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Under review as a conference paper at ICLR 2027

CATE Estimation or Empirical Welfare Maximization? A Statistical Analysis of Causal Decision Making under a Hard Budget

Abstract

Causal decision making under limited resources requires choosing whom to treat while respecting operational constraints. Two widely studied approaches to treatment allocation are (i) first estimating the conditional average treatment effect (CATE) and then using the estimated effects to determine a feasible allocation, and (ii) directly selecting an allocation by empirical welfare maximization (EWM). Their relative statistical performance, however, remains unclear when treatment costs are heterogeneous, and every deployment batch must satisfy a hard budget. To bridge this gap, we study the statistical comparison between CATE estimation and EWM for finite-batch treatment allocation under a hard budget. We develop a common framework that relates treatment effect estimation to allocation regret and characterizes the local regret of the two approaches under correct specification and model misspecification. Our analysis shows that CATE estimation can achieve lower regret by pooling information under correct specification, while misspecification can reverse the comparison in favor of EWM, with an explicit threshold separating the two cases. We extend these results to observational data using cross-fitted doubly robust scores. Finite-sample experiments confirm the predicted variance advantage and the reversal under misspecification. Source code is available at https://anonymous.4open.science/r/STEM-B0E3.

Primary area:
causal reasoning
Keywords:
Hard-budget causal allocation, Treatment effects, Policy value, Allocation regret

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_ayJ4OpenReview ↗
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Paper summary

This paper considers budget-constrained allocation based on estimated CATEs relative to selecting a policy through empirical welfare maximization (EWM) directly. Under a correctly specified shared treatment effect model, inverse-variance weighted CATE estimation is shown to achieve lower local allocation regret, as it uses information across population groups to learn a common parameter. For unweighted CATE, these gains also depend on the noise in the pooled observations. On the other hand, misspecification can reverse these gains.

Critical strengths
  • Interesting question: is CATE-based allocation preferable to EWM?
  • Interesting answers, with precise statements about local regret and crossover points.
  • Informative simulations to study these theoretical results.
  • Extends the comparison to cross-fitted doubly robust scores under nuisance-estimation conditions.
  • Interesting theory results, in particular that observations that cancel out of the empirical welfare difference can still be useful to learn the shared treatment effect parameter. The resulting thresholds make the tradeoff interpretable.
Critical weaknesses

My main concern is that it is not always clear that fixing the policy class means both procedures use the same restrictions on the treatment effect function. Particularly, the main allocation comparison is between treating one higher-cost individual and treating two lower-cost individuals together. Under correct specification, the CATE estimator treats the effects for the two lower-cost groups as fixed, while EWM estimates those effects with noisy data. So the results seem to indicate that the CATE estimator can outperform not only because it is pooling data across groups but also because it is using correct additional restrictions about treatment effects. Appendix L acknowledges that the comparison is between specific procedures, but this still seems important for interpreting the source of the advantage. I would be interested in learning how the results would change if these effects and the relation across groups were also estimated.

More generally, the theory results and simulation studies are in very stylized settings: four observed population groups, one unknown parameter, deployment batches of three, and two competing policies that differ only on one batch composition, with performance compared in a local neighborhood of the allocation boundary. So it is unclear how general these insights are for budget-constrained allocation questions more broadly. Even the extension to binary outcomes maintains this basic treatment effect structure. Related to my first point above, the misspecification analysis only changes the treatment effect for an additional group whose observations contribute to the shared CATE fit but cancel out of the empirical welfare difference. While this does neatly show cases where pooling information is bad, it also leaves the EWM comparison unchanged in the theoretical analysis. It is unclear how relevant this is relative to other forms of misspecification.

Questions for authors
  • Would it be useful to consider a third estimator that learns from observations of the higher-cost group alone, while retaining the assumed fixed effects for the two competing lower-cost groups? This could help tease apart the benefits of pooling data across groups from those of using the other restrictions in the CATE model.

  • Are there any insights you can share about how the results might change in more general settings—for instance, if the effects currently treated as fixed and the relation across groups had to be estimated, or if there were more allocation boundaries?

  • Could the misspecification theory results be extended to changes in treatment effects for the groups directly involved in the allocation comparison? Which insights about the reversal in local regret ordering would still hold more generally?

7 comments
AuthorsOpenReview ↗

Response to Reviewer ayJ4's comments (1/5)

We thank you for your review and suggestions. Our responses are as follows:

W1&Q1: "Sources of the CATE advantage"

Known low-cost effects contribute to the original advantage, but they do not fully explain it: pooling still improves local regret when these effects are estimated under the correct sharing relation. To separate these two sources of improvement, we introduce an E-only comparator and then allow the low-cost effects to be estimated. We also address the further question of learning the sharing relation itself.

1. The E-only comparison separates the benefit of known effects from the additional benefit of pooling. We consider

\operatorname{clip}_{[-\bar\theta,\bar\theta]} \{\frac{\bar\Gamma_E-b(E)}{r}\},$$ which retains the known low-cost effects and the original decoder while excluding $N$ from parameter estimation. Under the correctly specified sequence $\theta_n=sh/\sqrt n$, its local index is $I_E=h\sqrt{H_E}$, giving $$\sqrt n \mathbb E R_3(\widehat\pi_E) \longrightarrow 2p_Ep_1p_2hr \Phi(-I_E).$$ Using the notation of Eqs. (28) and (42), Eq. (38) decomposes as $$I_D^2=\frac{h^2r^2}{T_D} <I_E^2=h^2H_E <(I_R^*)^2=h^2(H_E+H_N).$$ The first improvement uses the known low-cost effects. The second isolates the additional information from $N$, with the same known effects and decoder. **2. Under correct specification, pooling still lowers local regret when the low-cost effects are estimated.** We also fit $$f_{\theta,\gamma_1,\gamma_2} =b+(r\theta,\gamma_1,\gamma_2,\kappa\theta)$$ using inverse variance weighting (IVW) in the squared loss. Both criteria use this enlarged class within a fixed parameter neighborhood preserving the same induced policies. The simulation uses $[-0.1,0.1]^3$. Under the correctly specified sequence $(\theta_n,\gamma_{1,n},\gamma_{2,n})=(sh/\sqrt n,0,0)$, the centered fitted bundle contrast multiplied by $\sqrt n$ has limiting variance $$V_{\mathrm{pool}} =\frac{r^2}{H_E+H_N} +\frac{\sigma_1^2}{p_1} +\frac{\sigma_2^2}{p_2} <T_D.$$ Its limiting wrong-allocation probability is therefore $\Phi(-hr/\sqrt{V_{\mathrm{pool}}})$, showing that a pooling benefit remains when the low-cost effects are estimated. This oracle-score experiment uses $n=2500$, $p=(0.2,0.2,0.2,0.4)$, $r=\kappa=h=1$, and unit conditional score variances. Entries are means across five seeds, with across-seed standard deviations in parentheses. Each seed uses 100,000 replications. All methods use the same simulated observations. Differences below are computed from unrounded estimates. **Table A1. Wrong-allocation probabilities under correct specification.** | Estimator | $L_1/L_2$ effects | Simulated probability (SD) | Local limit | |---|---|---:|---:| | EWM, raw complete-U criterion | Empirical score means | 0.3976 (0.0011) | 0.3981 | | E-only | Known | 0.3277 (0.0016) | 0.3274 | | weighted CATE | Known | 0.2191 (0.0009) | 0.2193 | | weighted CATE estimating $L_1/L_2$ | Estimated | 0.3842 (0.0008) | 0.3848 | Expected allocation regret equals each probability in Table A1 multiplied by the common value gap, $3.2\times10^{-4}$. Compared with EWM, E-only reduces error by approximately 6.9960 percentage points using the known low-cost effects. CATE estimation with inverse variance weighting further reduces error by 10.8602 percentage points relative to E-only through pooling. With estimated low-cost effects, the improvement over EWM is smaller but remains positive: 1.3436 percentage points, with a paired 95\% Monte Carlo interval of [1.2362, 1.4510] percentage points. ...
AuthorsOpenReview ↗

