Pessimistic Data Integration for Policy Evaluation

Thank you for your thoughtful and critical assessment. Many of your comments will help us produce a more readable and self-contained version of the paper. Below, we address each of your specific concerns in turn.

• Improvement over the ATE. Thank you for the insightful comment. We respectfully clarify that the proposed estimator is designed to improve the mean squared error (MSE) of the standard ATE estimator by integrating experimental data with potentially large-sample historical data. The core idea of our method is to adaptively combine potentially biased but low-variance historical estimators with unbiased experimental estimators—striking a principled balance between bias and variance in finite-sample settings. This leads to consistently improved performance across a broad range of practical scenarios.

  • When the bias introduced by the historical data is small or negligible, the proposed estimator effectively leverages both datasets, benefiting from the larger sample size and achieving a smaller MSE compared to the experimental-data-only (EDO) estimator.

  • When the bias is moderate, our method balances bias and variance in a way that reduces overall MSE. Minimizing MSE—reflecting the fundamental trade-off between bias and variance—is widely recognized as a more practical and robust objective in real-world applications. While the proposed estimator may introduce some bias, it is carefully calibrated to ensure that the reduction in variance outweighs the increase in bias, particularly in settings with distributional heterogeneity between datasets.

  • When the bias is substantial, the learned weight on historical data approaches zero, causing the proposed estimator to behave similarly to the EDO estimator. This adaptive behavior ensures robustness even under significant posterior shifts.

  • As demonstrated in our toy example (Table 2 on Page 5), even a slightly biased estimator can outperform the standard ATE estimator significantly in terms of MSE. Our theoretical analysis rigorously characterizes this trade-off, and our empirical evaluations across diverse scenarios consistently show that the proposed method achieves near-oracle performance by effectively managing the bias–variance balance.

• Perform a characterization for when the EDO is optimal. We thank the reviewer for the helpful comment. Below, we provide a more detailed explanation of the conditions under which the EDO estimator tends to perform best.

  In Section 4 of the paper, we analyze five representative scenarios and formally characterize the settings where the experimental-data-only (EDO) estimator achieves the lowest mean squared error (MSE). These conditions are explicitly stated in:

  • Corollary 1 (Page 7): In the presence of heavy-tailed historical rewards, EDO becomes optimal because the high variability in historical data outweighs its variance-reducing benefit. Under mild regularity conditions, we show that the optimal weight function converges to 1, effectively defaulting to EDO.
  • Corollary 4 (Page 7): When there is moderate or large posterior shift between historical and experimental data (i.e., substantial discrepancies in conditional outcome distributions), our analysis demonstrates that the optimal weight again converges to 1. In such settings, incorporating biased historical data would result in significant estimation error, making EDO the preferred choice.

  In both cases, we derive upper bounds for the excess MSE of our proposed estimator relative to EDO, and prove that this excess is negligible under the specified conditions. These results demonstrate that the proposed method is adaptive: it defaults to EDO when EDO is indeed optimal.

Thank you again for your thoughtful review. We look forward to further discussion.

Thank you for your thoughtful and critical assessment. Many of your comments will help us produce a more readable and self-contained version of the paper. Below, we address each of your specific concerns in turn.

• Notation for $\mathbb{E}\_{n}$ . We use $\\mathbb{E}\_{n}$ to denote the empirical average computed over a dataset. To distinguish between different data sources, we let $\\mathbb{E}\_{n_e}$ and $\mathbb{E}\_{n_h}$ represent the empirical averages over the experimental and historical data, respectively.

• Theory concerns. We sincerely thank the reviewer for the insightful comments regarding the theoretical analysis. Upon revisiting the proof, we agree with the observation and have strengthened Assumption 1 to ensure uniform concentration guarantees. We also clarified the definition of $\text{MSE}(\hat{w})$ by explicitly treating it as a conditional expectation given $\hat{w}$. Based on these revisions, we provide a more rigorous proof of Theorem 1.

