Disentangling misreporting from genuine adaptation in strategic settings: a causal approach

We thank the reviewer for their insightful feedback. We are encouraged that the reviewer found our causal framework novel and well-motivated, our theoretical analysis rigorous, and our empirical experiments compelling.

1 - No unobserved confounding assumption. The reviewer is correct in that the no unobserved confounding assumption is untestable. However, it is standard in causal inference literature and even causally-motivated work on strategic adaptation [1]. In addition, our method is compatible with existing sensitivity analysis techniques (e.g., [2]) that can relax Assumption 3 and provide bounds on the misreporting rate. Specifically, one can apply sensitivity analysis to get bounds on the estimated causal effects $\delta'_a$, $\tau'_a$, and $\tau_a$, and then apply those bounds through Theorem 1 to obtain a bound on the misreporting rate. We will highlight sensitivity to confounding as a promising direction for future work in the final version.

2 - Access to a manipulated dataset might be unrealistic. The reviewer is correct in that our approach requires access to an unmanipulated dataset. We note that such data is often available from pre-deployment (where there may be no incentive to misreport) or from audits.

3 - The framework mostly handles binary features and assumes misreporting only happens in one direction.

We note our method assumes only that $X^\ast$ and $X$ are binary; other variables ($C, A$, $Y$) can be arbitrarily defined. We chose this setup since it allows for a straightforward definition of the misreporting rate. However, our approach could potentially be extended to multi-valued or continuous features with additional parametric and behavioral assumptions (e.g., partially linear models and agents misreporting $X^\ast$ by applying a fixed additive bias, such that $X = X^\ast + \delta$ for some constant $\delta$). We will add this as a promising direction for future work in the final version.

We also note that while we assume agents only misreport in one direction (e.g., when $X^\ast=0$), our framework can be easily adapted to the opposite case (e.g., misreporting only when $X^\ast=1$). Moreover, one-directional misreporting is a realistic assumption -- e.g., in the Medicare context, private insurers are always incentivised to overreport diagnoses to increase reimbursement and have no incentive to underreport. Similar incentive asymmetries exist in school admissions, loan applications, and health insurance quotes (e.g., GPA, employment, health).

Citations

[1] Chang, Trenton, et al. "Who’s gaming the system? a causally-motivated approach for detecting strategic adaptation." Advances in Neural Information Processing Systems, 2024

[2] Kallus, Nathan, Xiaojie Mao, and Angela Zhou. "Interval estimation of individual-level causal effects under unobserved confounding." The 22nd international conference on artificial intelligence and statistics. PMLR, 2019.

We thank the reviewer for their insightful feedback. We are encouraged that the reviewer values the rigor of our theoretical analysis, the gap our work addresses, and the innovation of our approach.

1 - No unobserved confounding assumption. The reviewer is correct in that the no unobserved confounding assumption is untestable. However, it is standard in causal inference literature and even causally-motivated work on strategic adaptation [1]. In addition, our method is compatible with existing sensitivity analysis techniques (e.g., [2]) that can relax Assumption 3 and provide bounds on the misreporting rate. Specifically, one can apply sensitivity analysis to get bounds on the estimated causal effects $\delta'_a$, $\tau'_a$, and $\tau_a$, and then apply those bounds through Theorem 1 to obtain a bound on the misreporting rate. We will highlight sensitivity to confounding as a promising direction for future work in the final version.

2 - Can the method be generalized to continuous or categorical features? We note our method assumes only that $X^\ast$ and $X$ are binary; other variables ($C$, $A$, $Y$) can be arbitrarily defined. We chose this setup since it allows for a straightforward definition of the misreporting rate. However, our approach could potentially be extended to multi-valued or continuous features with additional parametric and behavioral assumptions (e.g., partially linear models and agents misreporting $X^\ast$ by applying a fixed additive bias, such that $X = X^\ast + \delta$ for some constant $\delta$). We will add this as a promising direction for future work in the final version.

3 - What are the barriers to deploying CMRE in practice (e.g., data access and transparency)? CMRE requires access to unmanipulated data -- typically available from pre-deployment training data or audits. Importantly, CMRE does not require access to the internals of the deployed model, making it applicable even with non-transparent, black-box decision models. We view the timeliness of our work as particularly conducive to its practical deployment, as it aligns with the need for operational efficiency and transparent models, increasingly expressed by AI regulators [3, 4].