Response to Reviewer ayJ4's comments (2/5)

...continued from above

3. Learning the sharing relation requires additional identification conditions in this local regime. This addresses the further question in W1 about estimating the relation across groups. The preceding extension estimates the low-cost effects while retaining known E/NE/N baselines and loadings. Estimating an unrestricted loading is a different problem because the information about that loading need not increase along the local sequence.

For example, even if θn=sh/n\theta_n=sh/\sqrt n were known, the Gaussian score experiment provides expected Fisher information

=\frac{np_N\theta_n^2}{\sigma_N^2} =\frac{p_Nh^2}{\sigma_N^2}=O(1).$$ For two sufficiently close fixed loadings, the Kullback–Leibler divergence is $p_Nh^2(\kappa_1-\kappa_0)^2/(2\sigma_N^2)$, so they cannot be distinguished with vanishing error. Hence, in this Gaussian local experiment, no estimator is consistent at every loading in an open interval. External calibration or additional identifying restrictions require separate analysis. This does not rule out useful pooling when, for example, the loading’s sign or range is known. It means that the known-loading efficiency formula cannot automatically be retained. The E-only comparison separates the benefit of known low-cost effects from the additional gain from pooling. **The pooling gain persists when the low-cost effects are estimated under the correct, known sharing relation**, as shown by the variance comparison and Table A1. Learning the relation itself requires separate analysis: information about an unrestricted loading remains bounded in this local experiment, so the known-loading constants cannot automatically be retained. As discussed in Appendix L, these conclusions concern the specified procedures and assumptions and do not establish a universal advantage of CATE-based allocation over EWM. **What we revised:** In the revised manuscript, Appendix M.6 now includes the E-only comparison, the variance derivation with estimated low-cost effects, and the oracle-score and cross-fitted results (Table 16). Estimating the sharing relation under additional identification conditions remains future work.
AuthorsOpenReview ↗

Response to Reviewer ayJ4's comments (3/5)

W2&Q3: "Scope of the comparison and misspecification beyond the auxiliary group"

Thank you for these related questions. The additional analyses extend the allocation settings and show that reversal can persist beyond the original NN-only deviation under the stated local conditions. Specifically, we vary the batch size, budget, and candidate policy class to assess sensitivity to the allocation setting. We then use local derivations and corresponding experiments to examine reversal when decision-critical effects also change.

The advantage persists in the tested larger batches and policy class. To examine the allocation structure, we use larger batches and different budgets, (m,B)∈{(3,2),(5,2),(8,2),(8,4),(8,6)},(m,B)\in\{(3,2),(5,2),(8,2),(8,4),(8,6)\}, while retaining costs (2,1,1,1)(2,1,1,1). In the Gaussian local experiment, with n=2500n=2500, h=0.25h=0.25, and 50,000 training replications per sign, weighted CATE has lower mean regret in all five configurations and both signal directions. The competing policies differ on 1, 6, 21, 25, and 19 batch compositions, respectively. These configurations retain the same local bundle contrast. Our supplementary derivation establishes that their different composition probabilities change the common regret multiplier, preserving the ordering under the specified conditions. Thus, this extension relaxes the three-person batch and single-composition restrictions while retaining one active boundary.

Separately, a Bernoulli experiment compares the criteria over 11 distinct policies induced by the full one-dimensional shared score class. Both procedures use the same score class and decoder, with EWM maximizing complete-U welfare over the induced policy class. S-learner and T-learner outcome regressions are used to construct cross-fitted doubly robust scores.

Here the enlarged class uses θ∈R\theta\in\mathbb R, bBer=(0.08,0.055,0.025,0.01)b_{\mathrm{Ber}}=(0.08,0.055,0.025,0.01), and ψ=(1,0,0,1)\psi=(1,0,0,1). The 11 policies span this full parameter range. Treated response probabilities are clipped to [10−5,1−10−5][10^{-5},1-10^{-5}], and the actual CATE is μ1−μ0\mu_1-\mu_0. No clipping was recorded in the simulated samples. This sample-level observation does not by itself establish exact sharing throughout the population. The results are interpreted as empirical evidence for this specified design.

S-learner results are shown for all deployment configurations and both parameter signs. Each sign uses n=2500n=2500 and five seeds with 20,000 training replications each, totaling 100,000. Regret is evaluated on independent deployment batches against the optimal budget-feasible allocation under the actual CATE μ1−μ0\mu_1-\mu_0.

