acceptodds
Under review as a conference paper at ICLR 2027

Causal Predict-Then-Optimize: Treatment Effect Estimation under Downstream Optimization

Abstract

Many operational decisions depend on estimating heterogeneous treatment effects and then using those estimates in constrained downstream optimization. In this setting, accurate causal prediction does not necessarily lead to good decisions, because estimation errors matter most when they occur near decision boundaries and alter the optimizer. We develop causal predict-then-optimize (CPO), which combines doubly robust causal estimation with decision-focused learning, and propose decision-calibrated causal predict-then-optimize (DC-CPO), which explicitly accounts for downstream decision sensitivity. Our framework characterizes causal uncertainty through its orientation relative to optimization boundaries and introduces a boundary-sensitive regularizer that emphasizes prediction errors along decision-relevant directions. The resulting method is designed to improve decisions rather than treatment-effect prediction accuracy alone. Across synthetic and real-world covariate designs, CPO+ achieves lower downstream regret than prediction-oriented causal learners, while DC-CPO further reduces regret and decision-boundary crossing. Our results show that causal prediction accuracy and downstream decision quality are distinct objectives, and that explicitly calibrating causal estimators to optimization boundaries can lead to better constrained treatment allocation.

Primary area:
causal reasoning
Keywords:
causal inference, predict-then-optimize, treatment effect estimation, causal policy learning

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_7GTSOpenReview ↗
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Paper summary

The paper studies treatment allocation in constrained settings, where benefit is defined by the conditional average treatment effect. The authors propose CPO+, which trains the decision model with an SPO+ surrogate to correctly allocate people across groups, using a doubly robust proxy as the true CATE is unobserved. They show the expected surrogate loss upper-bounds causal regret (Thm 3.3). They then define a decision fragility index (DFI) that characterizes the importance of examples along the decision boundary. This motivates DC-CPO, which adds a margin-weighted penalty for examples near the decision-boundary. The paper compares the proposed approaches to simpler regression-based approaches on synthetic and semi-synthetic datasets, and show better decision performance (i.e., lower regret) than the regression baselines.

Critical strengths
  1. Adapting SPO+ to doubly robust pseudo-outcomes is a natural idea and the authors do a good job of formalizing the problem to lead up to this natural conclusion. I appreciate Figure 1, really driving home how this is amenable to the SPO formulation and motivating the margin discussion.
  2. Looking at margins along decision-boundary directions is a nice idea that hasn't been explored as well in the treatment effect space. It explains why two estimators with the same error can lead to different allocations a bit more clearly than past work, connecting more to core ML/decision-theory, which comes with nice theoretical proofs.
Critical weaknesses
  1. The main motivation is not new. Kamran et al. (AISTATS 2024) argue that accurate CATE estimation is sufficient but not necessary for optimal allocation under resource constraints, and that better CATE accuracy does not imply a better allocation. They give a margin argument that is close to much of the theory in this work. The margin argument also lends itself very closely to the learning-to-rank area as a whole. Even more, Rank-Learner (Arno et al. 2026) make the same argument and propose a Neyman-orthogonal pairwise ranking loss for this problem that improves even more on past work Neither paper is cited. The authors should discuss how their contribution differs from this line of work (ranking treatment effects), and discuss whether neyman-orthogonality holds for their methods as well. If not, why should this be preferred over Rank-Learner?
  2. The experiments are quite limited and and show very limited improvements of the model and show limited results as a whole. Some pointed weaknesses in the experiments:
  • The papers in Weakness 1, and ranking methods in general, are missing as baselines. The experiments are directly testing ranking, so even non-CATE methods like LambdaRank would be useful as a baseline.
  • The results do not support the claim that accuracy and decision quality diverge. All CPO methods have lower PEHE than MSE-DR and MAE-DR in most settings throughout the paper. The only case of worse PEHE with better regret is DC-CPO vs CPO+ on ACTG-175. This suggests the gains may come from something other than reframing the problem as decision-oriented.
  • DC-CPO⁻ performs close to DC-CPO. The nonuniform weighting that Section 4 motivates appears to add little.
  • The baselines are linear and may be under-tuned. Specifically, 1) the baselines and the proposed methods are regularized differently (ridge vs no ridge) 2) Propensities clipping is it should be explored a bit more as it could cause the PEHE issues in the bad baseline results.
Questions for authors
  1. How does the proposed method compare to ranking methods like Rank-Learner? Both in motivation/theory and experimentally.
  2. Why do the baseline methods do so poorly in terms of PEHE compared to the decision-based estimators?
  3. Can you better quantify whether the DFI actually flips allocations in real problems/datasets?
  4. Why consider costs and individual-level baseline reweighting in the problem setting if these are never tested in the experiments?
5 comments

We have added ranking and stronger-baseline comparisons, DFI diagnostics, and utility tests.

W1 / Q1 — Treatment-effect ranking already addresses prediction–allocation mismatch. How does DC-CPO differ, including in orthogonality, and how does it compare with Rank-Learner?