4 - The paper could better explain why misreporting doesn't effect causal descendants before diving into technical details. We thank the reviewer for this insightful suggestion. In the final version, we will add the following example based on our Medicare fraud use case: "If a patient truly has cancer ($X^\ast = 1$), they may experience cancer-related symptoms ($Y$). However, if an insurer misreports a cancer diagnosis ($X^\ast = 0$, $X = 1$), this misreporting does not cause the patient to exhibit cancer-related symptoms."

5 - [The work] identifies average misreporting rates but not individual ones. We thank the reviewer for this comment, and wish to clarify that our method estimates a misreporting rate that is conditional on the agent identity rather than a population average. It can be trivially adapted to identify a misreporting rate that is conditional on features of individual datapoints (e.g., an individual's medical history in the Medicare setting), by estimating the conditional average treatment effect (CATE) versions of the TAFR, NAFR, and TAFM estimands in the paper, conditional on any features of interest. This allows us to identify which datapoints are most likely to be misreported. We will clarify this in the final version.

6 - The reliance on causal descendants means the method may not apply to settings where downstream effects are unobservable or delayed. The reviewer is correct that our method requires observing downstream outcomes. In practice, these are often available as the same labels used to train the manipulated model (e.g., enrollee costs in the Medicare risk-adjustment model example). When outcomes are delayed, surrogate or proxy outcomes can be used, consistent with existing causal literature [5]. We will clarify those two points in the final version.

7 - The approach is most useful in settings where agents have incentives to misreport and unmanipulated data is available, which may not cover all strategic ML scenarios. We agree that our method is useful for settings where there is an incentive to misreport. Such scenarios are common in practice (e.g., healthcare insurance, hiring, and lending). We also note that unmanipulated data is often available from pre-deployment or from audits.

Citations

[1] Chang, Trenton, et al. "Who’s gaming the system? a causally-motivated approach for detecting strategic adaptation." Advances in Neural Information Processing Systems, 2024

[2] Kallus, Nathan, Xiaojie Mao, and Angela Zhou. "Interval estimation of individual-level causal effects under unobserved confounding." The 22nd international conference on artificial intelligence and statistics. PMLR, 2019.

[3] Winning the Race AMERICA’S AI ACTION PLAN, White House

[4] Commission, European, et al. Adopt AI Study – Final Study Report. Publications Office of the European Union, 2024

[5] Athey, Susan, et al. The surrogate index: Combining short-term proxies to estimate long-term treatment effects more rapidly and precisely. No. w26463. National Bureau of Economic Research, 2019.

We thank the reviewer for their thoughtful and constructive feedback! The reviewer's comment that our work ``is a strong example of use case inspired basic research'' is truly encouraging. We are also encouraged that they found the problem timely and important, our technical novelty well articulated, and the work clear and easy to follow.

1 - How robust is the [work to the assumption that] the misreporting rate depends only on the true feature values $X^\ast$? How easily can the framework be extended to support subgroup-dependent misreporting rates? We appreciate the reviewer's question and clarify two points: (1) our method already accommodates other variables that affect the misreporting rate, (2) it can be trivially extended to even more fine-grained subgroup-dependent misreporting rates.

First, the agent variable $A$ can act as a confounder/effect modifier with $X \leftarrow A \rightarrow X^\ast$ exactly as the reviewer suggests (see figure 1a, b, and c). Our method is able to account for $A$, as reflected in the experiments section, figure 3 (middle and right), where we report misreporting rates conditional on $A=a$ (the insurance company). We acknowledge that lines 172-173 were unclear. Originally, these lines said "... only the variable $X^\ast$ influences an agent's decision to misreport..." A more precise statement is "Conditional on the agent identity, only $X^{*}$ influences the decision to misreport." That is, conditional on the agent, the misreported group is a random sample of those with $X^\ast=0$. We will clarify in the final version.

Second, our method can be trivially extended to accommodate more granular subgroup analysis by estimating CATE versions of TAFR, NAFR, and TAFM estimands conditioned on any features of interest. While this might increase the variance, as the reviewer noted, it reflects a natural trade-off between granularity and statistical stability that can be navigated based on the application. We will include this discussion in the final version.