Table A2. Mean per-person allocation regret multiplied by 10510^5 in the 11-policy experiment.

mmBBWeighted CATE, θ=−0.02\theta=-0.02EWM, θ=−0.02\theta=-0.02Weighted CATE, θ=0.02\theta=0.02EWM, θ=0.02\theta=0.02
3248.6752123.508147.7641101.6427
5223.6024106.400242.9180142.7502
8212.364890.592933.8971119.1577
8424.9020126.649949.3034176.5532
8637.8540144.088258.6636129.8624

Weighted CATE has lower mean regret in all ten S-learner comparisons in Table A2, and the corresponding T-learner experiments give the same ordering. These results show that the observed advantage is not confined to a two-policy search. They remain a structured, nonlocal numerical comparison and do not establish the original regret constants or reversal threshold for multiple active boundaries. We also relax the single-parameter restriction by estimating the two low-cost effects. In the Gaussian experiment with estimated scores and weights, the resulting error probability is 0.38280.3828, compared with 0.39670.3967 for EWM, indicating a smaller but remaining pooling advantage.

Decision-critical perturbations can produce reversal even when the true allocation contrast changes. To determine when reversal persists beyond the original NN-only path, retain the original baseline, known loadings, positive type probabilities and conditional score variances, and consider any fixed vector

\qquad \tau_n=b+\frac{d}{\sqrt n}.$$ Assume the other allocation comparisons remain separated, so the oracle remains in the same two-policy class. Define $$K=d_E-d_1-d_2,\qquad M=\frac{p_Er^2}{\sigma_E^2} +\frac{p_N\kappa^2}{\sigma_N^2},$$ $$a(d)=\frac{p_E r d_E}{\sigma_E^2} +\frac{p_N\kappa d_N}{\sigma_N^2}, \qquad T_D=\frac{\sigma_E^2}{p_E} +\frac{\sigma_1^2}{p_1} +\frac{\sigma_2^2}{p_2}.$$ Here $p_t$ and $\sigma_t^2$ are the type probabilities and conditional oracle-score variances. ...
Reviewer_JbjVOpenReview ↗
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Paper summary

This paper compares treatment allocation based on CATE estimation with empirical welfare maximization (EWM) under a hard budget constraint when treatment costs vary across individuals. The authors develop a tractable four-type shared treatment-effect model and use it to examine how information pooling affects allocation regret. Their analysis characterizes the benefits of information pooling and identifies conditions under which noise or misspecification of the sharing structure reverses the relative performance of the two approaches. The paper further extends the analysis to observational settings in which cross-fitted doubly robust scores must be estimated from data and validates the theoretical results through computational experiments.

Critical strengths
  • The paper clearly demonstrates that CATE-based allocation and EWM use different data to determine to whom treatment should be allocated.

  • It quantifies how information pooling affects local allocation regret and identifies explicit conditions under which noise or misspecification of the sharing structure reverses the relative performance of CATE-based allocation and EWM.

Critical weaknesses
  • Prior work, including Hu, Kallus, and Mao (2022), has also examined the distinction between estimate-then-optimize methods and methods that directly optimize decision quality. The paper does not yet make sufficiently clear what additional insight its analysis of local allocation regret and performance reversals provides beyond this existing literature.

  • The paper provides limited discussion of the real-world treatment-allocation problems that the assumed sharing structure is intended to represent. This makes it difficult to assess the practical significance and broader applicability of the findings.

Questions for authors
  • In what kinds of real-world problems might the assumed sharing structure for treatment effects hold, at least approximately? Concrete examples would help clarify the scope and practical relevance of the analysis.

  • What essential role does the hard budget constraint play in producing the benefits of information pooling and the reversal in relative performance between CATE-based allocation and EWM? In particular, which conclusions depend specifically on treatment decisions being coupled within a batch?

5 comments
AuthorsOpenReview ↗

Response to Reviewer JbjV's comments (1/2)

We thank you for your review and suggestions. Our responses are as follows:

W1: "Additional insight relative to Hu, Kallus, and Mao (2022)"

Our contribution relative to Hu, Kallus, and Mao (2022) is the local regret ordering, explicit misspecification threshold, and transfer to estimated causal scores for the specified batch allocation criteria. Their analysis establishes how exploiting regression structure can improve regret convergence rates in contextual linear optimization, and their discussion and experiments address constrained decisions and model misspecification. We ask how the leading allocation regret of two specified learning criteria compares near a hard-budget decision boundary, and how departures from the treatment effect restrictions change that comparison.

First, we connect individual-level causal data to jointly constrained batch decisions. Here the decision coefficients are causal treatment effects, identified under standard causal assumptions and estimated using doubly robust scores. Proposition 3 exactly reduces the complete-U empirical welfare difference, constructed from overlapping observation tuples, to the decision-critical bundle contrast. This reveals how structured CATE estimation can use observations that cancel from the welfare comparison, under a common score class, decoder, and induced policy class.

Second, Theorems 1–3 derive exact local regret constants and an explicit misspecification threshold. Along the analyzed n−1/2n^{-1/2} sequence approaching the allocation boundary, both procedures have regret of the same order. Their relative performance therefore depends on leading constants that convergence-rate comparisons alone do not determine. We quantify when the precision gain from treatment-effect restrictions is outweighed by their induced bias. The optimal policy remains in the common induced class along the misspecification sequence, so the reversal reflects how the criteria use inaccurate restrictions, rather than exclusion of the optimal allocation.

Third, Theorem 4 shows that cross-fitted doubly robust scores and consistently estimated variance weights preserve these leading regret constants under the stated overlap, moment, and nuisance-estimation conditions. This establishes when the comparison carries over to observational causal data.

The contribution is thus a quantitative characterization of the precision–misspecification tradeoff for causal batch allocation under a hard budget, for the specified criteria and local model. Our analysis resolves the local regret ordering and its sensitivity to misspecification, which the broader rate comparison of Hu et al. does not determine.

W2: "Practical meaning of the sharing structure"

Thank you for this comment. The sharing structure represents a common component of causal response across groups with different baseline benefits and delivery costs. To illustrate this interpretation, consider a service program with a fixed staff-hour budget per deployment batch. The same predefined intervention may require two hours for one client and one hour each for two others, creating a choice between competing bundles of treatment benefits.

Relations such as τ(E)−b(E)=rθ\tau(E)-b(E)=r \theta and $ \tau(N)-b(N)=\kappa \theta$ allow observations from one stratum to inform another’s treatment effect, even when the candidate policies agree on the former’s allocation.

We treat the baselines and loadings as known to isolate how this shared information affects allocation regret and how departures from the relation change the comparison. The analysis quantifies when sharing improves allocation precision and when inaccuracies reverse that advantage. The example motivates the assumption. Applying it requires domain evidence. It does not establish that the assumed sharing structure holds broadly.