  • Revised Assumption1. Define the following events: \\begin{aligned} A &:= \\left\\{ \\widehat{\\text{bias}}_U(w) \\geq |\\text{bias}(w)| \\text{ for all } w \\in \\mathcal{W} \\right\\}, \\\\ B &:= \\left\\{ \\widehat{\\text{Var}}_U(w) \\geq \\text{Var}(w) \\text{ for all } w \\in \\mathcal{W} \\right\\}, \\\\ \\end{aligned}
  We assume, for some $\alpha \in (0,1)$, that $\mathbb{P}(A) \geq1 - \alpha$, $\mathbb{P}(B) \geq 1 - \alpha$. - **Clarify the definition of $\\text{MSE}(\\hat{w}) .$** We define $\text{MSE}(\hat{w})$ as a conditional expectation—once $\hat{w}$ is fixed, the expectation is taken over the remaining randomness. Thus, $\text{MSE}(\hat{w})$ is itself a random variable. The overall estimator's MSE is: $ \text{MSE}(\widehat{\text{ATE}}(\hat{w})) = \mathbb{E}\left[\text{MSE}(\hat{w})\right], $where the expectation is taken over the randomness of $ \hat{w} $. - **Proof of Theorem1**. We decompose the MSE difference into two parts based on whether the event $ C := A \\cap B $ holds: $$ \text{MSE}(\widehat{\text{ATE}}(\hat{w})) - \text{MSE}(\widehat{\text{ATE}}(w)) = M_1 + M_2, $$ where $ M_1 = \mathbb{E} \left[(\text{MSE}(\hat{w}) - \text{MSE}(w)) \cdot \mathbf{1}_{C } \right], $ and $ M_2 = \mathbb{E}\left[(\text{MSE}(\hat{w}) - \text{MSE}(w)) \cdot \mathbf{1}_{C ^c} \right]. $ For $M_1$, since $\hat{w}$ minimizes the pessimistic upper bound within event $C$, we have: $$ \mathrm{bias}^2(\hat{w}) + \mathrm{Var}(\hat{w}) \leq \widehat{\mathrm{bias}}_U^2(\hat{w}) + \widehat{\mathrm{Var}}_U(\hat{w}) \leq \widehat{\mathrm{bias}}_U^2(w) + \widehat{\mathrm{Var}}_U(w). $$ Thus, $$ M_1 \leq \mathbb{E} \left[ \left( \widehat{\text{bias}}_U^2(w) - \text{bias}^2(w) + \widehat{\text{Var}}_U(w) - \text{Var}(w) \right) \cdot \mathbf{1}_C \right] \leq \mathbb{E} \left[ \widehat{\text{bias}}_U^2(w) - \text{bias}^2(w) \right] + \mathbb{E} \left[ \widehat{\text{Var}}_U(w) - \text{Var}(w) \right]. $$ For $M_2$, we apply the triangle inequality and Assumption 2 to get $$ \text{MSE}(\hat{w}) = \mathbb{E}[(\widehat{\text{ATE}}(\hat{w}) - \text{ATE})^2] \leq \mathbb{E}[(|\widehat{\text{ATE}}(\hat{w})| + |\text{ATE}|)^2] \leq \mathcal{O}(B^2). $$ Similarly, we have $\text{MSE}(w) \leq \mathcal{O}(B^2)$ for any $w \in \mathcal{W}$. By the union bound on probabilities $\mathbb{P}(C^{c}) = \mathbb{P}(A^{c} \cup B^{c} ) \leq \mathbb{P}(A^{c}) + \mathbb{P}(B^{c}) \leq 2\alpha.$ Hence, we bound the term $M_2$ as: $$ M_2 = \mathbb{E}\left[(\text{MSE}(\hat{w}) - \text{MSE}(w)) \cdot \mathbf{1}_{C^c} \right] \leq 2B^2 \cdot \mathbb{P}(C^c) \leq \mathcal{O}(\alpha B^2). $$ Combining both parts yields the final bound $$ \text{MSE}(\widehat{\text{ATE}}(\hat{w})) - \text{MSE}(\widehat{\text{ATE}}(w)) \leq \mathbb{E} \left[ \widehat{\text{bias}}_U^2(w) - \text{bias}^2(w) \right] + \mathbb{E} \left[ \widehat{\text{Var}}_U(w) - \text{Var}(w) \right] + \mathcal{O}(\alpha B^2). $$

• Statistical inference. This is an excellent comment, and we fully agree on the importance of conducting valid inference in A/B testing, as A/B testing is essentially a statistical inference problem. Fortunately, when employing DR -- used in our numerical studies -- for ATE estimation, valid p-values can be readily obtained. We have conducted both theoretical analysis and empirical evaluations during the rebuttal to demonstrate this.

  • Specifically, when combined with sample-splitting -- using one half of the data to estimate the weight function $\widehat{w}$ and nuisance functions (the reward and density ratio), and the other half to construct the ATE estimator -- following Chernozhukov et al. (2018), one can show that the resulting ATE estimator is asymptotically normal under suitable regularity conditions (i.e., the reward and density ratio functions converge at certain rates).