Answer: DC-CPO regularizes errors along contrasts between feasible allocations; CPO+ and DC-CPO generally retain first-order nuisance sensitivity after the nonlinear allocation map. In the reported comparison, DC-CPO has lower mean Out regret than both Rank-Learner validation variants on all four datasets.

1. Relation to treatment-effect ranking. Kamran et al. (2024) establish that accurate CATE estimation is sufficient but unnecessary for good allocation and develop a margin argument; Arno et al. (2026) turn the ranking perspective into a Neyman-orthogonal pairwise loss.

2. Allocation geometry and statistical properties. For our partition-capacity experiments, net-benefit ordering and sign determine an optimizer under consistent tie handling, making ranking a direct comparator. Under more general constraints, a direction can compare two feasible allocations through sums of individual net benefits. DFI measures directional uncertainty relative to the corresponding allocation margin; Theorems 4.1 and 4.3 translate this quantity into an invariance certificate and a crossing bound. DC-CPO uses nearby allocation contrasts to assign the penalty to decision-sensitive errors.

The AIPW guarantee concerns the pseudo-benefit's conditional mean. We evaluate the practical value of DC-CPO's allocation-geometry approach against pairwise and Rank-Learner adaptations using the same costs, constraints, and downstream regret.

3. Experimental comparison. Out regret; mean (SE), 30 matched seeds. Rank-Learner is the linear-feature plus DR-calibration adaptation; the two labels denote validation criteria.

DATASETCPO+DC-CPODR-PAIRWISERANK-LEARNER-LINEAR-AUTOCRANK-LEARNER-LINEAR-REGRET
DGP1.0502 (0.0584)0.9762 (0.0647)0.9837 (0.0534)0.9954 (0.0455)1.0450 (0.0466)
Twins0.7484 (0.0480)0.7270 (0.0436)0.7418 (0.0385)0.7470 (0.0348)0.7422 (0.0338)
NHANES1.4199 (0.0697)1.21993 (0.0708)1.32072 (0.0529)1.3414 (0.0692)1.3579 (0.0755)
ACTG-1751.6772 (0.0754)1.5642 (0.0510)1.5677 (0.0733)1.7976 (0.0982)1.9569 (0.1549)

DC-CPO also has lower mean Out regret than CPO+ and DR-Pairwise on all four datasets. The comparison uses the same downstream allocation criterion for all methods.

Appendix C.7 now includes the ranking comparison and its adaptation and validation procedures, while Appendix A presents the motivation and theory comparison.

W2 / Q2 — Could unequal regularization, limited tuning, or propensity clipping explain the poor baseline PEHE and the apparent decision gains?

Answer: Wider regularization search with prediction-loss selection lowers MSE-DR PEHE; stronger propensity clipping also lowers its ACTG-175 PEHE. With the strengthened prediction baseline, MSE-DR has lower mean PEHE than DC-CPO on all four datasets, while DC-CPO retains lower mean regret.

1. Regularization and model selection. Appendix C.1 specifies ridge-regularized MSE-DR and MAE-DR, with regularization selected by validation pseudo-regret, while the submitted CPO+ and DC-CPO objectives have no additional parameter ridge. For the supplementary comparison reported here, we use L2 parameter regularization across methods and evaluate prediction-loss-based selection for MSE-DR and MAE-DR over an expanded regularization grid. Data splits, features, and nuisance estimates are shared within the comparison.

2. Strengthened prediction baselines. Out results, 20 paired seeds; each cell reports mean PEHE / mean regret. Original MSE-DR uses the original ridge grid; the baselines selected by prediction loss use that grid augmented with {0.1, 1, 10}.

DATASETORIGINAL MSE-DR (PSEUDO-REGRET)MSE-DR (PREDICTION LOSS)MAE-DR (PREDICTION LOSS)DC-CPO
DGP0.7408 / 1.36730.4323 / 1.78920.4464 / 1.19800.5952 / 1.0450
Twins0.3540 / 0.78220.3480 / 0.79770.3950 / 0.90760.3762 / 0.7418
NHANES1.5519 / 1.51610.8146 / 1.52411.3489 / 1.44811.0215 / 1.3414
ACTG-1755.9773 / 1.93710.9638 / 2.23591.1643 / 1.89761.0930 / 1.5642

3. Propensity clipping. Increasing the shared propensity clipping threshold from 0.000001 to 0.05 reduces ACTG-175 MSE-DR PEHE from 5.9773 to 4.5026, with smaller changes on the other datasets. The flexible-learner comparisons in Appendix C.6 additionally evaluate forest and Nyström-RBF representations.

Appendix C.7 now includes the comparison of regularization search ranges and validation criteria.

Q3 — Can DFI be linked quantitatively to actual allocation changes on the datasets?

Answer: DFI measures how much perturbation is needed to reach an allocation boundary. Its predicted-center form is positively associated with bootstrap allocation changes on all four datasets.

