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Under review as a conference paper at ICLR 2027

Optimizing the Bias–Uncertainty Trade-off with Partially Ordered Bias Bounds

Abstract

We study the problem of aggregating multiple estimators to optimize the bias–uncertainty trade-off, especially when latent bias bounds are known only through their ordering and estimator uncertainties are represented by intervals. This problem naturally arises in hyperparameter tuning when candidate estimators cannot be directly validated, as in off-policy evaluation and pointwise nonparametric function estimation. However, existing methods cannot straightforwardly handle multidimensional hyperparameters for general estimator families because the associated bias bounds are only partially ordered. To address this issue, we formalize the aggregation of partially ordered intervals by minimizing the worst-case oracle-approximation ratio, leading to a novel aggregation rule called Optimal Aggregation of Confidence Intervals (OACIS). Our main contribution is a comprehensive theoretical analysis of this minimax problem, including the boundedness of the oracle ratio, uniqueness of the solution when this ratio is finite, stability, statistical error guarantees, and a linear-time algorithm. We also evaluate OACIS in synthetic and real-data experiments.

Primary area:
learning theory
Keywords:
Hyperparameter tuning, Lepski's principle, off-policy evaluation

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
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Paper summary

The paper studies aggregation of scalar interval estimators when their uncertainty radii are observed but their bias bounds are known only through a partial order. It asks for the output minimizing the worst-case ratio to an oracle that knows the compatible bias bounds and chooses the smallest bias-plus-uncertainty bound. The resulting rule, OACIS, has a closed-form characterization and is unique whenever the minimax ratio is finite. The paper establishes sharp uniform bounds under a subadditivity condition on the radii, relates bounded inefficiency to Lipschitz stability, and derives statistical oracle inequalities with estimated scales and a plug-in confidence level.

Critical strengths
  1. The exact minimax characterization makes the abstract problem tractable. It eliminates the unknown surrogate estimands and bias values while preserving the adversarial problem. Proposition 4.1 then expresses the epigraph through finitely many interval constraints, and Theorem 4.1 reduces feasibility to pairwise intersection on the real line. This gives an exact answer for each observed input, rather than only a uniform performance guarantee. The treatment of zero denominators and the separate uniqueness argument when the optimum ratio equals one make the characterization convincing, including at degenerate inputs.

  2. The boundedness results explain what partial-order information can and cannot provide. Theorem 4.2 establish a sharp bound for non-total meet-semilattices under radius subadditivity, with explicit matching constructions. Corollary 4.1 shows that no uniform finite oracle ratio is possible for a non-total meet-semilattice. The negative result makes the additional assumption meaningful and prevents the partial-order extension from being presented as cost-free.

  3. Stability is an additional reason to aggregate, and it supports a substantive statistical analysis. Theorem 4.3 goes beyond existence or optimality by bounding changes in the output in terms of changes in interval centers and radii. Remark 4.3 provides a useful contrast: bounded-inefficiency selection rules must sometimes jump between distinct midpoints, whereas continuous OACIS can remain stable.

Critical weaknesses
  1. The experiments use the confidence rule beyond the assumptions of the MAE guarantee. Section 5 assumes strictly positive scales, a finite scale ratio, and, for Proposition 5.2, almost-sure bounds σv,σ^v∈[c,C]\sigma_v,\widehat\sigma_v\in[c,C] with c>0c>0. This is transparently specified, but its statistical status needs clarification. In particular, the last step of Equation (25) in Appendix G.2 (p. 28) uses ρσv≥σmax⁡\rho\sigma_v\geq\sigma_{\max} for every candidate in the oracle minimum. Computing a finite ratio after omitting the zero-scale candidate does not preserve that step for the full family. The issue is substantive even when the nonzero scale is known exactly. Consider a two-element chain with target and both surrogate estimands equal to zero, both bias bounds zero, m^1∼N(0,1)\widehat m_1\sim N(0,1), interval [m^1−z,m^1+z][\widehat m_1-z,\widehat m_1+z] for finite z>0z>0, and abstention interval [0,0][0,0]. An extension of Equation (12) that retains abstention in its oracle minimum while using the finite ratio from the other candidate would have a zero right-hand side. However, for a realization m^1>z\widehat m_1>z, Equations (8)–(9) give the positive output (m^1−z)(m^1+2z)/(m^1+z).(\widehat m_1-z)(\widehat m_1+2z)/(\widehat m_1+z). In particular, m^1=2\widehat m_1=2 and z=1z=1 give 4/34/3. Since such realizations occur with positive probability, the MAE is positive. This is a counterexample to that unchanged extension, not to the stated positive-scale theorem.

