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Under review as a conference paper at ICLR 2027

N-of-1 Surrogacy: Evaluating and Learning Surrogate Maps for Individual-level Treatment Decisions

Abstract

The N-of-1 study design, i.e., experimentation on a single individual, is the gold standard for fully personalized treatment decisions. In practice, however, the primary outcome of interest can be too delayed or costly to measure, and is often observed only once, making an individual's counterfactual outcomes under different treatments unavailable. Treatment decisions must therefore rely on intermediate measurements, known as surrogate outcomes. Existing surrogate frameworks establish validity with respect to population-average treatment effects. However, population-level surrogacy need not imply correct _individual-level_ decisions. We formalize individual-level surrogacy through the regret of the treatment policy induced by a surrogate map, a function of intermediate measurements. Because individual-level regret depends on unobservable subject-level counterfactual outcomes, we propose an evaluation framework based on outcome imputation and establish identifiability of the individual-level regret under suitable assumptions. We propose an estimator that targets the individual-level regret of surrogate maps using observed data, and further discuss when how surrogate maps can be learned from data. In controlled experiments, we validate the finite-sample behavior of our evaluation procedure and its behavior under assumption violations. Finally, we apply the framework to longitudinal data from a large-scale wearable health study, and evaluate fixed biomarkers and learned surrogate maps as individual-level surrogates for the effect of changes in physical activity on the onset of cardiometabolic disease.

Primary area:
causal reasoning
Keywords:
causality, surrogate outcomes, surrogacy, individual treatment effect, individualized treatment rules, surrogate paradox

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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.
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Paper summary

The paper formalizes individual-level surrogacy for N-of-1 settings via the regret of a surrogate-map-induced policy and proposes an imputation-based evaluation that is identifiable under strong assumptions on latent invertibility and full mediation. While the problem is important and the formalization is clean, the core results rest on restrictive, untestable assumptions that are unlikely to hold in the motivating applications; the empirical support (synthetic DGPs matched to the assumptions + a heavily pre-processed observational wearable cohort) is insufficient to demonstrate reliable practical utility; and the overall advance over existing surrogate-index and causal-surrogacy literature is incremental. These foundational limitations make the work unsuitable for acceptance at a top venue.

Critical strengths
  1. The formalization of individual-level regret (Definitions 2–3) cleanly distinguishes ranking of counterfactual outcomes for a single subject from population-average treatment-effect estimation, filling a genuine conceptual gap left by classical surrogacy criteria.

  2. The synthetic experiments carefully isolate the effect of sample size, outcome-model misspecification, and assumption violations, and the Apple Heart & Movement Study application demonstrates that the proposed pipeline can be instantiated on complex longitudinal wearable data, producing concrete (if still observational) rankings of biomarkers.

Critical weaknesses
  1. Critical dependence on strong, untestable assumptions.Identifiability of individual-level regret (Theorem 1) requires Assumption 2 (latent type UjU^j is constant and fully recoverable by a measurable left-inverse of g0g_0) together with support inclusion. This is far stronger than standard unconfoundedness or Prentice-style conditions and is essentially untestable. The discussion acknowledges the issue but provides only limited ablations; in the Apple Heart & Movement Study application the assumption is simply postulated (“residual confounding captured in latent type UjU^j”). When the assumption fails, the pseudo-regret can be arbitrarily misleading.

  2. Evaluation procedure is circular and inherits observational confounding.Pseudo-outcomes are obtained by regressing the long-term outcome on (A,X,S)(A,X,S) in an observational population study and then plugging the N-of-1 subject’s observed (A,X,S)(A,X,S) into that regression. Any residual confounding, model misspecification, or support mismatch between the observational cohort and the N-of-1 subjects directly contaminates the “ground-truth” ranking used for evaluation. The real-data pipeline (change-window construction, Cox pseudo-labels, cross-fitting with only 10 % held-out subjects) amplifies rather than mitigates these problems.