1. Critical perturbation radius. For a unique reference optimum and perturbations in Er=Σ1/2u:∣u∣2≤r\mathcal E_r=\\{\Sigma^{1/2}u:\\|u\\|_2\le r\\}, the critical radius is rcrit=1/DFIr_{\mathrm{crit}}=1/\mathrm{DFI}. Perturbations inside this radius preserve the reference allocation; a competing allocation can tie at the boundary, and moving beyond it along a most sensitive direction changes the allocation. Thus a larger DFI corresponds to a smaller perturbation needed to reach a decision boundary.

2. Allocation changes and empirical association. Across 20,000 center–batch combinations on four datasets, using both predicted and oracle centers, scaling the constructed critical perturbation by 0.99 preserved the allocation in every case, while scaling it by 1.01 changed the allocation in every case. The table reports the empirical association between DFI and bootstrap switching on the synthetic and real-covariate semi-synthetic benchmarks.

DATASETMEDIAN CRITICAL RADIUS¹BOOTSTRAP SWITCH RATEPREDICTED-CENTER SPEARMAN [95% CI]ORACLE-CENTER SPEARMAN [95% CI]
DGP0.154285.45%0.439 [0.405, 0.472]0.054 [0.016, 0.092]
Twins0.236773.28%0.556 [0.522, 0.589]0.077 [0.036, 0.120]
NHANES0.186879.68%0.513 [0.480, 0.547]0.060 [0.026, 0.095]
ACTG-1750.173681.75%0.479 [0.442, 0.515]0.068 [0.032, 0.103]

¹ The critical-radius median uses the predicted center. We use CPO+ Out predictions from 50 seeds, 50 batches per seed, and 40 saved bootstrap refits; Σ\Sigma is estimated from the bootstrap benefit predictions. A switch denotes any change in the batch allocation. Spearman correlations are computed across batches within each seed and then averaged; confidence intervals resample seeds. DFI and switching frequencies use the same bootstrap draws.

Appendix C.7 now includes the critical-radius explanation, perturbation checks, and empirical association table.

W2 — DC-CPO⁻ performs close to DC-CPO. What does nonuniform direction weighting contribute?

Answer: Nonuniform weighting reduces Crossing by 0.63–1.07 percentage points and reduces regret relative to DC-CPO⁻ on all four datasets.

1. What the ablation retains. DC-CPO⁻ retains active-boundary selection, directional projections, and the boundary penalty, with uniform direction weights. Its comparison with DC-CPO therefore measures the additional contribution of how the penalty is distributed across directions.

2. Paired comparison. Out ablation, 50 paired seeds. Method columns report mean regret / mean Crossing, where Crossing is the whole-allocation bootstrap self-switch probability. Gains are DC-CPO⁻ minus DC-CPO; positive values favor DC-CPO. Crossing gains are in percentage points (pp), and intervals are paired-seed bootstrap 95% confidence intervals.

DATASETCPO+DC-CPO⁻DC-CPOREGRET GAIN [95% CI]CROSSING GAIN, PP [95% CI]
DGP1.1121 / 0.85441.1001 / 0.84951.0862 / 0.84310.0139 [0.0035, 0.0235]0.64 [0.50, 0.78]
Twins0.7207 / 0.73290.7033 / 0.72860.6839 / 0.72070.0194 [0.0020, 0.0204]0.79 [0.56, 1.04]
NHANES1.3880 / 0.79681.3152 / 0.77241.2969 / 0.76610.0183 [0.0062, 0.0304]0.63 [0.47, 0.79]
ACTG-1751.6386 / 0.81751.5460 / 0.79861.5169 / 0.78790.0292 [0.0141, 0.0441]1.07 [0.84, 1.30]

Gains use the paired seed-level estimates; displayed method means are rounded.

All reported paired intervals are above zero.

Appendix C.7 now includes this paired ablation, and Section 4 explains the incremental role of direction weighting.

Q4 — Costs and individual benefit weights appear in the formulation. How are they tested in the experiments?

Answer: The original experiments already use heterogeneous costs with equal benefit weights; the supplementary comparisons test zero costs and individual benefit weights. DC-CPO has lower regret than CPO+ under the tested individual weights on all four datasets.

1. Utility specification and experimental setup. Known costs and individual weights translate CATE into decision utility through b=r+Bτb=r+B\tau. The main setting uses ri=−cir_i=-c_i, ci∼Unif(0.3,1.2)c_i\sim\mathrm{Unif}(0.3,1.2), and Bi=1B_i=1; allocation-independent baseline terms are constants. The added comparisons use zero costs and Bi=1+1{Xi1>0}B_i=1+\mathbf1\{X_{i1}>0\}, applying each utility consistently in training, validation, and evaluation.

Section 6 now clarifies the utility specification, and Appendix C.7 includes the comparison.

2. Experimental results. Out regret gain = CPO+ − DC-CPO [95% CI], 20 paired seeds; positive values favor DC-CPO. Compare methods within each column's utility.

