- Rating
- 3
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 3
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Paper summary
The paper proposes a foundation model for causal inference with longitudinal data, focusing on estimating conditional average potential outcomes under static and dynamic treatment policies. Its central identification strategy relies on sequential ignorability conditional on observed histories, together with consistency and positivity. The proposed approach combines a policy-demonstration representation with synthetic pretraining to enable estimation across datasets, policies, and horizons without task-specific retraining.
Critical strengths
Developing foundation models for causal inference is a valuable and promising research direction. The paper extends this approach to longitudinal settings, where evaluating multiple treatment policies and intervention horizons can be computationally demanding. The ability to reuse a pretrained model without fitting a separate model for each downstream task could be useful in practice, particularly for applications requiring repeated policy evaluation.
The proposed method offers an appealing connection between the statistical formulation of causal inference and machine learning. Representing a policy through its decisions on factual histories provides a unified way to supply policy information to the model. Proposition 3.1 gives a useful population-level justification for this representation: under the stated assumptions, the policy-demonstration distributions, together with the observational distribution, identify the target conditional average potential outcome. This connection strengthens the motivation for the proposed learning framework.
Critical weaknesses
Difference-in-differences (DiD) and synthetic control are among the most widely used approaches to causal inference with panel data. However, the proposed framework does not appear to encompass these approaches under their usual identifying assumptions; its identification argument instead relies on sequential ignorability. Consequently, the model’s generality appears to be primarily across datasets, policies, and horizons within a particular identification framework, rather than across panel-data causal inference more broadly. In this respect, the model is less “foundational” than I would expect from the paper’s framing. The authors should clarify the intended scope and discuss whether these important settings can be accommodated or remain outside the proposed framework.
The empirical evaluation is relatively narrow and does not fully substantiate the claimed ability to accommodate policies with different underlying functional forms. In particular, the main dynamic-policy benchmarks vary a scalar perturbation of the behavior-policy rule, rather than evaluating substantially different history-dependent decision rules. These experiments provide evidence of performance across related policy variants, but less evidence of generalization across qualitatively different policy families. A broader evaluation involving more diverse dynamic policies would make this central claim more convincing.
Questions for authors
Could the authors provide a clearer explanation of the uncertainty intervals and their intended statistical interpretation? In particular, do the intervals capture variability in individual counterfactual outcomes, uncertainty in estimating their conditional means, or both? The paper notes that these intervals should not be interpreted as credible intervals for CAPO, while evaluating their empirical coverage against the true CAPO. How should readers interpret the nominal interval levels and the resulting calibration analysis?
Would it be possible to develop a formal sensitivity analysis for violations of sequential ignorability? For example, could users specify the strength of unobserved confounding and assess how their estimated causal quantities or substantive conclusions would change? A discussion of how such an analysis could be incorporated into the proposed framework would help clarify its practical usefulness when the identifying assumption is questionable.
3 comments
Q1 We thank the reviewer for highlighting the need to clarify the statistical interpretation of our intervals. The original model’s predictive intervals capture both outcome variability and uncertainty about conditional means. Their coverage of true CAPO therefore does not directly establish calibration of CAPO uncertainty. We have revised the abstract, introduction, and results discussion to describe our findings as improved uncertainty characterization, supported by empirical CAPO coverage substantially closer to nominal levels than the baseline, rather than calibrated CAPO uncertainty.
To better align supervision with CAPO, we add 12 hours of second-stage pretraining after the initial 36 hours, replacing each single-draw target with the average of 10 independent counterfactual rollouts under the same sampled SCM and conditioning history. The two-stage procedure combines computationally efficient initial pretraining with subsequent training on targets more concentrated around CAPO. The resulting intervals approximate uncertainty about CAPO while retaining residual Monte Carlo variability from the finite number of rollouts.
We have updated the main benchmarks, coverage analysis, and ablations using this checkpoint, with comparisons to the original checkpoint in Appendix G. Point-estimation RMSE remains nearly unchanged (Figure S.4), while intervals become narrower (Figure S.5). At the nominal 95% level, empirical CAPO coverage is 88–93% on MIMIC-Y1 and 93–94% on MIMIC-1T across horizons, still substantially closer to nominal coverage than IGC-Net (Figure 4). These results support tighter intervals with strong empirical CAPO coverage and preserved point-estimation accuracy. This finding suggests that PICLE-PFN’s predictive intervals provide a useful characterization of uncertainty in CAPO estimation.
Q2 We thank the reviewer for this suggestion. A recent study [7] develops formal sensitivity bounds for average potential outcomes under violation of sequential ignorability, allowing users to specify the strength of unmeasured confounding (UC). These bounds can help assess whether substantive conclusions remain unchanged under the specified degree of confounding.
Incorporating this approach into PICLE-PFN is a promising direction. It would require estimating treatment propensity scores at each time step and implementing the associated sensitivity-bound optimization (Proposition 1 in [7]), beyond the outcome modeling provided by our current framework. Separate propensity models could supply the treatment probabilities, but adapting and validating the bound computation for our amortized CAPO estimation setting would require additional methodological development. We therefore leave this extension to future work.
As a complementary empirical assessment, we conduct two additional studies. The original submission considered a time-invariant UC under a static treatment sequence. Here, we evaluate a dynamic treatment policy, considering both time-invariant and time-varying UCs (Details see Appendix D.7). We compare PICLE-PFN with the two strongest baselines supporting dynamic treatment policies and report mean ± SD of RMSE across 20 repetitions.
