A Unified Framework for the Transportability of Population-Level Causal Measures

Thank you for your thoughtful and constructive review. We are glad that you found the contributions of the paper valuable and the exposition clear.

Regarding your comment on small or moderate sample sizes: while our theoretical results are asymptotic, the methodology itself is not restricted to large samples. In practice, when RCT data is limited and nuisance functions (e.g., outcome or propensity models) must be estimated from this same limited data, a pragmatic approach would be to use parametric models to reduce variance and mitigate overfitting.

To assess finite-sample behaviour empirically, we conducted simulations with total sample size $N = 5000$ and $500$, of which respectively 1,500 and 150 for the RCT group. The results in Figure 4 (first table) correspond to the setting under exchangeability in mean, and those in Figure 2 (second table) to the setting under exchangeability in effect measure. Across both settings, the Estimating-equation estimator—whether standard or Γ-adjusted—shows the best empirical performance, achieving the lowest combination of bias and variance across RD, RR, and OR. While in some specific cases it may be marginally outperformed by a G-formula or a One-step estimator, the Estimating-equation remains doubly robust, offering consistent performance even under model misspecification. For this reason, we strongly recommend its use in practice, particularly when nuisance functions are estimated from limited data.

That said, we agree that further exploration of finite-sample properties would be valuable. In particular, understanding how the sizes of both the source (RCT) and target populations affect the performance of different estimators—especially those based on efficient influence functions—is a promising direction for future research. We have added a sentence to the conclusion to reflect this.

N=5000

N=500

We thank you for your carefull review. We will fix the several typos you pointed out.

Covariate Non-Overlap Between Source and Target Populations

The overlap assumption is critical for identifying causal effects in a target population. It requires that for any covariate pattern present in the target population, there is sufficient representation in the trial population ($P(S = 1 | X = x) > 0$). When this assumption is violated—i.e., when the observed covariates are not fully overlapping between training (RCT) and target populations—standard identification results no longer hold, and estimators proposed in the paper may become biased or unstable due to extreme or poorly estimated weights.

There are two main strategies to address this:

1. Restricting the target population: One approach is to redefine the generalization target to individuals in the target population who are within the support of the RCT sample—that is, those who could plausibly have been enrolled in the RCT. This amounts to generalizing the effect only to the subpopulation with overlapping covariates, thereby restoring identifiability at the cost of external validity (the target population has changed).

2. Performing sensitivity analyses: An alternative is to formally account for violations of overlap through sensitivity analyses, which quantify the robustness of conclusions under deviations from the assumption. See for instance Huang (2025) for recent developments in this direction.

Unobserved Shifting Covariates

If unobserved covariates drive differences in outcome distributions between the source and target populations, the assumption of exchangeability in mean is violated, undermining identification based on outcome modeling. In such cases, a weaker but potentially more realistic assumption—exchangeability in the effect measure—can still hold. Indeed, if the unobserved covariates influence only the outcome level but not the treatment effect heterogeneity, transportability of the effect measure is still possible. However, identification under this assumption requires access to control outcomes in the target population, which may not be feasible in many scenarios. If shifted treatment effect modifiers are not observed, then, this boils down to an identifiability issue and consequently, one has to resort to traditional methods to give bounds on treatment effects, for instance using sensitivity analysis. We added a paragraph in the discussion section on limitations, and the verification of assumptions.

Scalability of Estimators with Increasing Covariate Dimensions

It’s true that the example uses only six covariates, but this reflects the limited data collected in the clinical trial. In randomized trials, covariates are often less critical, since treatment effects can be estimated directly by comparing average outcomes between treated and control groups. The six covariates used are those shared between the trial and observational data, and which show distributional differences across the two datasets.

That said, there’s no theoretical limitation on the number of covariates. The estimators rely on the estimation of nuisance functions—such as regressions of $Y$ on $X$—which can be modeled using parametric (e.g., linear regression) or nonparametric methods (e.g., random forests). When using g-formula-type estimators, more data is required as the number of covariates increases, especially with nonparametric methods due to slower convergence rates. However, doubly robust estimators can recover parametric convergence rates even in high-dimensional settings.

Weaknesses

1. "The introduction is difficult to follow. Several concepts are not properly introduced, e.g.: l27 the risk difference is introduced with no definition or assumptions on the setting (binary outcome?). l54-55 'collapsible and not collapsible measures' are not defined."

We thank the reviewer for this comment. We have revised the introduction for clarity and now explicitly define key concepts such as the risk difference and collapsible vs. non-collapsible measures, including references for further reading.