DATASETZERO COST, EQUAL WEIGHTSHETEROGENEOUS COSTS, EQUAL WEIGHTSHETEROGENEOUS COSTS + INDIVIDUAL REWEIGHTING
DGP0.0447 [0.0090, 0.0585]0.0052 [0.0021, 0.0536]0.2679 [0.1635, 0.3804]
Twins0.0191 [0.0143, 0.0548]0.0066 [0.0015, 0.0570]0.0989 [0.0212, 0.1819]
NHANES0.0227 [0.0128, 0.0854]0.0785 [0.0331, 0.1231]0.1680 [0.0079, 0.3321]
ACTG-1750.1245 [0.0141, 0.2427]0.1130 [0.0302, 0.1955]0.5478 [0.3461, 0.7533]

We would welcome your feedback on whether we have addressed your concerns, and we would be happy to continue the discussion and provide any further clarification to support your re-evaluation.

Reviewer_8PjeOpenReview ↗
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2(+1)
Confidence
2
Informativeness
1
Presentation
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Soundness
2
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Paper summary

The paper addresses the practically important problem of learning causal-benefit predictions for constrained treatment allocation. The proposed boundary-sensitive regularizer is intuitively motivated: prediction errors that change the selected allocation deserve particular attention.

Critical strengths

The problem is practically important. And the general idea, updating the benefit prediction using decision-boundary regularizer, makes sense.

Critical weaknesses

The theoretical contribution appears limited relative to established results. Lemma 2.2 follows directly from the standard AIPW estimator; Proposition 3.2 adapts from the existing SPO+ framework; Theorem 3.3 is weak, as the disappearance of the bias term under either correctly specified nuisance model follows directly from the standard doubly robust property of AIPW. Theorem 5.2 additionally requires correct outcome regression and conditional residual symmetry, a more restrictive condition than the ealier doubly robust condition. Finally, the oracle inequality in Eqs. (23)–(24) leaves the nuisance and geometry estimation errors unspecified. These limitations make it difficult to assess what substantive guarantees the theory provides for the implemented iterative algorithm.

Questions for authors
  1. Please refine your notation throughout the paper. Just to name a few, Γη\Gamma_\eta represents AIPW estimates while Γn\Gamma_n represent error in Eq.22 are confusing; the ξS(u)\xi_S(u) function seems to be the same function as V∗()V*(), please do not introduce extra notation if not necessary.

  2. Theoretical novelty. Please identify which theoretical results are new and which adapt established results. Several statements follow from standard AIPW or SPO+ properties, making the principal theoretical advance difficult to identify.

  3. Assumption 5.1. Please explain the role and practical plausibility of conditional residual symmetry, and clarify which guarantees remain valid when only the propensity model is correct.

  4. Additional ablation. The DC-CPO−^{-} ablation is informative, but retains boundary projections and active-boundary selection. Please additionally compare against CPO+ augmented with an ordinary squared-error penalty on the DR pseudo-benefits, with comparable tuning, to isolate the benefit of boundary-sensitive regularization.

  5. Hyperparameter selection. Appendix C.2 reports fixed values for ρ,ε,W,\rho,\varepsilon,W, and TT. How were these selected, and how sensitive are the results to these choices? Please explain how they would be selected for a new dataset.

6 comments

We clarify the technical contribution and assumptions and add regularization controls.

Q1 — Please distinguish AIPW scores from error bounds and simplify the duplicate value-function notation.

Answer: We distinguish Γ, the AIPW score, from Eₙ, the uniform empirical-to-population deviation bound. We use a single value function, V∗(u) = max {uᵀw : w ∈ S}, replacing the duplicate support-function notation.

The support function of S − S is then V∗(u) + V∗(−u).

These notation changes are applied consistently throughout Eqs. (22)–(24), the value-function definitions, and the corresponding proofs.

W.a–c / Q2 — Several results follow from AIPW or SPO+. Which theoretical results are new, and what is the principal advance?

Answer: Our principal contribution is the allocation-geometry characterization of decision-sensitive causal errors and its translation into a trainable boundary penalty. AIPW conditional-mean robustness and the SPO+ surrogate provide the established foundations.

1. The scientific problem. Causal prediction measures error in benefit levels, whereas allocation stability depends on error projected onto contrasts between feasible allocations, relative to the margins separating them.

2. Geometry and a trainable penalty. Theorem 4.1 expresses this relationship as a decision-invariance certificate through DFI, and Theorem 4.3 bounds crossing probability using directional margins and uncertainty. DC-CPO makes this analysis trainable by selecting nearby allocation boundaries and penalizing projected pseudo-benefit errors. Proposition 5.3 connects the observable penalty to weighted directional benefit error: with geometry fixed and either nuisance model correct, the two differ by a predictor-independent noise term.