AuthorsOpenReview ↗

Response to Reviewer JbjV's comments (2/2)

Q1: Where might the shared relation hold approximately?"

Thank you for this question. Employment support and preventive care provide illustrative settings for shared causal responses with heterogeneous delivery costs. In a standardized job-training program, participant strata may share a response component to the same training content while differing in baseline gains and delivery costs. In a medication-adherence support program, a common improvement in adherence may translate into different health benefits across patient strata, while delivery costs vary with service needs or location.

These examples motivate approximating treatment effects as b(t)+θψ(t)b(t)+\theta\psi(t): a shared response parameter with stratum-specific baselines and loadings. The assumption concerns causal treatment effects, meaning differences between treatment and control outcomes. Similar untreated outcomes or prognostic profiles alone would not justify it. We treat the baselines and loadings as known for the statistical comparison. Applying such a relation would require domain support or calibration.

“Agreement-only” is relative to the policies being compared and does not make a group’s observations irrelevant to estimating the shared parameter. In the original three-person construction, the candidate policies make the same allocations on batches containing type NN, so those batches cancel from their empirical welfare difference. This does not mean that NN is never treated or irrelevant to other allocation comparisons. Its observations can still inform the shared parameter governing the decision-critical contrast.

Q2: Which conclusions require coupled batch decisions?"

The hard budget is essential to the coupled allocation boundary and the corresponding local regret comparison studied here. With budget two and costs (2,1,1)(2,1,1), treating EE competes with treating L1L_1 and L2L_2 together, even when all treatment effects are positive. The relevant decision therefore depends on the bundle contrast τ(E)−τ(L1)−τ(L2),\tau(E)-\tau(L_1)-\tau(L_2), rather than the sign of an individual treatment effect.

This coupling determines both the contrast entering the empirical welfare comparison and the welfare loss from selecting the wrong allocation. In our construction, the probability of the critical batch composition and its allocation-value gap produce the common local regret multiplier 2pEp1p2hr2p_Ep_1p_2hr in Theorems 1–3. The resulting constants and crossover threshold characterize how the specified criteria estimate this particular bundle boundary.

If the budget is removed while retaining the same welfare objective and positive effects, every score in the original local working class favors treating everyone. The competing allocations and the local regret comparison studied here consequently disappear.

More generally, pooling gains and misspecification bias do not require a hard budget. Cancellation where candidate policies agree is also a general property of welfare differences. The budget determines the coupled decision boundary and the welfare losses used in our precision–misspecification comparison.

What we revised: In the revised manuscript, Appendix M.8 now derives how batch size and budget affect the local regret multiplier and reports five deployment configurations (Tables 19–20). The original hard-budget model and its local comparison are unchanged.

Hi Reviewer JbjV, we would appreciate your valuable and thoughtful review again.

Since the deadline for the discussion period is approaching, it would be great to have feedback on whether our response addresses the concerns raised in your initial review.

Reviewer_V8WhOpenReview ↗
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Paper summary

The paper compares two approaches to treatment allocation under hard budget constraints: estimating conditional average treatment effects (CATE) followed by optimization, and directly learning a policy through empirical welfare maximization (EWM). The authors formulate the problem for finite batches with heterogeneous treatment costs and derive bounds relating CATE estimation error to allocation regret. Their main theoretical analysis considers a four-type knapsack model, showing that CATE estimation can achieve lower regret by pooling information when the model is correctly specified, while model misspecification can favor EWM. They derive explicit thresholds characterizing this tradeoff in the constructed setting. The analysis is extended to observational data using cross-fitted doubly robust estimators, and the theoretical predictions are validated through synthetic experiments.

Critical strengths
  1. The paper studies a relevant problem of treatment allocation under hard budget constraints, where decisions are coupled across individuals.

  2. The comparison between CATE estimation and EWM is made using the same policy class and allocation procedure, allowing the analysis to isolate the effect of the learning objective.

  3. The theoretical analysis provides explicit expressions for allocation regret and characterizes the variance–bias tradeoff in the constructed setting. The authors also extend the analysis to observational data using doubly robust estimators.

  4. The synthetic experiments closely match the theoretical predictions.

Critical weaknesses
  1. Limited significance: The main finding is not surprising. A correctly specified CATE model can improve statistical efficiency by pooling information, while misspecification can introduce bias and make direct policy learning preferable. The paper does not establish a substantially new principle beyond this observation.

  2. Limited generality of the theoretical results: The main comparison is established for a highly stylized four-type knapsack model with a single unknown parameter and effectively two competing policies. The explicit thresholds are specific to this construction. It is unclear whether the conclusions extend to more general CATE models and policy classes.

  3. The construction favors the claimed outcomes: The CATE model assumes a shared relationship between two populations, and misspecification is introduced in a population that does not affect the EWM policy comparison. This makes the reversal in relative performance largely expected. It is unclear how representative this construction is of practical policy learning problems.

Questions for authors
  1. Generality: Can the authors extend the regret comparison beyond the four-type, one-parameter model? In particular, are there more general conditions under which CATE estimation or EWM is preferable?

  2. Significance of the result: The main finding appears to follow from the standard bias–variance tradeoff. What new insight does the analysis provide beyond this? Is there a phenomenon specific to hard-budget allocation that would not arise in standard policy learning?

  3. Model construction: The misspecification is introduced in a population that contributes to CATE estimation but cancels from the EWM comparison. How representative is this setting? Does the conclusion persist under more general forms of misspecification where both approaches are affected?

  4. Practical relevance: Can the authors demonstrate the tradeoff using more realistic CATE models and policy classes, ideally on a real-world or established benchmark dataset?

7 comments
AuthorsOpenReview ↗

Response to Reviewer V8Wh's comments (1/4)

We thank you for your review and suggestions. Our responses are as follows:

W1: "Limited significance"

The established qualitative bias–variance tradeoff does not determine the leading regret constants or the misspecification threshold derived here. Related work, including Hu, Kallus, and Mao (2022), explains the value of regression structure and compares regret convergence rates. To distinguish criteria with the same local regret rate, we calculate their leading constants and sensitivity to departures from the assumed structure.

Structured CATE estimation uses treatment effect restrictions to incorporate observations that cancel from the EWM welfare contrast. Proposition 3 gives an exact reduction of the complete-U empirical welfare difference to the decision-critical bundle contrast. This identifies which observations enter the welfare comparison and how structured CATE estimation uses treatment effect restrictions to incorporate additional information. The comparison holds the score class, decoder, and induced policy class fixed.