2. "Risk ratio assumes continuous outcome for interpretation, but I cannot find where/if assumed in Section 2. Similarly Odds ratio etc."

The risk ratio can be interpreted for both binary and continuous outcomes (as long as the outcome remains positive), while the odds ratio applies only to binary outcomes. Our results hold in the continuous and binary setting, which we have now clarified in Section 2.

3. "l110 m and n are DEPENDENT binomials (use multimodal distribution instead)."

We infer you meant multinomial and not multimodal. You are right , $(n, m)$ follow a multinomial distribution with parameter $N$ and probabilities $(\alpha, 1 - \alpha)$.

5. "Synthetic experiments are under-defined and no code is provided. How many covariates are considered (d)? What are the source values in Figure 1 caption?"

Thank you for the feedback. We now also provide a link to the experimental code for reproducibility. We have updated the experiments section to clarify that:

• The number of covariates (d) is 5, consistent with real-world RCTs that often involve few covariates.
• The source value in Figure 1 denotes the true treatment effect in the source population, shown to illustrate the shift in effect when applied to the target population.

Clarification on discrepancy in the messages in the real experiments

Thank you for this comment. We have clarified the real data analysis in the revised manuscript. While the RCT analysis (not included in the paper; see Colnet et al., 2024) suggested a slightly positive effect of the treatment, the estimators applied to the target population suggest a slightly deleterious—but non-significant—effect. This discrepancy is expected due to differences in the underlying populations: the RCT population differs from the target population used in generalization.

All causal estimators applied to the target population—whether based on generalizing from the RCT or using purely observational data—converge on the same conclusion: a non-significant effect in the Traumabase cohort. As you rightly point out, the true effect is unknown. However, because we observe outcomes in the target population, it is possible to directly estimate treatment effects from the observational data (Mayer et al., 2020). While this relies on different assumptions—particularly, the absence of unmeasured confounding—it is reassuring that both approaches (generalization from RCT and causal inference from observational data) lead to the same conclusion. This is true for the risk difference as well as relative measures (Boughdiri et al., 2025).

In addition, if one suspects that some identifiability assumptions are not met, it is possible to resort to sensitivity analysis.

Position with Colnet et al. (2023)

We thank the reviewer for this comment and appreciate the opportunity to clarify the novelty and scope of our contributions relative to prior work, particularly to Colnet et al. (2023).

While Colnet et al. (2023) explores identification strategies for causal estimands—most notably the risk ratio and the risk difference—in the context of generalization, our work extends the identification and estimation landscape in several important directions:

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1. Unified Framework for Transportability

We introduce a general identification and estimation framework for transporting a broad class of first-moment causal estimands—including more than a dozen measures, both collapsible (e.g., RD, RR) and non-collapsible (e.g., OR)—across covariate shifts. Specifically:

• Under exchangeability in mean, we recover and extend existing identification results and derive asymptotic properties for all proposed estimators. For instance, under a logistic selection and linear outcome model, we show that the transported G-formula is asymptotically more efficient than the Horvitz–Thompson estimator.

• Under exchangeability in effect measure, a strictly weaker assumption, we provide a different result from Colnet, which is more general to cover any first-moment causal estimand, including non-collapsible ones like the odds ratio (OR). To our knowledge, these are novel identification results in the generalization context and are especially relevant given the widespread use of the OR in applied research.

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2. New Estimators for Transported Estimands

Whereas Colnet et al. focused on identification we propose new estimators designed for generalization from randomized trials, including:

• Semiparametric efficient estimators (one-step and estimating equation), and we demonstrate that their behavior diverges for nonlinear estimands such as RR and OR—a key theoretical and empirical contribution. Notably, we show that the estimating equation (EE) estimator is doubly robust for any causal measure (unlike the one-step estimator), and consistently outperforms it empirically. This difference had not been previously emphasized in the literature.

• Γ-formula estimators under exchangeability in effect measure, which are, to our knowledge, novel contributions, especially in the context of generalizing non-collapsible estimands.

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3. Complementary Goals to Prior Work

While Colnet et al. emphasize which causal estimands are easier to identify and generalize, our work offers a unified framework that supports the generalization of all first-moment causal measures, with a strong focus on estimation strategies and efficiency (which allows practical deployment of such methods with theoretical guarantees in contrats to their work). Their focus is on separating treatment effect from baseline; our focus reveals how many estimands share a common structure, enabling unified treatment in both identification and estimation. We see these as complementary contributions but different that together helps the understanding of causal transportability.