  3. Empirical validation is weak and does not support the claimed practical utility. Synthetic experiments use a DGP deliberately constructed to satisfy the paper’s assumptions; finite-sample consistency is therefore unsurprising. The sole real-world illustration is a secondary analysis of the observational Apple Heart & Movement Study, mapped onto the N-of-1 framework via post-hoc change windows. Treatments are self-selected, residual time-varying confounding is uncontrolled, and no prospective or external validation is performed. Findings such as “VO₂max ranks well” or “PPG embeddings do not help” remain descriptive and clinically uninterpretable under the paper’s own assumptions.

  4. Limited novelty relative to the surrogate-index and causal-surrogacy literature. The surrogate index of Athey et al. (and related causal maps) already constructs scalar summaries of intermediate measurements for treatment-effect estimation. The paper’s main conceptual move—reinterpreting the same conditional-expectation objects as ranking devices for individual-level regret—is modest. Learning results (Appendix A.7) recover essentially the same causal surrogate map under additive confounding, and generalization guarantees require an additional full-mediation assumption that is only marginally weaker than classical no-direct-effect conditions.

  5. Scope of the guarantees is too narrow for the motivating use-cases. Even under the stated assumptions, evaluation is only valid for treatments already observed in the population study (or for new treatments that fully mediate through the same surrogate space and produce sufficiently diverse surrogate pairs). In the very settings the paper advertises—novel exercise regimens, new advertising campaigns, new drug doses—population support is absent by definition, rendering the evaluation procedure inapplicable precisely when it is most needed.

Questions for authors

Please refer to the weaknesses

1 comment

We thank the reviewer for the detailed review and the appreciation of our formalization of individual-level surrogacy. Several listed weaknesses rest on what we believe to be a misunderstanding of our results, which we resolve below and in the general response (G1–G4). We have revised the presentation accordingly.

W1. Assumption 2. We agree that it is an untestable identification assumption, and our discussion says so. We do not agree that it is "far stronger" than unconfoundedness or Prentice-type conditions. Prentice-type criteria and the surrogate index rely on the absence of unobserved surrogate-outcome confounding, in which case our assumption (restated in G1, now allowing noisy surrogates) holds trivially if there is no latent UU. We cover confounded settings, as long as the confounder is revealed by the treatment-response pair. Although standard conditions might identify population-average effects here, ranking of a single subject's treatments remains highly nontrivial (App. A.3). We explain in G2 why such an assumption is unavoidable. "Arbitrarily misleading": map comparisons remain valid under any within-subject constant bias, and otherwise admit a simple sensitivity analysis (G3).

W2. "Circular" evaluation. A surrogate map is a function of (S,X)(S,X) only, whereas the pseudo-label uses the regression of YY on (A,X,S)(A,X,S). Both are fitted on separate samples. If the evaluation were circular, we could predict ahead which map achieves the lowest pseudo-regret, and the surrogate index E[Y∣S,X]\mathbb{E}[Y\mid S,X], similar to the label up to inclusion of AA, should win. This is not the case: it often achieves a higher pseudo-regret than other methods, such as control functions, so our evaluation carries real signal. In contrast to the reviewer's claim, our preprocessing (change windows, change-from-baseline, Cox model) makes the assumptions more plausible (G4). "Only 10% held-out" is per rotation: over the 20 rotations every participant serves as an evaluation subject twice. Map fitting, pseudo-outcome fitting and evaluation are fully disjoint.

W3. Empirical validation. The consistency of our estimator is not meant to be surprising: Fig. 2 illustrates that the pseudo-regret inherits the finite-sample rate of the pseudo-label estimator and is biased if that model is misspecified. In Fig. 8, we actually study violations of Assumption 2 and misspecification. In AHMS, one strength of our framework is that treatments are allowed to be self-selected within a subject (App. A.6), and we do control for time-varying confounding (G4). Our findings are meant to be initial and qualitative. In G4, we explain why no ground truth exists yet. If the reviewer knows of suitable N-of-1 trials with years of follow-up per treatment, we would be happy to validate our method there.