Theorems 1–3 derive exact leading regret constants and an explicit local misspecification threshold. Along the analyzed n−1/2n^{-1/2} sequence, both procedures have regret of the same order, so convergence rates alone do not determine which performs better. The threshold quantifies when the precision advantage from the restrictions is outweighed by their induced bias. The optimal policy also remains in the common induced class along this misspecification sequence. The reversal therefore concerns the fitted effect model, not exclusion of the optimal policy.

Finally, Theorem 4 transfers the local limits to estimated causal scores, using cross-fitted doubly robust scores and consistently estimated variance weights under the stated conditions. The analysis quantifies the familiar tradeoff in the specified hard-budget allocation model. It does not claim a new universal bias–variance principle.

What we revised: In the revised manuscript, Section 6 now states explicitly which model and empirical criteria the regret ordering concerns. Section 5.2 also summarizes the experiments on oracle equivalence and nuisance model misspecification from Appendix M.4 in the main text. Theorems 1–4 are unchanged.

AuthorsOpenReview ↗

Response to Reviewer V8Wh's comments (2/4)

W2&Q1: Limited generality of the theoretical results"

Thank you for raising these questions. The local comparison extends beyond one parameter under stated conditions, but its scalar threshold does not transfer directly to multiple active boundaries. Propositions 1–2 establish batch-value identification and allocation-sensitivity results beyond the four-type model. The explicit regret ordering and thresholds in Theorems 1–3 concern a particular local construction. To state what can be extended, we give a comparison for one active boundary and then allow the low-cost effects to be estimated.

With one active boundary, the signed standardized means determine the local regret ordering. Consider a local comparison between two policies containing the oracle, with signed value difference δV/n\delta_V/\sqrt n, where δV≠0\delta_V\neq0. Suppose procedure jj selects the first policy when C^j≥0\widehat C_j\geq0, and otherwise selects the second, with nC^j⇒N(μj,vj),vj>0.\sqrt n \widehat C_j\Rightarrow N(\mu_j,v_j),\qquad v_j>0. Then its scaled expected regret converges to

\Phi\left(-\frac{\operatorname{sign}(\delta_V)\mu_j}{\sqrt{v_j}}\right).$$ Consequently, the procedure with the larger signed standardized mean has lower local regret. This comparison applies to different models and estimators whenever the stated limits hold: both precision gains and shifts caused by misspecification must be evaluated relative to the true decision boundary. **Estimating the low-cost effects need not remove the pooling gain.** We allow the two effects to be estimated through $$f_{\theta,\gamma_1,\gamma_2} =b+(r\theta,\gamma_1,\gamma_2,\kappa\theta).$$ Within a sufficiently small parameter neighborhood preserving the allocation geometry, both criteria use this enlarged class. For inverse variance weighted CATE, under the correctly specified sequence $(\theta_n,\gamma_{1,n},\gamma_{2,n})=(sh/\sqrt n,0,0)$ and the known $E/N$ sharing relation, the centered fitted bundle contrast multiplied by $\sqrt n$ has limiting variance $$V_{\mathrm{pool}} =\frac{r^2}{H_E+H_N} +\frac{\sigma_1^2}{p_1} +\frac{\sigma_2^2}{p_2} <T_D.$$ Thus, the pooling advantage can persist beyond the one-parameter specification and does not require treating the low-cost effects as known. Its magnitude and misspecification threshold change with the expanded model. **Several active boundaries require a joint comparison.** The analysis then needs the joint distribution of competing contrasts and their distinct welfare losses. The scalar threshold cannot be transferred directly. Additional experiments examine five batch/budget configurations retaining a common local bundle contrast and, separately, an enlarged one-dimensional class inducing 11 policies. Table V1 reports the S-learner results for all five deployment configurations and both parameter signs in the latter experiment. **As complementary numerical evidence, Table V1 shows lower mean regret for weighted CATE than EWM in all ten S-learner comparisons.** The corresponding T-learner experiments yield the same ordering in the other ten. We use S-learner outcome regressions to construct the cross-fitted doubly robust scores. Each parameter sign uses $n=2500$ and five seeds with 20,000 training replications each. Regret is evaluated against the optimal budget-feasible allocation under the actual treatment effects. **Table V1. Mean per-person allocation regret multiplied by $10^5$ in the 11-policy experiment.** | $m$ | $B$ | Weighted CATE, $\theta=-0.02$ | EWM, $\theta=-0.02$ | Weighted CATE, $\theta=0.02$ | EWM, $\theta=0.02$ | |---:|---:|---:|---:|---:|---:| | 3 | 2 | 48.6752 | 123.5081 | 47.7641 | 101.6427 | | 5 | 2 | 23.6024 | 106.4002 | 42.9180 | 142.7502 | | 8 | 2 | 12.3648 | 90.5929 | 33.8971 | 119.1577 | | 8 | 4 | 24.9020 | 126.6499 | 49.3034 | 176.5532 | | 8 | 6 | 37.8540 | 144.0882 | 58.6636 | 129.8624 | **The analysis shows that the local regret comparison extends beyond the one-parameter model when one boundary remains relevant and the stated limits hold.** Table V1 provides complementary numerical evidence beyond a two-policy search, while retaining four types and the original cost vector. This experiment does not establish the original regret constants or threshold for multiple active boundaries. Extending the comparison to more types and several simultaneously active boundaries remains a direction for our future theoretical work. **What we revised:** In the revised manuscript, Appendix M.6 now gives the variance comparison with estimated low-cost effects, and Appendices M.8–M.9 add the larger-batch and eleven-policy experiments. Deriving explicit regret orderings for more types or multiple active boundaries remains future theoretical work.
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Response to Reviewer V8Wh's comments (3/4)

W3&Q3: "Construction and broader misspecification"

The reversal is not confined to the original NN-only deviation: it can also occur when decision-critical effects change, as shown below. The original NN-only deviation is a controlled perturbation that varies the accuracy of the sharing relation while keeping the decision-critical bundle contrast fixed. This isolates the bias induced by the restriction and permits an explicit calculation of when it outweighs the precision gain. The qualitative possibility of reversal alone does not locate the threshold. That requires comparing the local regret constants. The construction is not intended to imply that misspecification typically occurs only in agreement-only groups.