A concrete implication is that uncertainty ellipsoids with the same eigenvalues, total variance, and volume can have threefold different DFI values solely because their orientations relative to an allocation boundary differ (Appendix B.2.1). This gives a principle for directing learning precision toward the errors that matter under a specified set of constraints.

3. Established foundations and the advance. Lemma 2.2 uses standard conditional-mean double robustness, Proposition 3.2 adapts SPO+ to benefit maximization, and Theorem 3.3 transfers its surrogate-risk control to causal regret, with the bias term vanishing when either nuisance model is correct. Appendix A expands the comparison with SPO+ and treatment-effect ranking.

W.d / Q3 — Why is conditional residual symmetry needed, how plausible is it, and which guarantees remain when only the propensity model is correct?

Answer: Conditional residual symmetry, together with correct outcome regression, supports Fisher consistency and is plausible for conditionally symmetric additive noise. When only the propensity model is correct, the conditional-mean, causal-regret, and fixed-geometry directional-error results remain valid under their stated conditions.

1. Role and plausibility of symmetry. Under Assumption 5.1, the DR pseudo-benefit is symmetric around the true benefit, allowing the true coefficient to minimize the population objective in Theorem 5.2. Heteroskedastic Gaussian noise is one example. Treatment-specific residual diagnostics can help assess plausibility; skewness and outcome-model misspecification can violate the assumption.

2. Guarantees with a correct propensity model. Specifically, Lemma 2.2 retains its conditional-mean DR property, and Theorem 3.3 retains its zero-bias specialization. Proposition 5.3 also retains its directional-error decomposition under the fixed-geometry and moment conditions. Theorem 5.4 additionally depends on its uniform-deviation and approximate-optimization premises. Fisher consistency in Theorem 5.2 requires the stronger conditions in Assumption 5.1 because conditional mean correctness alone does not determine the expected nonlinear allocation loss.

Section 5 now clarifies this distinction, and Appendix B summarizes the assumptions required for each guarantee.

W.e–f — The nuisance and geometry errors are unspecified. What guarantee does the oracle inequality provide for the implemented iterative algorithm?

Answer: Theorem 5.4 gives a population-risk guarantee for a fixed-geometry inner fit, conditional on uniform deviation and approximate empirical minimization. The bound separates the effects of sampling, nuisance estimation, geometry estimation, and inner optimization.

1. Inner fitting and outer updates. In the algorithm, each inner solve holds the current directions and weights fixed; the outer update then rebuilds that geometry.

2. Nuisance and geometry errors. To make the two estimation terms explicit, write L^λ(f;η,G)\widehat L_\lambda(f;\eta,G) for the complete empirical surrogate-plus-penalty objective, with fixed reference nuisance functions η0\eta_0 and geometry G0G_0. Define

\Delta_{n,\eta} &=\sup_{f\in\mathcal F}\left|\widehat L_\lambda(f;\widehat\eta,G_0)-\widehat L_\lambda(f;\eta_0,G_0)\right|,\\ \Delta_{n,\mathrm{geom}} &=\sup_{f\in\mathcal F}\left|\widehat L_\lambda(f;\widehat\eta,\widehat G)-\widehat L_\lambda(f;\widehat\eta,G_0)\right|. \end{aligned}$$ The first term changes pseudo-benefits at fixed geometry; the second changes geometry while retaining the estimated pseudo-benefits. Both include the regularization strength λ. **3. Population-risk guarantee.** If $L_\lambda^0$ is the reference population objective, its uniform sampling deviation is bounded by $\mathcal E_n^0$, and the inner optimization tolerance is $\epsilon_{\mathrm{opt}}$, the transfer argument gives $$L_\lambda^0(\widehat f)-\inf_{f\in\mathcal F}L_\lambda^0(f) \le 2\bigl(\mathcal E_n^0+\Delta_{n,\eta}+\Delta_{n,\mathrm{geom}}\bigr)+\epsilon_{\mathrm{opt}}.$$ The total deviation is $\mathcal E_n=\mathcal E_n^0+\Delta_{n,\eta}+\Delta_{n,\mathrm{geom}}$. Here, $\widehat f$ is an $\epsilon_{\mathrm{opt}}$-approximate minimizer of the empirical objective at $(\widehat\eta,\widehat G)$. This compares predictors under the same reference population objective, including its surrogate and boundary penalty. The estimation terms depend on nuisance accuracy and boundary stability. The outer iteration count controls how often the geometry is refreshed, and Q5 reports its empirical effect for the specified supplementary implementation. Appendix B.3.3 now includes these definitions and the transfer argument, and Section 5.3 explicitly states the inner-fit scope. > **Q4 — Does boundary-sensitive regularization improve on CPO+ with an ordinary squared-error penalty on DR pseudo-benefits under comparable tuning?** **Answer:** Our boundary-sensitive penalty yields **lower mean Out regret** than the ordinary squared-error penalty on all four datasets under both fixed-λ and validation-selected comparisons. **1. Controls and tuning protocol.** To isolate the boundary contribution, we augment CPO+ with ordinary squared error on raw cross-fitted DR pseudo-benefits (ISO-raw), retaining the CPO+ surrogate without boundary selection, directional projections or boundary weights. We also include ISO-denoised as an additional target variant; ISO-raw is the primary control for our raw-DR formulation. **2. Experimental comparison.** Out regret, mean (SE), over 50 paired seeds per dataset; fixed penalties use λ=0.3, while selected penalties use the same five-value λ grid and validation pseudo-regret. | DATASET | CPO+ | DC FIXED .3 | ISO RAW FIXED .3 | ISO DENOISED FIXED .3 | DC SELECTED | ISO RAW SELECTED | ISO DENOISED SELECTED | | -------- | --------------- | --------------- | ---------------- | --------------------- | --------------- | ---------------- | --------------------- | | DGP | 1.1121 (0.0412) | 1.0862 (0.0355) | 1.1048 (0.0370) | 1.1081 (0.0402) | 1.0724 (0.0375) | 1.1153 (0.0380) | 1.0980 (0.0390) | | Twins | 0.7207 (0.0283) | 0.6839 (0.0265) | 0.6936 (0.0251) | 0.7100 (0.0277) | 0.6877 (0.0255) | 0.7015 (0.0263) | 0.7133 (0.0281) | | NHANES | 1.3880 (0.0445) | 1.2969 (0.0417) | 1.3268 (0.0417) | 1.3629 (0.0438) | 1.3257 (0.0425) | 1.3408 (0.0469) | 1.3535 (0.0436) | | ACTG-175 | 1.6386 (0.0460) | 1.5169 (0.0406) | 1.6029 (0.0511) | 1.6160 (0.0445) | 1.5216 (0.0409) | 1.5624 (0.0425) | 1.6200 (0.0441) | The ISO-raw comparison supports an incremental regret benefit from boundary-sensitive regularization beyond an ordinary prediction penalty across the tested datasets. Appendix C.7 now includes this ordinary-penalty ablation and its tuning protocol alongside the DC-CPO⁻ comparison.