2 - Variance of the estimator The reviewer is correct that our approach gives high variance estimates when the causal effect of $X^\ast$ on $Y$ is low. However, we view this as a strength -- it appropriately reflects uncertainty rather than projecting false confidence, which is critical in high-stakes settings.

We also clarify that the non-significant estimated MR rates in Fig. 3 (center) are not simply due to wide intervals. As shown in Fig. 3 (left and right), our method detects significant misreporting when present, indicating that the intervals are informative. The wider intervals in real data reflect honest uncertainty, while NDEE and NMRE yield narrower but biased estimates. Thus, our intervals, though broader, lead to more reliable conclusions.

We note our analysis gives principled approaches for reducing this variance: by picking downstream variables known to be significantly affected by the potentially misreported variable. For example, in our real data analysis, we used mortality as the downstream outcome for simplicity. However, many diagnoses have weak causal effects on mortality, leading to high variance. Using condition-specific downstream outcomes (e.g., insulin for diabetes-related diagnoses) would likely reduce variance. Further reductions in variance are possible, as the reviewer points out, by using DR estimators rather than S-learners. We used S-learners for simplicity. We will clarify these points in the final version.

3 - Are the $\beta$'s chosen for the simulation a good reference point for the real data? We appreciate the reviewer’s question. The $\beta$ values were chosen to reflect effect sizes observed in the Medicare dataset. Our simulations used $\beta \in [0.1, 0.5]$, consistent with estimated effects shown in Appendix F.1, where each diagnosis’s effect on mortality ($Y$) falls between 0.117 and 0.276.

4 - How robust are the real-data findings to the exclusion [criteria], and why are [they] reasonable? What percent of the records were omitted on the basis of these criteria? We thank the reviewer for the thoughtful question. No patient records were excluded; the criteria only filtered which of the 182 diagnoses were reported in the appendix table, not which patient records were used in the analysis. In other words, the reported estimates and their variances do not change at all when removing these exclusion criteria. We would just have 182 diagnoses reported rather than the top 10. These thresholds were selected with clinical input to ensure stable estimates when using mortality as the outcome by excluding diagnoses clinically known to have minimal impact on mortality (e.g., cataracts or osteoarthritis of the hip or knee). In our final version, we will consider reporting all diagnoses in the appendix.

5 - How robust are the synthetic results to coefficient values? We chose coefficients so that the Bernoulli input remained in $[0, 1]$ without requiring transformations (e.g., sigmoid), allowing direct interpretability. Specifically, this allowed us to set the $X^\ast$ coefficient equal to the causal effect. As the reviewer suggests, an alternative is to draw coefficients randomly and apply a sigmoid to the input of the Bernoulli draw, offering more flexibility but requiring additional steps to recover causal effects. We conducted this analysis and found that our conclusions remain robust. The three tables below shows the results from the reviewer's suggested analysis; it shows the squared error of the estimated misreporting rate. Our approach outperforms the baselines in the majority of settings, and performs comparably (not statistically significantly different from) the best baseline in a few of the settings, as indicated by the bold entries in the tables.

6 - The assumption that $X, X^\ast$ are dichotomous is restrictive. We chose this setup since it allows for a straightforward definition of the misreporting rate. However, our approach could potentially be extended to multi-valued or continuous features with additional parametric and behavioral assumptions (e.g., partially linear models and agents misreporting $X^\ast$ by applying a fixed additive bias, such that $X = X^\ast + \delta$ for some constant $\delta$). We will add this as a promising direction for future work in the final version.

7 -- Other minor comments

• Prior work by Chang et al.: We appreciate the reviewer's point and will clarify the differences with Chang et al.
• Notation on line 119 is slightly awkward: We will revise the notation as suggested.
• Buildup to Theorem 1 is somewhat long: We appreciate the reviewer's suggestions and will consider restructuring Section 4.1 to enhance the flow.
• Extra equation number: We will remove.
• Convert text description to main figure: We thank the reviewer for this suggestion! We agree that a visual comparison would clarify the limitations of naive estimators and will add a figure illustrating how our method separates misreporting from genuine modification using causal descendants.

Table 1: MSE of Estimated MR vs Causal Effect of $A$ on $X^\ast$

Table 2: MSE of Estimated MR vs Causal Effect of $X^\ast$ on $Y$

Table 3: MSE of Estimated MR vs Misreporting Rate