W4. Novelty. We extensively position our work against the surrogate index (SI) (l. 65-75, App. A.1, A.3, A.7). The SI, proposed for population-level surrogacy under Prentice-style assumptions, is one of the candidate maps we evaluate. By A.3, population-level surrogacy neither implies nor is implied by individual-level surrogacy, and in our setting the SI is provably suboptimal, as also observed in our experiments. We study a different notion of surrogacy, propose an evaluation framework instead of a single map, relax unconfoundedness, and establish when maps generalize to unseen treatments, whereas SI literature mostly considers a single binary treatment. The causal surrogate map's estimand and IV estimators are well-known and cited (App. A.1). Our claims are its optimality for individual surrogacy (Theorem 4) and its suboptimality under general confounding (Proposition 3). No direct effect is necessary for generalization of any map f(S,X)f(S,X) (App. A.5), we do not claim to generalize it. However, in our setting the Prentice criterion Y⊥A∣SY\perp A\mid S fails even without direct effect, since conditioning on SS opens the path A→S←U→YA\to S\leftarrow U\to Y. SI-style literature thus relies on a stricter statistical assumption, and Assumption 3 needs mediation only through the whole surrogate vector, not a scalar endpoint.

W5. New treatments. "Evaluation is only valid for treatments already observed in the population study" is incorrect. Generalization to new treatments is one of our main contributions: Theorem 2 gives explicit conditions under which our evaluation transfers to unseen treatments. Even for fully mediated treatments this is highly nontrivial. To the best of our knowledge, existing (population-level) surrogacy literature gives no such guarantees, assuming the same treatment for learning and deployment. Our result does not restrict the surrogate mechanism g0(a,⋅)g_0(a,\cdot) of the new treatment and only requires sufficiently diverse surrogate response pairs at evaluation. The revision states Theorem 2 in the main text.

Ethics flag. The reviewer names no concern. If the reviewer states one, we will address it.

Reviewer_qJznOpenReview ↗
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Paper summary

This paper addresses the challenge of making personalized, individual-level treatment decisions (N-of-1 studies) when the primary long-term health outcome is delayed, costly, or only observed once.

Critical strengths
  1. Significant research in the field of health and medicine.
  2. Clear presentation in experimental parts.
Critical weaknesses

see questions.

Questions for authors
  • In this article, population observation data is used to construct pseudo outcomes to evaluate individual regret, and pseudo outcomes based on outcome regression are used. Has the author compared other strategies for constructing pseudo outcomes?
  • Is regular correction used for the estimation method used to fit Cox in the article? What is the computational cost of this module throughout the entire experimental pipeline?
  • This article uses the discrete changes of six daily activity indicators (step count, walking/running distance, exercise duration, standing duration, activity consumption, and number of floors climbed) as intervention labels. What is the basis for selecting daily activity indicators and substitute vectors based on the standardized changes within the window of six wearable biomarkers: resting heart rate, heart rate variability, maximum oxygen uptake, walking heart rate, 6-minute walking distance, and walking speed? Are these only a few items in the data or have feature filtering been performed, and then these daily activity indicators and alternative vectors were selected?
3 comments

We thank the reviewer for their review and address all questions below.

Q1. Other strategies for constructing pseudo-outcomes. The form of the pseudo-outcome is fixed by the identification result. Theorem 1 shows that the subject's label equals the regression Eobs[Y∣A=a,X,S]\mathbb{E}^{\mathrm{obs}}[Y \mid A=a,X,S] evaluated at the subject's own treatment, covariates and response (or averaged over the subject's responses to the same treatment in the more general case, see G1 of our general response). What can vary is the estimator of that regression. In our synthetic study, we compare three such estimators: a pooled probit, a quadratic probit and gradient boosting (Figs. 2, 6 and 8). In Proposition 1, we bound the error of the regret by the error of the regression estimator uniformly over surrogate maps, so any consistent regression method can be used (however, if it is misspecified, the pseudo-regret will be generally biased, as we observe in Fig. 2). Weighting-based or doubly robust pseudo-outcomes target effects averaged over people with the same covariates, and thus could not be used in our setting, since this could mix together different latent types UU, and the label would stop being truly individual-level.