To compare the procedures when decision-critical effects also change, let

\qquad d=(d_E,d_1,d_2,d_N),$$ with fixed $d$, type probabilities, and conditional score variances. Define $$K=d_E-d_1-d_2,\qquad a=\frac{p_Er d_E}{\sigma_E^2} +\frac{p_N\kappa d_N}{\sigma_N^2},$$ with $M=H_E+H_N$ and $T_D$ as in the paper. Provided the other allocation margins remain strict and $K\neq0$, the oracle is $\pi_{\operatorname{sign}(K)}$. Let $S_R^*=\sum_i\psi(X_i)\{\Gamma_i-b(X_i)\}/\sigma_{X_i}^2$ and $S_D=\bar\Gamma_E-\bar\Gamma_1-\bar\Gamma_2$. Under the Gaussian score model, the corresponding decision statistics satisfy $$\frac{S_R^*}{\sqrt n}\Rightarrow N(a,M), \qquad \sqrt n\,S_D\Rightarrow N(K,T_D).$$ Multiplying their sign-error probabilities by the policy-value gap gives $$\begin{aligned} \sqrt n \mathbb E R_3(\widehat\pi_{\mathrm{CATE}}) \longrightarrow 2p_Ep_1p_2|K| \Phi\left(-\frac{\operatorname{sign}(K)a}{\sqrt M}\right),\\ \sqrt n \mathbb E R_3(\widehat\pi_{\mathrm{EWM}}) \longrightarrow 2p_Ep_1p_2|K| \Phi\left(-\frac{|K|}{\sqrt{T_D}}\right). \end{aligned}$$ Here CATE denotes the original inverse-variance weighted estimator with fixed low-cost effects. These expressions accommodate local changes in all four types. Under the corresponding overlap, moment, and nuisance-rate conditions along the new sequence, cross-fitted scores preserve the limits when their changes in the normalized statistics are $o_p(1)$ and estimated weights are consistent. **A joint perturbation produces reversal while changing EWM’s target.** We examine the simultaneous perturbation $$d(\rho)=(1+\rho/2,\rho/10,0,1-\rho), \qquad 0\leq\rho\leq2.$$ Under the baseline parameters, both decision indices change: $$I_{\mathrm{CATE}}(\rho)=\frac{0.6-0.3\rho}{\sqrt{0.6}}, \qquad I_{\mathrm{EWM}}(\rho)=\frac{1+0.4\rho}{\sqrt{15}}.$$ Their equality yields a local crossover at $\rho=20/19$. Oracle-score experiments use $n=2500$, five seeds, and 100,000 replications per seed and setting. Parentheses report across-seed standard deviations. Both methods use the same simulated observations. **Table V2. Wrong-allocation probabilities at selected simultaneous perturbations.** | $\rho$ | CATE: simulated (SD) | CATE: local limit | EWM: simulated (SD) | EWM: local limit | |---|---:|---:|---:|---:| | 0 | 0.2192 (0.0012) | 0.2193 | 0.3987 (0.0007) | 0.3981 | | 0.5 | 0.2793 (0.0011) | 0.2806 | 0.3778 (0.0010) | 0.3783 | | $20/19\approx1.0526$ | 0.3566 (0.0023) | 0.3568 | 0.3572 (0.0017) | 0.3568 | | 1.5 | 0.4241 (0.0006) | 0.4232 | 0.3398 (0.0015) | 0.3398 | Within each setting, expected regret equals the error probability multiplied by the common value gap $3.2\times10^{-4}(1+0.4\rho)$. The comparisons in Table V2 are consistent with the predicted regret reversal while EWM’s comparison also changes. The original perturbation holds the bundle contrast fixed to isolate the bias from an inaccurate sharing relation and compare it with the precision gain. **The extended analysis and Table V2 show that reversal can also occur when decision-critical effects change and EWM’s target changes accordingly.** This change in target does not itself bias fixed-policy welfare estimation with valid oracle scores. **The regret ordering depends on the signed standardized means along the perturbation path, so neither reversal nor a unique crossing is guaranteed for an arbitrary path.** **What we revised:** In the revised manuscript, Appendix M.7 now gives the broader local derivation and experiments for simultaneous and $L_1$-only deviations (Tables 17–18). Section 6 now specifies that EWM's contrast remains unchanged along the original $N$-only path.
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Paper summary

The paper compares two approaches to treatment allocation under heterogeneous costs and a hard budget for each deployment batch: estimating conditional average treatment effects (CATE) before optimizing allocation, and directly selecting a policy through empirical welfare maximization (EWM). It establishes a common framework for evaluating both approaches and relates treatment-effect estimation error to allocation regret.

The main contribution is an explicit local asymptotic comparison in a four-type knapsack model. The structured CATE estimation pools information across covariate types, including observations that cancel from EWM’s comparison between competing allocations. Under the correct specification, the inverse-variance-weighted CATE achieves a lower local allocation regret than the particular EWM criterion studied, although unweighted pooling can be disadvantaged by noisy observations. Under the local model mis-specification, pooling introduces bias, and the paper derives an explicit threshold beyond which EWM performs better. It also shows that these comparisons can be extended to estimated, cross-fitted doubly-robust (DR) scores under suitable nuisance-estimation conditions.

Validation consists of theoretical derivations and synthetic experiments. Monte Carlo simulations closely reproduce the predicted error probabilities and crossover thresholds. Additional experiments vary sample sizes and model parameters, examine estimated scores and nuisance-model misspecification, and extend the comparison to Bernoulli outcomes. The empirical evidence therefore supports the proposed mechanism within the controlled settings built around the four-type model.

Critical strengths

(S1) The paper makes the trade-off between information pooling and model mis-specification precise: In the four-type knapsack model, the analysis identifies exactly which observations inform each method’s allocation decision. Theorems 1--3 quantify the variance advantage of the correctly specified CATE estimation and derive an explicit mis-specification threshold beyond which EWM achieves a lower local allocation regret. It provides a concrete explanation of why the methods can perform differently even when selecting among the same feasible policies, and clarifies when pooling information helps or hurts.

(S2) The comparison extends beyond oracle treatment-effect scores: Theorem 4 establishes that the cross-fitted doubly-robust scores and consistently estimated variance weights preserve the local allocation regret comparisons under the stated nuisance-estimation conditions. This strengthens the contribution because the central mechanism survives the additional estimation required with the observational data, rather than depending entirely on access to unknown nuisance functions.