  2. The real-data bias order is plausible as a modeling choice, but its oracle interpretation remains underdeveloped. The distinction between actual biases and their bounds is important here. Section 3 requires ordered upper bounds, so nonmonotonicity of the actual biases would not invalidate the framework. Indeed, a monotone upper envelope can always be constructed, but it may be substantially larger than the actual bias of a favorable candidate, thereby weakening the oracle benchmark. The substantive question is therefore whether sufficiently informative ordered bias bounds exist in the proposed application. The empirical κ=1\kappa=1 subadditivity reported in Section 7.2 concerns the constructed uncertainty radii and does not establish the usefulness of the assumed bias order. This limits the extent to which the real-data experiment validates the substantive bias-ordering assumption, without undermining the abstract minimax results. A sufficient condition separating the history-truncation error from the omitted-reward contribution, with appropriate uniformity over the other hyperparameter, would help justify the proposed two-dimensional bias order.

  3. The real-data comparison lacks uncertainty information needed to assess the size and reliability of the advantage. Table 7.2 reports NMAE 0.754 for OACIS versus 0.843 for SLOPE++, a difference of 0.089, with marginal standard errors 0.074 and 0.078. Those marginal errors do not determine the standard error of the paired difference, because both methods are evaluated on the same 25 dates. The Pearson p-values concern correlation with the reference outcome, not a comparison between methods. The reported ordering of the point estimates is clear while the precision of that ordering is not.

Questions for authors
  1. What statistical claim is intended for the B.5 calibration after abstention is excluded from ρ^\widehat\rho? In particular, is the desired oracle comparison restricted to non-abstaining candidates, or is the rule intended as a heuristic extension? A scope clarification can resolve the mismatch with Equation (12). A claimed guarantee for the full candidate family would need to address the zero-benchmark example above. A targeted comparison on the existing data with abstention removed would show how much this extension contributes to the reported performance.

  2. Can the two-dimensional bias order in Appendix B be supported by a bound that separates residual history dependence from the reward discarded by the exposure indicator? The useful answer would explain why the bound remains informative while being monotone in both coordinates, rather than requiring monotonic actual biases. Such a result would strengthen the application substantially.

  3. Can the OACIS–SLOPE++ comparison be accompanied by uncertainty for the paired MAE difference, together with user counts and the precision of the A/B reference outcomes? Please explain how the analysis treats repeated users and dependence across dates. This would establish whether Table 7.2 supports a reasonably precise advantage over the strongest baseline or should be interpreted mainly as an encouraging case study.

3 comments

Thank you for highlighting the limitation of Proposition 5.2 for zero-width abstention and for your detailed questions about Web OPE. Our General Response and Revision Summary (a separate post) presents the theoretical extensions, experimental revisions, and planned Web OPE analyses relevant to your questions. Please read it alongside the specific responses below.


Q1. Zero-width abstention and its ablation

Please refer to the general response, specifically Section I.2 for the theoretical treatment and Section III for the ablation study.

Q2. Joint bias bound for history truncation and discarded rewards

Please refer to Section I.2 in the general response.

Q3. Paired uncertainty, reference precision, and repeated users across dates

Please refer to Section III in the general response. We also clarify that there should be some dependency across dates due to the repeated users and the result should be treated as more of an encouraging result rather than statistically significant evidence.

Thank you for the clarification and revisions. I appreciate the additional theoretical analyses and experiments. The extension of the MAE guarantee to plug-in Wald intervals and the treatment of zero-width abstention substantially address my original concern. The additional experiments also strengthen the empirical evaluation. Some concerns remain regarding the practical tightness of the assumed bias bounds. Overall, I think the revisions have addressed most of my original concerns, and I am inclined to raise my assessment.

Thank you for reviewing our revisions and for your encouraging feedback! Your constructive comments have helped us strengthen both the theoretical analysis and the empirical evaluation.

Reviewer_cq4DOpenReview ↗
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Paper summary

The paper considers a situation where several methods estimate the same unknown quantity, but it is difficult to check which estimate is closest to the truth. Each estimate comes with an interval describing its uncertainty. The method also needs information about which estimates have smaller bounds on systematic error, called bias. Some pairs of estimates may not be comparable in this way.

The proposed method, OACIS, combines this information to return one estimate. The authors give mathematical guarantees and test the method using simulated data and a web recommendation example. The web example asks how much a new recommendation policy changes clicks, using data collected under an existing policy.

Critical strengths
  1. The paper addresses a useful problem. When several estimates disagree and there is no direct way to check them, a rule for combining them could be helpful. The authors explain mathematically how their method compares with a hypothetical choice that knows the bias bounds. They also study how the output changes when the input estimates change slightly. I see value in these results, although I do not have enough experience to judge all aspects of their originality.

  2. The experiments provide encouraging evidence. The web experiment has a sensible basic design: estimates made from the existing policy’s data are checked against an A/B comparison involving the new policy.