Q2. Regularization of the Cox model and its cost. The Cox model is L2-penalized. The penalty is chosen by 5-fold cross-validation of the partial likelihood within the sample used to fit it (see App. A.9.3). The penalized linear predictor is used directly as the label, with no further correction (however, treatment-independent terms corresponding to covariates (β⊤X\beta^\top X) cancel out in every treatment contrast). The fit is a convex problem with a low-dimensional linear predictor, on at most 45% of the eligible cohort (about 14,000 participants) per rotation. A single penalized Cox fit (with the lifelines library in python) takes about 0.1-0.3s on a laptop CPU. We consider 6 treatments for evaluation and use 20 rotations with a 5-fold CV in every rotation. This results in a total of 600 pseudo-outcome model fits, and thus about 60-180s. The computational cost is (number of treatments)x(number of rotations)x(number of CV folds)x(cost of 1 Cox fit). The cost of imputing the labels is one evaluation of the linear predictor per window.

Q3. Choice of activity metrics and biomarkers. Both sets were fixed in advance, and no outcome-based feature selection was performed. The six activity metrics are the daily activity summaries recorded by the wearable device, and they describe behaviour a person can change, which makes them natural treatment labels. The six biomarkers are the common wearable biomarkers the device derives routinely. A window enters the analysis if at least one activity metric and every biomarker have measurements in its baseline and follow-up periods (App. A.9.1). The PPG dimension reduction is completely unsupervised: the PPG embeddings go from 256 to 20 dimensions by PCA, without using the outcome (App. A.9.2). In the revision, we emphasize this more clearly.

Thank you for the response. I have certain concerns.

In Section 5, it mentions that "As treatment labels for each window, we consider discretized within-window changes in one of the six daily activity metrics (step count, walking/running distance, exercise time, stand time, active energy burned, flights climbed)." What is the basis for considering these six daily activity indicators? What are the reasons why non-activity indicators such as sleep time are not included in the consideration criteria? Additionally, there is a clear multicollinearity among the six indicators mentioned above. What impact does this have on the evaluation of subsequent results?

In equation (3), when calculating regret, it first weights the treatment pairs and then weights the individuals. Why not directly weight the individuals? What impact do these two methods have on your subsequent analysis?

Thank you for your questions. For the analysis, we built a cohort in which every subject contains at least some data from all activity metrics and all considered surrogate quantities, to avoid subpopulation shift effects due to analyzing different cohorts for each treatment. Thus, we had to select activity and surrogate metrics which were measured in a large part of the study cohort simultaneously. This excluded metrics like sleep which restricted the cohort greatly (since many subjects do not wear the watch to sleep) and other actively logged metrics like weight, since only few subjects regularly log it. The remaining metrics are measured passively on many versions of the device and do not require wearing the watch to sleep, resulting in many measurements in most of the subjects. The same cohort filtering logic was applied to the surrogate metrics. Importantly, the selection of both the activity and surrogate metrics was done without access to any outcome data, and before any evaluation, based purely on the resulting cohort size.

We agree that the six considered activity metrics are correlated. Indeed, we conducted a separate evaluation where we performed PCA in the treatment space and extracted 6 uncorrelated "treatment directions". Each subject then received orthogonalized treatment labels (such as PC5 +1, a significant increase in PC5) instead of the original labels. We found that the resulting pseudo-regret was very close to the raw labels, and the surrogate map ranking was the same. For clarity of the presentation, we thus show the analysis for raw labels only.

In equation (3), we do not want to give greater weight to individuals which have a larger set of attempted treatments, since this could lead to bias (subjects who have tried more treatments contribute more to the total regret). For population-level evaluation, which aims to estimate how good the surrogate map will be on some new N-of-1 subject (without prior knowledge of which subject this will be), each evaluation subject should be weighted equally. Averaging first over pairs and then over subjects ensures that each individual-level regret counts equally independently of ∣Aj∣|\mathcal{A}^j|.

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Paper summary

This paper studies the use of surrogate maps for individual-level treatment decisions in N-of-1 settings, where individuals can try multiple treatments and observe their short-term responses, but their long term outcomes remain unavailable. The paper proposes a framework that uses individuals' observed responses to different treatments to identify which option is best for them. The authors propose evaluating surrogate measures based on the regret of the treatment rankings they induce, rather than their predictive accuracy or ability to estimate average treatment effects. By combining repeated individual-level experiments with population data containing long-term outcomes, they establish conditions under which individual treatment regret can be identified and estimated, and examine how surrogate measures can generalize to previously unseen treatments. The framework is further evaluated through simulations and data from the Apple Heart and Movement Study.