Critical weaknesses

(W1) My main concern is that the comparison depends substantially on how the two estimators use the assumed model structure: The CATE regression treats the effects at L1L_1 and L2L_2 as fixed, whereas EWM estimates these effects through noisy sample means. The equation (38) makes this observation particularly clear: an estimator using only type EE and its known baseline already outperforms the raw EWM, without pooling observations from type NN. This is a legitimate comparison of the specified estimators, but it leaves unclear how much of the advantage should be attributed to the CATE estimation itself. The advantage partially reflects the structural information that EWM does not exploit. Consequently, the results seem to provide limited support for a broader distinction between CATE-based allocation and EWM.

(W2) The scope of the evidence is too narrow to establish the broader significance of the findings: The main comparison uses four covariate types, batches of three, and a known one-parameter model that reduces allocation to a choice between two policies. The mis-specification changes type NN, which is absent from the decision statistic of EWM, so EWM is unaffected by design. The simulations provide corroborations of the theoretical results, but largely stay within this construction; even the Bernoulli experiments retain the four-type structure. The simulations provide useful checks of the theoretical predictions, but largely stay within this construction; even the Bernoulli experiments retain the four-type structure. The example is informative, yet I am not sufficiently convinced that the paper establishes enough beyond it to support a strong contribution to budget-constrained policy learning.

Questions for authors

(Q1) The main results of the paper explain when sharing information across groups helps or hurts treatment decisions. What do we learn specifically about decisions under a limited budget constraint that we would not learn from a similar problem without a budget?

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AuthorsOpenReview ↗

Response to Reviewer yUfB's comments (1/4)

We thank you for your review and suggestions. Our responses are as follows:

W1: "Fixed low-cost effects versus cross-type pooling"

Known low-cost effects explain part of the original advantage, but pooling provides an additional gain that remains when those effects are estimated under the correct sharing relation. To separate these gains, we introduce an E-only comparator and then estimate the low-cost effects while retaining the sharing relation.

The E-only comparison separates the two sources of the advantage. We introduce

\operatorname{clip}_{[-\bar\theta,\bar\theta]} \{\frac{\bar\Gamma_E-b(E)}{r}\},$$ which retains the fixed low-cost effects and the original decoder but does not use observations from $N$. Under the correctly specified local sequence $\theta_n=sh/\sqrt n$, the cell-mean central limit theorem gives its index $I_E=h\sqrt{H_E}$ and $$\sqrt n \mathbb E R_3(\widehat\pi_E) \longrightarrow 2p_Ep_1p_2hr \Phi(-I_E).$$ Using the notation of Eqs. (28) and (42), Eq. (38) can be written as: $$I_D^2=\frac{h^2r^2}{T_D} <I_E^2=h^2H_E <(I_R^*)^2=h^2(H_E+H_N).$$ The first improvement uses the known low-cost effects and the second isolates the incremental information from $N$. **Under correct specification, pooling still lowers local regret when the low-cost effects are estimated.** We fit the following model: $$f_{\theta,\gamma_1,\gamma_2} =b+(r\theta,\gamma_1,\gamma_2,\kappa\theta).$$ The CATE parameters are fitted by inverse-variance weighted squared loss. Both criteria are defined on this enlarged class, within a fixed parameter neighborhood preserving the same induced policies. The simulation uses $[-0.1,0.1]^3$. Under the correctly specified sequence $(\theta_n,\gamma_{1,n},\gamma_{2,n})=(sh/\sqrt n,0,0)$, the centered fitted bundle contrast, multiplied by $\sqrt n$, has limiting variance $$V_{\mathrm{pool}} =\frac{r^2}{H_E+H_N} +\frac{\sigma_1^2}{p_1} +\frac{\sigma_2^2}{p_2} <T_D.$$ Thus, an incremental pooling benefit remains when the low-cost effects are estimated, while the $E/N$ baselines and loadings remain known. This oracle-score experiment uses $n=2500$, $p=(0.2,0.2,0.2,0.4)$, $r=\kappa=h=1$, and unit conditional score variances. Entries report means across five seeds, with across-seed standard deviations in parentheses. Each seed uses 100,000 replications. All estimators use the same simulated observations. Local limits are reported separately. Differences below are computed from unrounded estimates. **Table Y1. Wrong-allocation probabilities under correct specification.** | Estimator | Treatment of $L_1/L_2$ effects | Simulated probability (SD) | Local limit | |---|---|---:|---:| | EWM, raw complete-U criterion | Empirical score means | 0.3976 (0.0011) | 0.3981 | | E-only | Known | 0.3277 (0.0016) | 0.3274 | | weighted CATE | Known | 0.2191 (0.0009) | 0.2193 | | weighted CATE estimating $L_1/L_2$ | Estimated | 0.3842 (0.0008) | 0.3848 | In this setting, expected allocation regret equals the wrong-allocation probability multiplied by the common value gap, $3.2\times10^{-4}$, so Table Y1 also determines the regret ordering. Compared with EWM, E-only reduces the error probability by approximately 6.9960 percentage points using the known low-cost effects. CATE estimation with inverse-variance weighting provides a further 10.8602 percentage-point reduction relative to E-only through pooling. When the low-cost effects are estimated, the improvement over EWM is smaller but remains positive: 1.3436 percentage points, with a paired 95\% Monte Carlo interval of [1.2362, 1.4510] percentage points. **The E-only comparison separates the benefit of known low-cost effects from the additional gain from pooling**. The variance comparison and Table Y1 further show that **pooling still lowers local regret when the low-cost effects are estimated under the correct, known sharing relation.** As discussed in Appendix L, these conclusions apply to the specified criteria and effect restrictions. They do not establish a universal advantage of CATE-based allocation over EWM. **What we revised:** In the revised manuscript, Appendix M.6 now includes the E-only comparison, the variance calculation with estimated low-cost effects, and the oracle-score and cross-fitted results (Table 16). Section 6 explicitly limits the regret ordering to the specified shared model and raw complete-U EWM criterion.
AuthorsOpenReview ↗

Response to Reviewer yUfB's comments (2/4)

W2: "Narrow construction and scope of the evidence"

In the extensions studied here, the CATE advantage persists with estimated low-cost effects and larger allocation searches, and reversal can occur when decision-critical effects change. The explicit regret constants and thresholds still concern the stated local construction. To assess which restrictions matter, we estimate the low-cost effects, vary batch size and budget, enlarge the candidate policy class, and perturb decision-critical types.

A smaller pooling gain remains when the low-cost effects are estimated. This enlarges the CATE model to three parameters while retaining the known sharing relation. Under correct specification, the allocation-error probabilities are 0.38420.3842 for the weighted CATE criterion and 0.39760.3976 for EWM with oracle scores (Table Y1). In the Gaussian causal-data experiment with cross-fitted doubly robust scores and estimated variance weights, they are 0.38280.3828 and 0.39670.3967, respectively. Thus, an incremental pooling advantage remains, although it is smaller than when the low-cost effects are known.