  • As a result, standard $z$-tests with normal approximation can be used to obtain valid p-values. The only issue that may invalidate the p-value is the bias introduced through the incorporation of historical data. However, our proposed data integration procedure is explicitly designed to minimize MSE and control this bias. We elaborate on this below.

  • For a given $\widehat{w}$, the bias of the ATE estimator is given by $E(1-\widehat{w}(S^{(e)}))b(S^{(e)})$ where the expectation is taken over $S^{(e)}$. In the first three scenarios considered in our paper, the variance of the estimator dominates $b^2(s)$, so the bias $E(1-\widehat{w}(S^{(e)}))b(S^{(e)})$ is also negligible compared to the variance. This ensures the validity of p-values in these three scenarios. In the last two scenarios, $b^2(s)$ might dominate the variance. However, since our method is designed to minimize the MSE, the estimated weight function $\widehat{w}$ will converge to 1 to ensure the bias $E(1-\widehat{w}(S^{(e)}))b(S^{(e)})$ remains small. Our numerical studies presented below confirm this behavior: the bias is negligible in magnitude, and the resulting p-values remain valid across all scenarios.

• Additional simulation studies. For completeness, we conducted additional simulations to evaluate the finite-sample performance of hypothesis testing using the proposed estimator. Specifically, we consider the following hypothesis testing problem: $H_0: \text{ATE} = 0 \quad \text{vs.} \quad H_1: \text{ATE} \ne 0$.

  • To assess the performance of the EDO, Pessi, and Proposed methods, we first set the true ATE to 0 and perform 1,000 Monte Carlo simulations to estimate the Type I error rate of each method at the 5% significance level. Next, to evaluate the empirical power, we gradually increase the signal strength by setting the ATE to values in the set ${0.5,\ 1.0,\ 1.5,\ 2.0,\ 2.5,\ 3.0}$, and again conduct 1,000 simulations for each setting to compute the probability of correctly rejecting the null hypothesis under the alternative. We also examine three levels of bias: small, moderate, and large.

  • The tables below report the empirical rejection rates. Under the null hypothesis, all three methods maintain Type I error rates close to the nominal 5% level, albeit slightly conservative. Under the alternative hypothesis, the proposed method consistently achieves higher power than the alternatives, with power approaching 1 as the signal strength increases.

  ATE	Metric	EDO (Small)	CWE (Small)	Proposed (Small)	EDO (Moderate)	CWE (Moderate)	Proposed (Moderate)	EDO (Large)	CWE (Large)	Proposed (Large)
  0.0	Type-I Error	0.030	0.032	0.024	0.030	0.035	0.029	0.030	0.030	0.027
  0.5	Power	0.081	0.097	0.093	0.081	0.103	0.114	0.081	0.084	0.088
  1.0	Power	0.267	0.310	0.320	0.267	0.311	0.335	0.267	0.276	0.286
  1.5	Power	0.546	0.592	0.611	0.546	0.586	0.613	0.546	0.558	0.572
  2.0	Power	0.810	0.847	0.867	0.810	0.835	0.863	0.810	0.815	0.825
  2.5	Power	0.955	0.967	0.974	0.955	0.965	0.970	0.955	0.960	0.962
  3.0	Power	0.994	0.996	0.997	0.994	0.996	0.997	0.994	0.994	0.994

To conclude, we sincerely thank you for your detailed and constructive review. Your comments on the theoretical aspects have guided us in refining the arguments and completing a more rigorous proof framework. We also found your suggestion regarding the potential for statistical inference based on our method to be highly insightful. In response, we have revised the manuscript to incorporate your suggestions and would welcome any further discussion. Thank you again for your thoughtful review.

Thank you for your thoughtful and critical assessment. Many of your comments will help us produce a more readable and self-contained version of the paper. Below, we address each of your specific concerns in turn.

• Contribution relative to existing work on data combination.
  We thank the reviewer for raising the connection to prior work on combining observational and experimental data—a well-studied topic.

  • Existing methods largely fall into two categories:
    (1) those addressing unobserved confounding in observational data using experimental data (e.g., Kallus et al., 2018; Athey et al., 2020; Bartolomeis et al., 2024; Imbens et al., 2025), and
    (2) those improving efficiency under distributional shifts by combining datasets (e.g., Degtiar & Rose, 2023; Shi et al., 2023; Colnet et al., 2024).