Critical strengths
  1. The paper formulates a relatively underexplored setting for individualized treatment decisions.

Most existing work on individualized treatment rules considers policies that select treatments based on pretreatment covariates X. In contrast, this paper considers a different information structure: the individual has already experienced multiple treatments, and the policy can leverage the observed treatment-specific surrogate responses S(a) in addition to X to determine which treatment is preferable.

This distinction is meaningful because the observed responses can potentially capture individual heterogeneity that cannot be explained by pretreatment covariates alone. I consider the formulation of this problem an important conceptual contribution.

  1. The idea of generalization to previously unseen treatments is interesting.

Another interesting idea in the paper is how the authors generalize to treatments that are not observed in the population-level outcome dataset. In many personalized decision problems, new interventions may become available without corresponding long-term outcome data.

Theorem 2 provides a theoretical result on this problem by identifying conditions under which low evaluation-time surrogate regret implies low regret for unseen treatments. In particular, the result characterizes generalization through the distribution of surrogate-response pairs rather than requiring the same treatment identities to appear in both evaluation and deployment.

Critical weaknesses
  1. The main identification results are solely driven by a highly restrictive structural assumption.

The identification results in Theorems 1 build on the invertibility assumption, which is essentially enabled by the assumption S = g_0(A, X, U). The implicit assumption here is that the mapping from A, X, U to S is deterministic and injective, without random error. However, in the structural equations for Y and A, random errors are allowed. So if we modify this equation to a more general case with S = g_0(A, X, U, ε_S), then invertibility will no longer necessarily hold, and we cannot identify the results in general. The authors discuss this briefly in Appendix A.8.5, but the analysis is limited to a particular form of errors and does not apply to a more general identification framework.

While I agree some structural assumption is needed for identification, this one appears largely tailored mechanically and arbitrarily to make the identification problem tractable rather than grounded in a convincing argument. I am not convinced that the paper adequately motivates why such a strong assumption should hold in applications.

  1. The framing overstates their contribution from CATE-based policy learning.

The paper emphasizes that CATE-based individualized treatment rules may be insufficient for identifying the best treatment for a particular individual. While I agree with this motivation, I find the interpretation of the paper's individual-level identification contribution overstated than what the proposed estimand establishes.

In Section 2.2, the authors define the subject-specific outcome label as μ^j(a) = E_j[Y^j(a)], which is subsequently identified through the conditional outcome regression E^obs[Y | A = a, X = X^j, S = S^j(a)].

Therefore, the identification strategy still relies on using population-level observations to infer the expected outcome for an individual with the same treatment, covariates, and surrogate response. This is not identical to standard CATE estimation based only on pretreatment covariates. However, the paper should not overclaim its contributions: the paper introduces a new decision problem that leverages individual-specific treatment responses, rather than identifying causal effects at the individual level.

Questions for authors
  1. The main identification result relies on the deterministic surrogate-generating mechanism S = g_0(A, X, U) and the invertibility assumption. Could the authors consider relaxing this assumption and allowing for partial-identification results instead?

  2. Why is a separate surrogate map necessary when long-term outcome data are available? Under the paper's conditional random assignment assumption and given the available data, one can directly estimate m(a, x, s) = E[Y | A = a, X = x, S = s] from the observational data and use it to select the best treatment for an individual after observing their surrogate responses. This seems more reasonable than learning a separate surrogate map f(S, X) if the goal is not to generalize to new treatments. How would the authors justify their method in this case?

  3. I would appreciate a more detailed discussion of the relationship between this framework and the policy-learning literature, such as Yang et al. (2024), Targeting for Long-Term Outcomes, where they also use the similar idea of ranking conditions to identify optimal policies.

1 comment

We thank the reviewer for the careful reading and the appreciation of our results, including Theorem 2. The questions and suggestions have led to concrete changes in the manuscript. Please refer to G1–G3 in our general response.