Critical weaknesses
  1. The real-data example needs more explanation and evidence. The method needs an ordering of bias bounds, but I could not find a clear justification for the particular ordering used in the web example. I would also like more evidence that the uncertainty intervals are reliable. The A/B comparison itself is an estimate with sampling noise. The paper should report how many users were involved, how uncertain that comparison is, and whether OACIS’s improvement over SLOPE++ is convincing when the methods are compared on the same dates. The reported errors of 0.754 and 0.843 favor OACIS, but the summary table alone does not show how reliable that difference is. This limits how strongly I can interpret the real-data result.

  2. More comparisons are needed to show when OACIS helps. Most methods compared in the paper choose one estimate, while OACIS can combine information from several estimates. It would help to compare with simple averaging and other methods that combine estimates. In the independent test, simple averaging had error 0.209 in the second condition, compared with 0.429 for OACIS. Averaging was much worse in the other two conditions, so it is not a better method in general. This result still shows that the current comparisons do not tell the whole story. The methods also use different interval widths and handle the ordering differently. Comparisons using the same intervals would make it easier to see where OACIS’s benefit comes from.

Questions for authors
  1. Could you add a small numerical example before the main formulas, showing the target, the candidate estimates, their uncertainty intervals, and the known ordering of bias bounds?

  2. What assumptions justify the bias ordering used in the web experiment? How did you check that the uncertainty intervals were reliable for that data?

  3. How many users were in each A/B group, and how uncertain were the daily A/B differences? Could you show how reliably OACIS beats SLOPE++ when comparing their errors on the same dates, allowing for dates that may be related?

  4. How do simple averaging and other methods that combine estimates perform? Does OACIS still improve the results when competing methods use the same uncertainty intervals?

  5. Please clarify which mathematical guarantees cover the exact experimental setup. For example, the web experiment includes an estimate fixed at zero with no uncertainty, while Section 5 assumes positive uncertainty scales. The simulated uncertainty estimates can also fall outside the fixed limits assumed for the average-error guarantee. Can the results be extended to cover these choices, or should those parts of the implementation be described as practical choices without the stated guarantee?

3 comments

Thank you for your constructive review and suggestions for improving the presentation and empirical comparisons. Our General Response and Revision Summary (a separate post) summarizes the new theoretical results and expanded evaluation. Please read it alongside our responses to your questions below.


Q1. A small numerical example

Figure 1.1(a) now illustrates the candidate intervals, target, and OACIS output.

Q2. Web OPE bias ordering and reliability of uncertainty intervals

Please refer to Sections I.1 and I.2 in the general response.

Q3. A/B group sizes, reference precision, and paired comparisons

Please refer to Section III in the general response.

Q4. Simple aggregation and comparisons with matched intervals

The revised evaluation uses Mobile Health and Spatial Adaptation, both with the mean of midpoints as a simple baseline. Figure 7.1 also includes SLOPE and SLOPE++ with exactly the same confidence intervals as OACIS, labeled "calibrated." Additional Web OPE comparisons are pending clearance, as described in Section III of the general response. Please also refer to Sections II.1–II.3 of the general response and Appendix A.2 of the revised paper.

Q5. Statistical guarantees for abstention and estimated scales

Please refer to Sections I.1 and I.2 in the general response.

The revision addresses several major concerns and gives stronger support for acceptance. I would retain weak acceptance, with more confidence than before. Remaining concerns are mainly the private web evidence, conditional application assumptions, and presentation—not a demonstrated failure of the method.

Thank you for your follow-up and encouraging feedback!

Let us address your remaining comments on presentation and the application assumptions.

Presentation

We have worked to make the presentation as clear and accessible as possible, including adding Figure 1.1(a) to provide a concrete illustration of OACIS early in the paper. We would be grateful for any specific suggestions that could help us improve the presentation further.


Application assumptions

We will clarify the basis for the Web OPE assumptions stated in Appendices D.6–D.7 by adding the following tables to the manuscript:

Assumptions for Theorem D.1 in Section D.6 (bias bound)

ConditionCategoryJustification
Correct propensities and overlap (Assm. D.1)Satisfied by designThese are ensured by the design of the behavior and target policies.
Bounded reward (Assm. D.2)Satisfied by designThe per-user reward is either 0 or 1.
Exponential forgetting (Assm. D.3)Key modeling assumptionWe assume that the effects of past recommendations on user behavior decay exponentially fast. (Note: the exponential rate can be weakened to an arbitrarily slow rate without breaking the bias-bound order)
Exposure by the evaluation date (Assm. D.4)Satisfied by designOnly users with a prior impression are included in the A/B test.