  • Our method belongs to the latter and focuses on mitigating distribution shift to enhance estimation accuracy.Within this group, existing methods can be further divided into:

    • Category 1: Assume no posterior shift, and only address covariate and policy shifts (e.g., Li & Luedtke, 2023; Yang et al., 2023; Gao et al., 2025).
    • Category 2: Handle posterior, covariate, and policy shifts, often via $\ell_1$-penalized selection (e.g., Xiong et al., 2023; Sheng et al., 2024; Wu et al., 2025; Cheng & Cai, 2021; Han et al., 2023, 2025).

  • Our approach differs from both in three key aspects:

    • Posterior shift: Unlike Category 1, we explicitly model and account for it.

    • Robustness: Unlike Category 2, which may rely on large posterior shifts, our method is robust to moderate shifts and heavy-tailed data.

    • Estimation principle: We go beyond naive pooling or penalized influence functions by directly minimizing estimated MSE via covariate-adaptive, pessimistic weighting.

    • While the idea of data combination is well-established, our contribution lies in its robust handling of posterior shift, adaptive sample-wise weighting, and a bandit-inspired framework suited to real-world heterogeneous settings.

• Gap Between Theory and Practice

  First, we emphasize that Theorem 1 is generic. As noted (Page 6, Line 234), it applies not only to IS but also to the DR estimator used in our experiments. Details for DR construction are provided in Appendix B.3 to save space. Thus, our theory aligns with our practical implementation. Although the corollaries focus on IS for clarity, our theoretical analysis shows that all results can be extended to DR. Below, we outline the necessary assumptions and provide sketches of the main results.

  • Additional Assumptions for DR

    • Assumption 6 (Doubly Robust Specification): Either the reward function or the density ratio is correctly specified.
    • Assumption 7 (Boundedness of Nuisance Functions):
      • (i) Reward functions are bounded by $r_{\max}$.
      • (ii) Density ratios are bounded between $\epsilon$ and $\epsilon^{-1}$.

  Assumption 6 ensures consistency of DR estimators and can be replaced by requiring both nuisance functions to converge to oracle targets. Under Assumptions 3 and 5, the oracle functions satisfy Assumption 7, making it reasonable to impose boundedness on their estimates.

  • Corollaries for DR

    Let $\delta$ represent the posterior shift magnitude and $\sigma^{(e)}, \sigma^{(h)}$ be reward variances in experimental and historical data.

  • Corollary 1 (Heavy-tailed Historical Rewards)
    DR-EDO remains optimal if: $\sigma^{(h)} \gg \epsilon^{-2} \sqrt{\delta} [\sigma^{(e)} + r_{\max}]$ and the MSE difference between DR and EDO is negligible.

  • Corollary 2 (Heavy-tailed Experimental Rewards)
    DR-HDB remains optimal if: $\sigma^{(e)} \gg \epsilon^{-2} \sqrt{\delta} [\sigma^{(h)} \delta^{-1/2} + \sqrt{n^{(e)}} r_{\max}]$

  • Corollary 3 (Small Posterior Shift) DR-MVE remains optimal under the same condition as the main text.

  • Corollary 4 (Moderate/Large Posterior Shift)
    DR-EDO remains optimal if: $|b(s)| \gg \epsilon^{-2} \left[ |D^{(e)}|^{-1/2} (\sigma^{(e)} + r_{\max}) + |D^{(h)}|^{-1/2} (\sigma^{(h)} + r_{\max}) \right]$

  Compared to IS-based results, the main difference is the dependence on $\epsilon^{-2}$ due to potential density ratio misspecification.

  • Sketch of Proof

    The proof follows that of IS but differs in bias and variance control:

  • Bias: In IS, correct density ratios are needed. In DR, the bias still equals $\mathbb{E}[b(S^{(e)})]$ under Assumption 6 due to its doubly robust nature (see Chernozhukov et al., 2018).

  • Variance: IS is a special case of DR with zero reward function. For general DR, variance bounds still hold under Assumption 7. However, misspecified density ratios yield heavier dependence on $\epsilon^{-1}$, explaining the stronger conditions in DR corollaries.