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4. Relevance to NeurIPS

Although we agree that real-world validation is valuable, our primary goal is to offer a principled, broadly applicable framework for researchers and practitioners at the interface of machine learning, statistics, and application. Specifically, our use of influence functions, robustness analysis, and complex simulation designs (e.g., under model misspecification and nonlinear responses) directly targets challenges common in machine learning applications that require both generalizability and estimator efficiency.

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We hope to have convinced you that our contribution is both theoretical and methodological, encompassing a unified transportability framework and novel results at both the identification and estimation levels, especially for nonlinear estimands. We believe this goes well beyond a routine application or minor extension and is a strong fit for a generalist ML venue like NeurIPS. Furthermore, our framework is broadly applicable across domains—biostatistics, econometrics, and public policy—underscoring its potential impact.

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References

• Colnet, B., Mayer, I., Chen, G., Dieng, A., Li, R., Varoquaux, G., Vert, J.-P., Josse, J., & Yang, S. (2024). Causal Inference Methods for Combining Randomized Trials and Observational Studies: A Review. Statistical Science, 39(1), 165–191.

• Mayer, I., Sverdrup, E., Gauss, T., Moyer, J.-D., Wager, S., & Josse, J. (2020). Doubly robust treatment effect estimation with missing attributes. arXiv preprint

• Boughdiri, A., Josse, J., & Scornet, E. (2025). Quantifying Treatment Effects: Estimating Risk Ratios in Causal Inference. ICML2025

We are grateful for the reviewer’s positive remarks. In particular, we appreciate the recognition of our effort to present a unified causal framework that accommodates different effect measures and transportability assumptions. We aimed to make the methodology both general and practically accessible. We are encouraged that this structure was found to be clear and well-organized.

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Response to Comment on Exchangeability Assumptions and Applied Guidance

We thank the reviewer for this thoughtful and constructive comment. We fully agree that providing concrete examples and clearer practical guidance on when to prefer each assumption significantly improves the applied relevance of the work.

Applied Scenarios Where Exchangeability in Effect Measure Is Plausible

In pre-treatment settings, the intervention has not yet been introduced, so outcomes under usual care can be observed for all individuals. We are currently collaborating with an Inserm team to generalize the effect of paracetamol (acetaminophen) for preterm infants to prevent patent ductus arteriosus from the RCT TREOCAPA trial to 23 cohorts from the RECAP preterm project. In this setting, outcome data under the control condition are available for the cohorts, as the infants in these cohorts did not receive paracetamol. The aim is to predict the treatment effect across these different populations. These untreated cohorts provide high-quality data on clinically important outcomes—including survival without severe morbidity, defined as the absence of major complications such as bronchopulmonary dysplasia (BPD), necrotizing enterocolitis (NEC), severe intraventricular hemorrhage (IVH), and cystic periventricular leukomalacia (cPVL).

We have revised the discussion section to highlight a real-world setting in which control outcomes are available in the target population.

Understanding the Assumptions and Their Plausibility

We also clarify the structural differences between the two assumptions:

• Exchangeability in effect measure assumes that treatment effects are portable but requires access to control outcomes in the target population and access to shifted treatment effect modifiers.

• Exchangeability in mean, is stronger and assumes that conditional outcome models are stable across populations, but relies on shifted prognostic covariates.

To assess which assumption is plausible, it is possible to perform some statistical tests. To help practitioners we now include the following guidance:

• Model-based diagnostics: To test exchangeability in mean, one can regress the outcome on covariates and a study indicator. If the study coefficient is significant, it suggests the conditional mean function differs across populations (Robertson et al., 2021).

• Illustrative example: Suppose the potential outcomes in the source population follow

  $$\mathbb{E}_S[Y^{(a)} | X] = b(X) + a \cdot m(X),$$

  while in the target population they follow

  $$\mathbb{E}_T[Y^{(a)} | X] = \gamma + b(X) + a \cdot m(X).$$

  where $m(.)$ and $b(.)$ respectively correspond to the treatment effect and the baseline. The constant $\gamma$ modifies the baseline of the target population and may be due to the fact that the target population is more likely than the source population to undergo undesirable events, due to exogeneous variables whose information is not fully contained in the covariates $X$. In this case, the local effect of the Risk Difference can be generalized but the distribution of the potential outcomes cannot.

• Identifying effect modifiers is an ongoing research challenge, but recent methods (e.g., Hines et al., 2022; Benard et al., 2023; Paillard et al., 2025) provide tools for detecting covariates that drive treatment effect heterogeneity.