The tested larger batches preserve the local ordering while retaining one active local boundary. To examine the role of batch size and budget, we use the deployment configurations (m,B)∈{(3,2),(5,2),(8,2),(8,4),(8,6)},(m,B)\in\{(3,2),(5,2),(8,2),(8,4),(8,6)\}, retaining the heterogeneous costs (2,1,1,1)(2,1,1,1). In the correctly specified Gaussian local experiment, with n=2500n=2500, h=0.25h=0.25, and 50,000 training replications per sign, weighted CATE has lower mean regret in all five configurations and both signal directions. Enumeration identifies 1, 6, 21, 25, and 19 batch compositions on which allocations change, respectively. These configurations retain a common local bundle contrast. Our supplementary derivation shows that their different composition probabilities change the common welfare-loss multiplier, preserving the local ordering under the stated conditions. The deployment settings change, but the comparison still has one active local boundary.

The observed advantage is not restricted to a two-policy search. To test a larger candidate class, we run a separate Bernoulli experiment. For each deployment configuration, the full one-dimensional shared score class induces 11 distinct policies. EWM maximizes the complete-U welfare criterion over this class, while CATE uses its fitted score with the same decoder and induced class. S-learner and T-learner outcome regressions provide the cross-fitted doubly robust scores.

Here the enlarged class uses θ∈R\theta\in\mathbb R, bBer=(0.08,0.055,0.025,0.01)b_{\mathrm{Ber}}=(0.08,0.055,0.025,0.01), and ψ=(1,0,0,1)\psi=(1,0,0,1). The 11 policies span this full parameter range. Treated response probabilities are clipped to [10−5,1−10−5][10^{-5},1-10^{-5}], and the actual CATE is μ1−μ0\mu_1-\mu_0. No clipping was recorded in the simulated samples. This sample-level observation does not by itself establish exact sharing throughout the population. The results are interpreted as empirical evidence for this specified design.

Each nuisance-learner/sign combination uses n=2500n=2500 and five seeds with 20,000 training replications each, totaling 100,000. Regret is evaluated on independent deployment batches against the optimal budget-feasible allocation under the actual CATE μ1−μ0\mu_1-\mu_0. CATE denotes the weighted structured criterion.

Table Y2. Mean per-person allocation regret multiplied by 10510^5 in the 11-policy experiment.

Nuisance learnermmBBCATE, θ=−0.02\theta=-0.02EWM, θ=−0.02\theta=-0.02CATE, θ=0.02\theta=0.02EWM, θ=0.02\theta=0.02
S3248.6752123.508147.7641101.6427
S5223.6024106.400242.9180142.7502
S8212.364890.592933.8971119.1577
S8424.9020126.649949.3034176.5532
S8637.8540144.088258.6636129.8624
T3248.7063123.350647.7118101.6512
T5223.6019106.399942.8745142.7458
T8212.362490.552733.8631119.0659
T8424.9010126.699349.2445176.4723
T8637.8737144.025958.5870129.8072

Table Y2 shows lower mean regret for weighted CATE in all 20 configurations. The advantage in this design therefore extends beyond a two-policy search within a structured, one-dimensional class. We treat it as a nonlocal empirical extension, rather than a validation of the original local constants or misspecification threshold.

...

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Response to Reviewer yUfB's comments (3/4)

...continued from above

Reversal can persist when EWM’s target also changes. To test dependence on the original perturbation, we use a path that also changes decision-critical effects:

\qquad d(\rho)=\left(1+\frac{\rho}{2}, \frac{\rho}{10}, 0, 1-\rho\right),$$ in the order $(E,L_1,L_2,N)$. The true bundle contrast becomes $(1+0.4\rho)/\sqrt n$, so EWM’s comparison target changes. Results use $n=2500$, 50,000 replications per setting, cross-fitted doubly robust scores, and estimated variance weights. **Table Y3. Expected per-person allocation regret multiplied by $10^5$ under simultaneous deviations.** | $\rho$ | Weighted CATE | EWM | |---:|---:|---:| | 0.5 | 10.8557 | 14.6396 | | $20/19$ | 16.2159 | 16.3687 | | 1.5 | 21.7303 | 17.3793 | Table Y3 shows a change in ordering consistent with the path-specific local crossing $\rho^*=20/19$. The oracle-score experiment gives the same ordering. At the crossing, the paired 95\% Monte Carlo interval for the EWM-minus-CATE wrong-policy probability difference is $[-0.0019,0.0086]$, consistent with equal leading regret. EWM continues to estimate the changed welfare contrast using valid scores. A change in its target does not itself introduce estimation bias. Reversal is therefore possible beyond the original $N$-only path, although it is not guaranteed for every perturbation. **The reported extensions show that the advantage persists in the tested allocation settings, and reversal can occur when decision-critical effects change, even though EWM’s target also changes.** The larger-batch experiments retain a common local contrast, while the larger policy search provides nonlocal numerical evidence. The batch-value identification and perturbation results are not restricted to four types, but the regret constants depend on the allocation geometry and contrast distributions. Comparisons involving more types or simultaneously active boundaries require further analysis, and benchmark evaluation would add evidence on practical relevance. These findings therefore support conditional comparisons of the specified criteria without implying a universal ranking of CATE-based allocation and EWM. **What we revised:** In the revised manuscript, we added the derivations and experiments in Appendices M.6–M.9 on estimated low-cost effects, broader perturbations, larger batches and budgets, and the eleven-policy search. Deriving explicit regret orderings for more types or multiple active boundaries, and benchmark validation, remain future work.

Comments on the paper

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AuthorsOpenReview ↗

Summary of Revisions to the Manuscript — Submission 57459

The revised manuscript retains the original learning criteria and main theoretical conclusions. Section 5.2 now summarizes selected Gaussian causal-data results from Appendix M.4, which remains available in full. New Appendices M.6–M.9 provide supplementary derivations and experiments on the sources of the CATE advantage, estimation of low-cost effects, broader local perturbations, larger batch/budget configurations, and an eleven-policy Bernoulli comparison. We also clarified notation, statistical reporting, and the scope of the conclusions, updated figure labels, and corrected one rounded table entry. Added and revised content, including material newly presented in the main text, is marked in blue.

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