• Additional Experiments. We add experiments on a public real-world dataset.We evaluate our method on the ACTG175 dataset with 2,139 HIV-positive individuals randomized to four treatments. We focus on comparing ZDV+ddI ($n=522$) and ZDV+zal ($n=524$), using rescaled CD4 count as the outcome and three covariates: age ($S_1$, rescaled by 10), homosexual activity ($S_2$), and hemophilia ($S_3$). The outcome model is:

R_e = f(S') + 0.8 \delta \epsilon_e, \quad R_h = f(S') + \mu_d + 0.05\mu_d S_1' + 0.8 \delta \epsilon_h,

Thank you for your thoughtful and critical assessment. Many of your comments will help us produce a more readable and self-contained version of the paper. Below, we address each of your specific concerns in turn.

• Extension to Sequential Setting Our method naturally extends to sequential decision-making, differing significantly from Li et al. [3]. Given a time horizon $T$, we split the process into $T$ sub-sequences of lengths $1, 2, \ldots, T$, where only the reward at the final step $t$ is retained, preserving the original reward structure.

  • For each sub-sequence, we build a state-varying double robust estimator using both experimental and historical data. At each time $t$, we compute pessimistic estimates of bias, variance, and account for cross-time correlations, aiming to minimize the sum of pessimistic MSEs over all $T$ steps.

  • To illustrate the key difference between our method and that of Li et al.[3], we present a simplified mathematical formulation. Suppose we have value function estimates at each of the $T$ time steps: $\phi_t(S^{(e)})$ based on experimental data and $\phi_t(S^{(h)})$ based on historical data.

    Our weighted estimators:

    • For experimental unit data: $\sum_{t=1}^{T} w_t(S^{(e)}) \cdot \phi_t(S^{(e)})$
    • For historical unit data: $\sum_{t=1}^{T} \left(1 - w_t(S^{(h)}) \right) \cdot \phi_t(S^{(h)})$

    Li et al.'s fixed-weight estimators:

    • For experimental unit data: $w \sum_{t=1}^{T} \cdot \phi_t(S^{(e)})$
    • For historical unit data: $(1-w) \sum_{t=1}^{T} \cdot \phi_t(S^{(h)})$

  • Advantages over Li et al. [3]:

    • State-adaptivity: Sample weights vary with local state information, reducing MSE.

    • Time-adaptivity: Unlike Li et al. [3], who use fixed weights across time, our method allows time-varying weights. It reduces the MSE by leveraging information from specific moments in the dataset. Even if an estimator has a large overall bias across $T$ moments, certain moments may exhibit smaller biases.

    • Computational challenges: Estimating time- and state-varying weights involves handling multi-dimensional state spaces and complex dependencies, while accounting for cross-time correlations adds further computational burden.

• Differences with Li et al. [3]. We appreciate the reviewer’s observation and clarify key distinctions highlighting our novel contributions beyond Li et al. [3].

  • Covariate-Adaptive vs. Constant Weights. A central distinction lies in how the integration weight is defined and optimized.

    • Li et al. [3] propose a constant weight that linearly combines historical and experimental estimators by minimizing a pessimistic bound on the MSE. This approach performs well in cases of large or zero reward shift, but may not adapt well in intermediate regimes.
    • Our method extends this framework by allowing the weight to be a function of the covariates (i.e., covariate-adaptive), treating it as a policy in a contextual bandit framework. This design enables local adaptation to distributional heterogeneity, leading to more refined and robust integration.

  • Theoretical Justification. Our theoretical analysis (see Theorem 1 and Corollaries 1–4 in our paper) provides rigorous justification for the superiority of covariate-adaptive weighting in several challenging settings.

    • In moderate posterior shift scenarios (which are typically the hardest to detect and address), our covariate-adaptive weighting achieves near-oracle performance, while the constant-weighted estimator may suffer from substantial bias if the fixed weight is not well-tuned.

    • The proposed estimator is adaptive: it recovers the optimal performance of the scenario-specific best estimator without knowing the shift regime a priori. This is not achievable by constant-weighted methods, including Li et al. [3].

    • We show that our estimator retains robustness even when the historical or experimental data are heavy-tailed, or when the posterior shift is moderate and non-identifiable from the data.

  • Low-data regimes. We agree that in very low-data regimes, a simple constant-weight approach (e.g., Li et al. [3]) may exhibit lower variance due to reduced model complexity. However, we highlight that

    • Our estimator includes constant weighting as a special case, meaning it can recover the behavior of Li et al. [3] when that is optimal.

    • Moreover, the pessimistic principle we adopt prevents overfitting even in small samples by minimizing an upper bound of the estimated MSE, providing a safeguard in low-data settings.