Q5 — How were ρ, ε, W, and T selected, how sensitive are the results to them, and how should they be chosen for a new dataset?

Answer: We select ε = 0.05 using validation DR pseudo-regret, then set W = 1/ε² = 400 to match the upper bound of the inverse-margin weights.

1. Validation selection. The added ε sweep follows the main experimental workflow, using raw DR targets and fixing W = 400. Among {0.001, 0.01, 0.05, 0.1, 0.2}, ε = 0.05 yields the lowest validation DR pseudo-regret on both datasets: 16.2192 on DGP and 18.3306 on ACTG-175. The two curves are included in revised Appendix C.5. As described there, λ = 0.3 is selected by minimizing validation DR pseudo-regret averaged across the synthetic-DGP seeds and then fixed across the main experiments.

2. Weight-cap rule. For nonnegative margins Δ, (Δ + ε)⁻² ≤ ε⁻². Thus ε = 0.05 gives an upper bound of 400, which determines our default W. At fixed ε = 0.05 and the same margins, any W ≥ 400 produces identical weights; smaller W introduces additional clipping.

3. Other parameters and new datasets. We use ρ = 1 and T = 4 as common defaults. The https://anonymous.4open.science/r/Hyperparameter-selection-and-sensitivity-425D/ examines ρ and T in the denoised-target, inverse-directional-variance variant using 50 paired seeds. Increasing T from 4 to 8 changes mean Out regret by +0.0043 on DGP and −0.0044 on ACTG-175. For a new dataset, we recommend selecting λ, ρ, ε, and T using held-out DR pseudo-regret, then setting W = 1/ε². Nuisance models and boundary geometry use training data, and the test set is reserved for final evaluation.

Appendix C.5 now includes the ε-validation curves and the rule linking ε to W.

We are eager to know whether we have addressed your questions, and we would be happy to discuss further at any time to assist with your re-evaluation.

Reviewer_dNw5OpenReview ↗
Rating
3
Confidence
2(−1)
Informativeness
2
Presentation
2(−1)
Soundness
2
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Paper summary

This paper introduces Causal Predict-then-Optimize (CPO) and Decision-Calibrated Causal Predict-then-Optimize (DC-CPO), a framework that aligns causal machine learning with downstream operational decisions rather than statistical accuracy alone. In real-world resource allocation, traditional causal models can fail because they treat all prediction errors equally, whereas errors near optimization boundaries drastically alter final decisions and cause high regret. By combining doubly robust causal estimation with decision-focused learning and a boundary-sensitive regularizer, the proposed methods explicitly penalize prediction errors along decision-relevant directions. With synthetic and semi-synthetic benchmarks, the paper showed that the new method significantly reduces downstream regret and prevents costly decision-boundary crossings.