To conclude, the choice among different approaches often depends on data availability—particularly whether outcomes in the target population are accessible. When outcome data are available, both identification assumptions can be empirically tested. Close collaboration with clinicians is essential to develop a DAG and to identify key variables: those likely to act as shifted prognostic factors, and potential treatment effect modifiers. In the latter case, specific statistical tests can also be conducted to support the analysis.

We believe these additions help clarify when each assumption is likely to be valid and how practitioners can evaluate them in applied settings.

Estimator Recommendation

Regardless of which identification assumption is used, we recommend the corresponding estimating equation (EE) estimator (and not the one-step estimators): either the standard version (under exchangeability in mean) or the Γ-formula-based version (under exchangeability in effect measure). These estimators are doubly robust, providing consistent estimates if either the outcome model or the density ratio model is correctly specified. Our theoretical and empirical results show that EE estimators offer favorable bias–variance trade-offs under both assumptions.

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Clarification on Lemma 2: Positive Semi-Definiteness Argument

You're absolutely right that the expression

$$\mathbb{E}_T[VV^\top] - \mathbb{E}_T[VV^\top] \left( \mathbb{E}_T[\sigma(X,\beta) VV^\top] \right)^{-1} \mathbb{E}_T[VV^\top]$$

is not guaranteed to be PSD unless additional structural assumptions (e.g., $B \succeq A$) are imposed which does not hold in our setting. However, this can be easily solved. The second statement holds if the matrix H is symmetric and positive semidefinite. We can rewrite H up to a positive scaling factor as the regrouped form:

$$H := \mathbb{E}_T\left[\frac{1}{\sigma(X,\beta)} VV^\top\right] - \mathbb{E}_T[VV^\top] \left( \mathbb{E}_T[\sigma(X,\beta) VV^\top] \right)^{-1} \mathbb{E}_T[VV^\top].$$

Let us define:

• $A := \mathbb{E}_T[VV^\top]$,
• $B := \mathbb{E}_T[\sigma(X,\beta) VV^\top]$,
• $C := \mathbb{E}_T\left[\frac{1}{\sigma(X,\beta)} VV^\top\right]$.

Then we can write:

$$H = C - A B^{-1} A.$$

This expression is PSD if and only if the following block matrix is PSD (by the Schur complement condition):

$$M := \begin{bmatrix} C & A \\\\ A & B \end{bmatrix}.$$

Now observe that this matrix can be written as an expectation over rank-one PSD matrices:

$$M = \mathbb{E}_T[\tilde{V} \tilde{V}^\top],$$

where

$$\tilde{V}^T := \begin{bmatrix} \frac{1}{\sqrt{\sigma(X,\beta)}} V^T \\ \sqrt{\sigma(X,\beta)} V^T \end{bmatrix} \in \mathbb{R}^{2d}.$$

Since each outer product $\tilde{V} \tilde{V}^\top$ is PSD and expectations preserve positive semi-definiteness, it follows that $M \succeq 0$. By the Schur complement identity, this implies that $H = C - A B^{-1} A \succeq 0$ as well.

We have updated the manuscript to reflect this corrected structure and clarify the PSD argument. This correction ensures the validity of the key step used in Proposition 2.

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Clarification on Interpretation of Real-World Results

We agree that the phrase “little to no impact” was unclear. We have revised the sentence as follows:

All estimators (except one) indicate a positive treatment effect; however, the confidence intervals are wide and include the null value (zero or one), preventing any definitive conclusions about the treatment’s effectiveness.

This revised phrasing better captures the uncertainty in the estimates and avoids overinterpreting the results. We thank the reviewer for pointing this out.

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We thank the reviewer again for their feedback. We have addressed all raised concerns, including the clarification of Lemma 2, improved interpretation of the real-world results, and the addition of practical guidance and examples to support assumption selection. We believe these revisions substantially strengthen both the theoretical clarity and applied usability of the paper.

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References

• Hines, O., Diaz-Ordaz, K., & Vansteelandt, S. (2022). Variable importance measures for heterogeneous causal effects. arXiv preprint arXiv:2204.06030.
• Benard, C., & Josse, J. (2023). Variable importance for causal forests: breaking down the heterogeneity of treatment effects. arXiv preprint arXiv:2308.03369.
• Paillard, J., Reyero Lobo, A. D., Kolodyazhniy, V., Thirion, B., & Engemann, D. A. (2025). Measuring variable importance in heterogeneous treatment effects with confidence. ICML 2025.
• Robertson, S. E., Steingrimsson, J. A., Joyce, N. R., Stuart, E. A., & Dahabreh, I. J. (2021). Center-specific causal inference with multicenter trials: Reinterpreting trial evidence in the context of each participating center. arXiv preprint arXiv:2104.05905.