    • In our experiments, our estimator consistently outperforms or matches the best baseline across all data regimes, including low-sample scenarios.

• Exhaustiveness of distribution shift scenarios. This is an excellent comment. As summarized in Section 3.1 of the main text, all potential distributional shifts can be broadly categorized into three types: (i) covariate shift, (ii) policy shift, and (iii) posterior shift. The first two types can be easily handled using importance sampling. In contrast, posterior shift inevitably introduces bias when incorporating historical data -- a challenge we specifically focus on addressing in this paper.

  • Posterior shift primarily concerns changes in the conditional distribution of the reward given a covariate-policy pair. Since this distribution is quite general, and our main interest lies in minimizing the mean squared error (MSE) of the estimator, we restrict attention to its first two moments: the conditional mean and variance of the reward. The conditional mean is captured by the mean reward difference function $b(s)$, while the conditional variances of the historical and experimental rewards are denoted by $(\sigma^{(e)})^2$ and $(\sigma^{(h)})^2$, respectively.

  • By focusing on these two key quantities, all relevant scenarios can be systematically categorized as follows, based on whether one dominates the other or whether they are of comparable magnitude:

    (i) $\sigma^{(h)}$ deminates both $|b(s)|$ and $\sigma^{(e)})$: This corresponds to the heavy-tailed historical reward scenario (Scenario (i)) considered in the paper.

    (ii) $\sigma^{(e)}$ deminates both $|b(s)|$ and $\sigma^{(h)})$: This corresponds to the heavy-tailed experimental reward scenario (Scenario (ii)).

    (iii) $\sigma^{(e)}$ and $\sigma^{(h)})$ are comparable and both dominate $|b(s)|$: This corresponds to the small mean shift scenario (Scenario (iii)).

    (iv) All three quantities are comparable: This corresponds to the moderate mean shift scenario (Scenario (iv)).

    (v) $|b(s)|$ dominates both $\sigma^{(e)}$ and $\sigma^{(h)})$: This corresponds to the large mean shift scenario (Scenario (v)).

  • Accordingly, all the aforementioned scenarios -- or closely related settings -- are systematically studied in this paper. In summary, our analysis considers all three types of distributional shifts: shifts in the covariate distribution, the policy distribution, and the reward distribution. For the reward distribution, we focus specifically on changes in its first two moments (mean and variance). While this does not exhaustively cover all possible posterior shift scenarios, we believe it captures the most practically relevant scenarios for the purpose of MSE minimization.

• Differences from Theorem 1 in Li et al.[3].
  Li et al. [3] analyze constant weights without pessimism. Their result relies on $\hat{w}$, a data-dependent random variable that can induce high variance. In contrast, our conclusion considers a pessimistic, state-dependent constant weight $w$, which avoids such randomness and reduces variance. Moreover, we explicitly address heavy-tailed settings, which are not covered in Li et al. [3].

• Disconnect between the method and theory with the experimental results. We emphasize that the theoretical foundations of importance sampling and doubly robust estimation are closely linked in assumptions and statistical properties. To better align theory with experiments, we have expanded the discussion of the doubly robust framework in our revision, clarifying its relation to our method. This strengthens the connection between our theoretical claims and empirical performance. For further details, please see our response to Reviewer TPvk due to character limits.

• Extension to Historical Treatment & Control Data Our method is initially developed for scenarios where only control outcomes are available in the historical dataset—a common case in A/B testing. It can be naturally extended to more general settings where both treatment and control outcomes are observed. In this case, we estimate individual treatment effects for historical samples and construct a corresponding estimator. Each experimental unit is assigned a personalized weight $w(S^{(e)})$, while each historical unit receives a complementary weight $1 - w(S^{(h)})$. This enables flexible integration of both datasets in the estimation process and allows us to compute a pessimistic MSE accordingly.

• Conclusion. We will include the following conclusion in the final version.

  • We propose a pessimistic data integration method for causal effect estimation that leverages both experimental and historical datasets. Our method formulates sample-wise weight assignment as a learnable policy. This allows us to apply pessimistic policy optimization to minimize the estimator’s mean squared error .The resulting state-adaptive weights adjust flexibly to individual covariates, improving efficiency and balancing bias-variance tradeoffs. We evaluate the method theoretically and empirically across five scenarios, showing that it achieves near-optimal performance and superior robustness under distribution shift or limited experimental data.

Thank you again for your thoughtful review. We look forward to further discussion.