Critical strengths
  • this paper provided an interesting framework that bridges causal inference with decision-focused learning. It extends the Predict-then-Optimize paradigm to settings with unobserved counterfactuals by successfully combining doubly robust estimation with decision regret minimization.
  • the paper introduced the Decision Fragility Index (DFI) to mathematically formalize how directional causal prediction errors interact with optimization boundaries, shifting the focus from uniform statistical error to decision-relevant accuracy.
  • theoretically, this work provided formal boundary-crossing probability bounds and an oracle inequality, while consistently demonstrating lower downstream regret against traditional prediction-oriented causal learners across benchmarks.
Critical weaknesses
  • Decision-focused learning (DFL) and the computation of a boundary-sensitive regularizer can incur high computational overhead. Calculating active boundaries or the Decision Fragility Index (DFI) may struggle to scale to high-dimensional constraint matrices or massive sample sizes.
  • theoretical guarantees relied on a "fixed decision geometry." In real-world environments, operational constraints, budgets, and feasible regions can frequently shift dynamically, which could undermine the regularizer's effectiveness.
Questions for authors
  • the doubly robust estimation helps with confounding, but the boundary-sensitive penalty relies on having enough data density near the decision thresholds. In regions with limited data or poor overlap, propensity score variance could cause the regularizer to misidentify active boundaries?
2 comments

Thank you for the suggestion! We have added runtime comparisons and robustness tests.

W1 — Active-boundary construction and DFI may be costly for high-dimensional constraints or large samples. How do they scale?

Answer: At batch size 16, the supplementary denoised-target DC-CPO implementation adds 0.43–0.55 seconds over CPO+, taking 1.34–1.49 seconds in total. Scaling to larger problems depends on allocation-oracle cost and the number of candidate boundary directions.

1. Training complexity. DC-CPO adds four rounds of boundary construction and regularized fitting to CPO+; each round includes solving the regularized subproblem. With J batches of size b, p predictor parameters, at most K candidate directions per batch and A retained directions overall, penalty construction costs O[J(Cor+Ccand+Kb)+A(bp+p2)]O[J(C_{\mathrm{or}}+C_{\mathrm{cand}}+Kb)+A(bp+p^2)] per round, where CorC_{\mathrm{or}} and CcandC_{\mathrm{cand}} are per-batch allocation and candidate-generation costs. The penalty changes the quadratic objective without adding fitting variables.

By comparison, MSE-DR costs O(Np2+p3)O(Np^2+p^3) for N training individuals; MAE-DR and CPO+ require convex optimization, with CPO+ additionally invoking allocation oracles.

2. DFI computation. For DFI, given R stored bootstrap predictions and K candidate directions, covariance estimation and direction evaluation cost O((R+K)b2)O((R+K)b^2) per batch; bootstrap refitting is additional.

3. Measured runtime. Supplementary timing of the denoised-target implementation with four outer updates; seconds, mean (SD).

DATASETMSE-DRMAE-DRCPO+DC-CPO (T=4)
Synthetic DGP0.055 (0.001)0.789 (0.028)1.011 (0.066)1.437 (0.103)
Twins0.053 (0.001)0.777 (0.018)0.871 (0.097)1.338 (0.151)
NHANES0.054 (0.001)0.796 (0.022)0.941 (0.089)1.486 (0.110)
ACTG-1750.051 (0.001)0.777 (0.023)0.892 (0.042)1.403 (0.072)

Appendix C.7 now includes the complexity analysis, timing comparison and table, and scaling analysis.

W2 — The guarantees assume fixed decision geometry, but budgets and feasible regions can change. How does this affect the method?

Answer: When budgets change, we update the allocation oracle and can refit the predictor using the new boundary geometry. In the tested capacity shift, DC-CPO retains lower regret than CPO+ with both frozen and refitted predictors on all four datasets.

1. Changing the feasible region. For the new feasible set S', the bound RS′(b^,b0)≤∣b^−b0∣\*diam⁡∣⋅∣(S′)R_{S'}(\widehat b,b_0)\le\\|\widehat b-b_0\\|_\*\operatorname{diam}_{\\|\cdot\\|}(S') still holds, although the previously learned directions and margins need not transfer. Both tables report mean regret relative to the corresponding oracle and paired 95% confidence intervals for DC-CPO minus CPO+.

2. Capacity-shift experiment. We compare frozen predictors, using only the new allocation oracle, with refitted predictors trained for the new constraints on the same data and hyperparameter rule.

Total/group capacities (5,4)→(2,1)(5,4)\to(2,1), batch size 16.

DATASETFROZEN CPO+FROZEN DC-CPODC−CPO [95% CI]REFIT CPO+REFIT DC-CPODC−CPO [95% CI]
Synthetic DGP0.67090.6592−0.0117 [−0.0248, −0.0096]0.89090.7158−0.1751 [−0.2438, −0.1037]
Twins0.55460.5454−0.0092 [−0.0348, −0.0053]0.58460.5418−0.0428 [−0.1317, −0.0342]
NHANES0.71240.6794−0.0330 [−0.0894, −0.0204]0.79890.6653−0.1336 [−0.1977, −0.0779]
ACTG-1750.73670.6746−0.0621 [−0.1258, −0.0042]0.77010.6871−0.0830 [−0.1678, −0.0009]

Every reported paired interval is below zero.