W1. The deterministic mechanism S=g0(A,X,U)S = g_0(A, X, U). We agree that a noise-free surrogate response is not required. The revision states Assumption 2 for the proposed form S:=g0(A,X,U,ϵS)S := g_0(A, X, U, \epsilon_S). Theorem 1 holds with the pseudo-outcome averaged over the subject's responses to the same treatment (G1). The assumption is not arbitrary (G2): it formalizes the premise, named as one of the strengths, that a subject's surrogate responses carry additional information about the individual which covariates do not.

Q1. Partial identification. Yes, see G3: any label bias that is constant within a subject cancels when two surrogate maps are compared. Otherwise, similarly to classical sensitivity analysis, each comparison has a breakdown value quantifying how large the bias would have to be to flip the comparison.

W2. Framing relative to CATE-based policy learning. We agree that our setting constitutes a new decision problem (cf. Strength 1), and view it as distinct from CATE-based policy learning, which asks which treatment an individual with covariates xx should receive before any treatment is administered, for a fixed collection of treatments with outcome data. First, in our setting the decision is made after the subject has been exposed to several treatments, and can thus use their own post-treatment responses Sj(a)S^j(a), which carry information (e.g., "responder" or "non-responder" type) that pre-treatment covariates do not. Second, the object of interest is a surrogate map f(S,X)f(S, X), which does not depend on the treatment, since it is meant for new treatments without long-term outcome data. Third, we do not estimate a predefined effect, but evaluate arbitrary surrogate maps via the regret of their induced rankings and transfer this evaluation to unseen treatments (Theorem 2).

Lastly, our pseudo-labels may resemble CATE-based learning with (X,S)(X, S) as covariates. With m(a,x,s)m(a,x,s) as in the reviewer's Q2, treating SS as a covariate yields the contrast m(a,x,s)−m(a′,x,s)m(a,x,s) - m(a',x,s) at a common, fixed ss. Since SS is a post-treatment variable, the units with S=sS = s under aa and under a′a' generally have different latent types, and this contrast compares different individuals. Our pseudo-label instead evaluates each treatment at the subject's own potential surrogate responses, m(a,Xj,Sj(a))−m(a′,Xj,Sj(a′))m(a,X^j,S^j(a)) - m(a',X^j,S^j(a')). We can condition on these potential surrogate responses only because they are observed in the N-of-1 design. In an observational study, they are unobservable cross-world quantities.

Q2. Why a surrogate map when m(a,x,s)m(a, x, s) can be estimated? If outcome data is available for treatments a,a′a,a', we agree: m(a,x,s)m(a,x,s) is sufficient to rank them correctly on the individual level. A surrogate map is needed precisely when no long-term data is available for the treatment, i.e., when it is novel. New treatments are our primary application of interest, which necessitates learning f(S,X)f(S,X) as opposed to some f(A,S,X)f(A,S,X): an individual's treatment is almost never an exact copy of something observed in the population study, as the dose or routine is always at least slightly different. Fixed surrogate endpoints (e.g., LDL cholesterol) are already used in this way, e.g., to assess a new drug. Our framework evaluates both learned maps and such fixed endpoints, with treatment-independent generalization to unseen treatments (Theorem 2).

Q3. Relation to Yang et al. (2024). We thank the reviewer for the reference (added to App. A.1). Yang et al. assume statistical (Prentice) surrogacy, impute long-term outcomes with a surrogate index, and learn a targeting policy on the imputed outcomes. They show that the conditions for effect estimation can be relaxed for policy optimization, which is close in spirit to our regret: it needs a correct ordering of treatments instead of accurate effect sizes. However, first, their policy assigns a treatment from pre-treatment covariates, while ours ranks treatments by the individual's responses in the N-of-1 design. Second, their policy is evaluated by its value in the population, whereas our regret is computed within each subject, even for just one individual. Finally, our setting generalizes statistical surrogacy (G1) and allows for certain types of confounding: as Example 2 shows, the same surrogate index can order treatments correctly on average yet misrank them on the individual level, so the two regrets measure fundamentally different quantities.

We thank the reviewer again. The comments on Assumption 2 and the framing improved our manuscript.

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