximate these targets. So when the fitting errors ρR\rho_R and ρN\rho_N in Theorem 2 are small, the comparison holds for the fitted networks.

Q1. A concrete example; why not robust regression? NHANES replaced its serum-folate assay between cycles, so legacy and new measurements are on different scales. A bridge exists there, so the example motivates the setting. With a reliable, often costly bridge, regression on the harmonized scale is the right choice. Without one, robust regression does not help: it downweights extreme residuals on the given scale but cannot undo a nonlinear measurement change. It therefore still learns the wrong conditional mean, while ranks are unchanged.

Q2 (and W1). Sensitivity to A5. In short, Gumbel is a convenient choice for identifiability; A5 is A4 in the revision. For i.i.d. noise independent of covariates, asymmetric or not, the comparison probability is still increasing in the prognosis gap, so ordering survives. Gumbel makes the log odds exactly linear in the gap, which gives distances.

With covariate-dependent (heteroscedastic) error shape, spacing and even ordering can fail. For example, Ya=1Y_a=1 with probability 0.9 and −10-10 otherwise has mean −0.1-0.1, yet beats Yb≡0Y_b\equiv0 with probability 0.9. We do not claim robustness there, and we did not run a heteroscedastic study. Empirically, the simulations show the same behaviour beyond the Gumbel model, under Gaussian noise (Section 4.3) and under equal-variance Gumbel noise (Appendix B.5).

Q3. Detecting support failures; avoiding forced bad matches. Our experiments match every treated unit and do not trim, so we claim no caliper benefit. To diagnose problems before seeing future outcomes, one can check treated–control overlap in the future cohort (propensity scores, key covariates and subgroups). One can also check historical-to-future coverage with a sample-membership model (Stuart et al., 2014, The use of propensity scores to assess the generalizability of results from randomized trials). To avoid forcing bad matches, prespecify a maximum score distance and leave treated units without an acceptable donor unmatched. Then report retention by subgroup; the estimand becomes the ATT of the retained treated (cf. Che et al., 2024, Caliper Synthetic Matching).

Comments on the paper

1 comment

We thank the reviewers for careful and candid reviews. All three raised two shared questions: what is new, and when outcome order should be used instead of outcome values. We answer both here, then summarize the revision. Section, figure and appendix numbers refer to the revised PDF; parentheses give one Monte Carlo standard error (MCSE).

What is new. RankNet and prognostic-score matching are established, and we no longer present their combination or monotone invariance as new. The contribution is an argument from measurement to matching:

  1. Under a latent Gumbel location model with an unknown increasing measurement change, comparison probabilities identify prognosis distances up to scale, not only their order (Proposition 1, now proved in full in Section 3.2). The simulations show the same behaviour beyond the Gumbel model, under Gaussian noise.
  2. One bound links any frozen scalar score, RankNet or regression, to the actual donor assignment and ATT bias through its best affine calibration error (Theorem 1).
  3. A sufficient condition states when Rank Matching's bound is the smaller one: the measurement change must distort the regression target by more than the two learners' fitting errors (Theorem 2).

When is order better than values? When historical outcomes are recorded on an unknown nonlinear scale that cannot be reliably bridged to the future scale, but still rank patients correctly. An increasing transformation leaves every comparison, and hence the fitted RankNet score and its donors, unchanged. Regression on the recorded values instead learns a distorted target: the wrong conditional mean. In other words, ranks encode the outcome distribution better than the mean does here (Figure 1 and Section 3.1). The theory in Section 3.2 generalizes this example to the general case. The main experiment in Section 4.3 shows the phenomenon: RankNet is clearly better. We also show similar results in the appendix, using semi-synthetic data with NHANES covariates.

When values are reliable, that is, when the transformation is mild, regression should be used. This is now shown in Section 4.4 (Section 4.2 in the original submission).

Other changes

  • The Introduction opens with the NHANES serum-folate assay change. Section 2 defines both cohorts and the measurement map first.
  • Section 3 follows one chain: the three-patient example, Proposition 1, then Theorems 1–2. The finite-class and sampled-pair bounds are removed.
  • The benchmark (Section 4.4, Figure 3) now uses 54 paired replications and adds Li and Fu (2017).
  • We report the individual prognosis discrepancy next to the signed bias, plus covariate balance and donor reuse (Section 4.2; Appendix B.9).
  • We removed the observed-X oracle diagnostic and several secondary tables.
  • All results where regression is better remain: the clean benchmark, the archived sample-size and perturbation studies (Appendix B.6), the LaLonde study (Appendix B.7) and the NHANES study without distortion.

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