3. Covariate-shift experiment. Separately, we shift test covariate X2X_2 by δ\delta in the DGP without retraining, keeping the conditional response mechanism, costs and constraints fixed.

X2→X2+δX_2\to X_2+\delta on the synthetic DGP.

SHIFT ΔCPO+ REGRETDC-CPO REGRETDC−CPO [95% CI]
01.05021.045−0.0052 [−0.0528, −0.0015]
0.51.12411.114−0.0101 [−0.0563, −0.0055]
11.30011.2758−0.0243 [−0.0845, −0.0235]

Our method retains lower regret at every tested shift even as both methods' regret increases, supporting robustness of the relative advantage within this tested range.

Appendix C.7 now includes these shift protocols and tables and describes the evaluated changes alongside the robustness results.

Q1 — Can poor overlap or sparse data near decision thresholds cause the regularizer to misidentify active boundaries?

Answer: Poor overlap or sparse local support can cause active-boundary misidentification by increasing benefit-estimation error.

1. Boundary-identification error. For a fixed allocation contrast d, the margin error satisfies ∣(b^−b0)⊤d∣≤∥b^−b0∥∞∥d∥1|(\widehat b-b_0)^\top d|\le\|\widehat b-b_0\|_\infty\|d\|_1; weak overlap or sparse local support can therefore change active-set membership when estimation errors exceed the distance to a margin threshold. This connects reliable boundary identification to local estimation accuracy and motivates the following stress tests.

2. Weak-overlap and long-tail tests. To examine your concern, we increase the propensity-logit scale from γe=1\gamma_e=1 to 2 and, separately, construct a long-tail subgroup comprising the top 15% of X6X_6, with a +4 logit shift and true net benefits near the allocation cutoff. The table reports out-of-sample regret / crossing; lower values are better.

DATASETSETTINGMSE-DRMAE-DRCPO+DC-CPO
Synthetic DGPWeak overlap1.8506 / 0.89221.8035 / 0.86931.5375 / 0.86031.3113 / 0.8448
Synthetic DGPLong-tail1.6564 / 0.88541.5493 / 0.85391.4214 / 0.84171.2006 / 0.8064
ACTG-175Weak overlap2.5495 / 0.84092.4561 / 0.77382.3313 / 0.79132.2062 / 0.7853
ACTG-175Long-tail2.0759 / 0.84992.1365 / 0.85382.0150 / 0.87141.7272 / 0.8642
Online NewsWeak overlap1.4986 / 0.78441.6918 / 0.71921.4543 / 0.69251.3450 / 0.6360
Online NewsLong-tail1.3641 / 0.80121.4531 / 0.79991.2954 / 0.77021.1858 / 0.7636
NHANESWeak overlap1.9292 / 0.84911.7814 / 0.79771.6929 / 0.75411.6288 / 0.7157
NHANESLong-tail1.7217 / 0.89051.6512 / 0.89771.6995 / 0.87121.5827 / 0.8502

Across these eight settings, our DC-CPO achieves lower mean regret than all three comparators and lower crossing than CPO+, showing that the regret and stability advantages over CPO+ persist under these weak-overlap and long-tail perturbations.

Appendix C.7 now includes these weak-overlap and long-tail results and makes the dependence on reliable boundary estimation explicit.

Comments on the paper

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AuthorsOpenReview ↗

General response to the reviewers and Area Chair

General response to the reviewers and Area Chair

We thank the reviewers for their careful assessment and suggestions. Our responses address four areas:

  1. Theoretical contribution and assumptions. We explain how allocation geometry leads to DFI, a directional crossing bound, and a trainable boundary penalty, distinguish these contributions from the AIPW and SPO+ foundations, and clarify notation, symmetry, and the inner-fit guarantee (8Pje Q1–Q3 and W.e–f, 7GTS Q1).
  2. Computational cost and robustness. We provide complexity and timing comparisons, together with experiments under changed capacities, covariate shifts, weak overlap, and sparse treatment regions (dNw5 W1–W2 and Q1).
  3. Source of the empirical gains. We compare with ordinary squared-error penalties and ranking adaptations, strengthen prediction-baseline selection, and quantify the incremental benefit of directional weighting. The stronger MSE baseline achieves lower PEHE while DC-CPO retains lower regret (8Pje Q4, 7GTS Q1–Q2 and W2).
  4. Stability and practical use. We connect DFI to allocation changes, test costs and individual benefit weights, and explain hyperparameter selection (7GTS Q3–Q4, 8Pje Q5).

The revised appendices include the supplementary protocols and results, with targeted main-text revisions to notation and the assumptions attached to each guarantee.

Thank you again for the time and care invested in these reviews. We welcome further questions and would be happy to discuss any aspect of the revision.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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