(1) Time-invariant UC. , and the fixed enters the treatment logit as and the outcome as at every time step.
| PICLE-PFN | IGC-Net | D3 | |
|---|---|---|---|
| 0 | 0.363 ± 0.100 | 0.372 ± 0.097 | 0.381 ± 0.099 |
| 1 | 0.354 ± 0.098 | 0.363 ± 0.092 | 0.374 ± 0.096 |
| 2 | 0.355 ± 0.092 | 0.362 ± 0.091 | 0.380 ± 0.089 |
| 4 | 0.346 ± 0.084 | 0.359 ± 0.079 | 0.381 ± 0.080 |
(2) Time-varying UC. . The time-varying enters the treatment logit as and the outcome as at every time step.
| PICLE-PFN | IGC-Net | D3 | |
|---|---|---|---|
| 0 | 0.363 ± 0.100 | 0.372 ± 0.097 | 0.381 ± 0.099 |
| 1 | 0.488 ± 0.060 | 0.485 ± 0.064 | 0.527 ± 0.062 |
| 2 | 0.499 ± 0.053 | 0.503 ± 0.065 | 0.513 ± 0.049 |
| 4 | 0.524 ± 0.047 | 0.528 ± 0.068 | 0.531 ± 0.040 |
All methods exhibit relatively stable performance across confounding strengths in the time-invariant setting, whereas time-varying confounding increases RMSE for all methods. PICLE-PFN achieves the lowest mean RMSE in 7 out of 8 configurations, including all strong-confounding settings, maintaining its relative performance advantage under the evaluated violations of sequential ignorability.
[7] Tan, Zhiqiang. "Sensitivity models and bounds under sequential unmeasured confounding in longitudinal studies." Biometrika 112.1 (2025): asae044.
Thank you for the detailed clarifications and additional experiments. The revised scope and evaluations of qualitatively different dynamic policies substantially address my main concerns. I also appreciate the additional pretraining and the more cautious interpretation of uncertainty. The intervals still retain rollout variability, and reported CAPO coverage remains below nominal, so these limitations should remain explicit. The confounding experiments provide useful empirical assessments, with formal sensitivity analysis remaining an important extension. Overall, the response strengthens the paper, and I will maintain my rating of weak acceptance.
W1 We thank the reviewer for the suggestion to clarify our scope. Indeed, our method aims to amortize CAPO estimation across datasets, policies, and horizons within the sequential backdoor adjustment framework, and does not intend to encompass all identification strategies for causal effect estimation on panel data. To make the scope explicit, we have revised the abstract (line 21) and introduction (line 74), in addition to the stated identifying assumption in Section 3.
DiD and synthetic control (SC) offer alternative identification strategies for panel data, and extensions such as Synthetic Blips [4] also accommodate sequential treatments. However, their identifying assumptions differ from those underlying PICLE-PFN. DiD relies on parallel-trends assumptions, potentially conditional on covariates [1], and the compatibility of parallel-trends assumptions with dynamic treatment policies requires careful consideration [2,3]. SC typically adopts latent-factor approaches to exploit additional structure across units and time [4–6]. These approaches can accommodate certain forms of unobserved confounding that are outside our sequential-ignorability framework. Extending PICLE-PFN to these settings would require establishing identification of the target estimands under the alternative assumptions and developing corresponding pretraining formulations and input representations. Such extensions remain outside the present study.
[1] Caetano, Carolina, et al. "Difference in differences with time-varying covariates." arXiv preprint arXiv:2202.02903 (2022).
[2] Stéphane Bonhomme, Back to feedback: dynamics and heterogeneity in panel data, The Econometrics Journal, 2026, utag027
[3] Marx, Philip, Elie Tamer, and Xun Tang. "Parallel trends and dynamic choices." Journal of Political Economy Microeconomics 2.1 (2024): 129-171.
[4] Agarwal, Anish, et al. "Synthetic Blips: Generalizing Synthetic Controls for Dynamic Treatment Effects." arXiv preprint arXiv:2210.11003 (2022).
[5] Arkhangelsky, Dmitry, and David Hirshberg. "Large-sample properties of the synthetic control method under selection on unobservables." arXiv preprint arXiv:2311.13575 (2023).
[6] Imbens, Guido W., and Davide Viviano. "Identification and inference for synthetic controls with confounding." arXiv preprint arXiv:2312.00955 (2023).
W2 We thank the reviewer for suggesting broader evaluations of policies with different underlying functional forms. We expand our evaluation to three dynamic policies that use qualitatively different history-dependent policy families, rather than scalar perturbations of the behavioral policy. These policies incorporate treatment history, outcome trends, and combinations of patient characteristics (definition details in Appendix D.8):
Deterioration: At step t, if the patient was not treated at t-1, start treatment if the target outcome increases relative to the previous step (deterioration); once treated, continue treatment.
Response-guided: At each step t, if the patient was not treated at t-1, start treatment when heart rate exceeds its 75th percentile; if the patient was treated at t-1, continue treatment while the target outcome is decreasing relative to the previous step, and stop it otherwise.
Tree: At each step t, treat if the target outcome increased relative to the previous step and the patient is older than the cohort median age, or if heart rate exceeds its 90th percentile; otherwise do not treat.
We compare PICLE-PFN with IGC-Net and D3, the two strongest baselines in our evaluation that support dynamic policies, across horizons of 2/4/6/8/10 with 20 repetitions. The table below summarizes RMSE averaged across horizons; detailed results for individual horizons are provided in Table 6.
PICLE-PFN achieves the lowest mean normalized RMSE at every evaluated horizon under both the deterioration and response-guided policies. Under the tree policy, the ranking varies across horizons, but PICLE-PFN achieves the lowest mean normalized RMSE aggregated across horizons. These results provide additional evidence that PICLE-PFN generalizes beyond scalar perturbations of the behavioral policy to diverse policies with different underlying functional forms.