Assumptions for Theorem J.1 in Section J.5 (MAE bound)

ConditionCategoryJustification
Independent usersTypical modeling assumptionWithin each date, we model user trajectories as i.i.d. conditional on the fixed policies, treating cross-user interactions as negligible on our large-scale web platform.
Positive variance of population IFTypical modeling assumptionFollows from the assumption that the reward is noisy, conditional on the logged history.
Reviewer_177kOpenReview ↗
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2
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2
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2
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3
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Paper summary

This paper studies how to aggregate estimators of a scalar quantity when their accuracy cannot be directly validated. Each candidate is represented by an interval around a possibly biased surrogate, and the available bias information is a partial order on unknown upper bounds. The authors propose OACIS, which minimizes the worst-case error relative to the oracle benchmark R⋆=min⁡v(bv+uv)R^\star=\min_v(b_v+u_v), where bvb_v is a bias bound and uvu_v is the interval radius. They derive an exact characterization of the aggregate, sharp bounds on its oracle ratio, stability results, and an algorithm whose running time is linear in the size of the graph representing the order. Under additional statistical assumptions, they obtain quantile and mean absolute error guarantees with estimated confidence radii. The method is evaluated on synthetic examples and a real off-policy evaluation task.

Critical strengths
  1. The exact minimax analysis is the main strength of the paper. In particular, the distinction between total and partial orders, together with the sharp bounds under radius subadditivity, explains what can and cannot be achieved using only the intervals and their bias order (Section 4.1). This provides useful insight into the additional difficulty of aggregation with multiple hyperparameters.

  2. The stability result gives a concrete advantage of aggregation over selecting a single candidate, i.e., the output can remain stable when the interval centers and widths are perturbed. The authors then use this property to derive statistical guarantees with estimated uncertainty (Theorem 4.3 and Section 5). Together with the efficient algorithm, this makes the theoretical development fairly complete.

Critical weaknesses
  1. My main concern is whether the oracle benchmark is informative in the intended applications. The assumption concerns ordered upper bounds on bias, and such bounds can always be constructed by taking the largest actual bias among a candidate’s predecessors. Their existence therefore does not ensure that the bound for a good candidate is reasonably tight. In the real OPE example, the order on history length and impression duration is motivated by qualitative beliefs, without deriving a useful joint bias bound for the modified estimator relative to the daily policy effect (Appendix B.4). This leaves an important gap between the abstract guarantee and its practical interpretation.

  2. The empirical evidence does not sufficiently resolve this concern. The only real application uses 25 dates and evaluates against estimated A/B differences, which share Group A data with the candidate estimators. Table 7.2 reports better performance for OACIS, but does not quantify uncertainty in the paired improvement over SLOPE++ or assess the effect of noise in the reference values. The separate standard errors and correlation p-values do not answer these questions. Therefore, I am not yet convinced that the observed improvement establishes a reliable advantage in estimating the underlying policy effects.

Questions for authors
  1. For the modified OPE estimator in Appendix B.2, under what assumptions does increasing history length or impression duration lead to a reasonably tight, jointly monotone bias bound relative to the daily policy effect? A concrete derivation, together with an explanation of when the uncertainty scales have a small subadditivity constant, would help establish that the oracle guarantee is useful for this application.

  2. Which guarantees in Section 5 apply to the implementation in Appendix B? In particular, please clarify how the Wald intervals meet the simultaneous coverage and tail requirements used for the MAE bound. The zero-width abstention candidate also falls outside the positive-scale assumptions of Proposition 5.2. Can the corresponding guarantee be stated precisely, including whether its oracle comparison includes abstention?

  3. Can you provide a paired uncertainty analysis for the improvement over SLOPE++, accounting for any dependence across dates? Please also report the A/B group sizes and uncertainty in the reference differences, and assess whether their shared use of Group A data could materially affect the comparison. These details would help determine how much confidence to place in the real-data result.

1 comment

Thank you for your careful review and detailed questions about the bias ordering, statistical guarantees, and Web OPE evaluation. Our General Response and Revision Summary (a separate post) summarizes the main revisions and responses to concerns shared across the reviews. Please read it alongside the point-by-point replies below.


Q1. Joint bias bound and uncertainty subadditivity in Web OPE

Please refer to Section I.2 of the general response. Although we do not derive a theoretical upper bound on κ\kappa for this particular OPE problem, we note that κ\kappa can be roughly estimated from the subadditivity κ^\widehat \kappa of σ^\widehat \sigma. For instance, we have confirmed κ^≤1\widehat \kappa\le 1 for Web OPE experiment.

Q2. Applicability of the statistical guarantees and zero-width abstention

Please refer to Sections I.1 and I.2 of the general response.

Q3. Additional analysis and concerns on the web OPE experiment

Shared Group A data

Thank you for raising this concern. For the reported MAE comparison, adding the observed Group A mean to both the effect predictions and the A/B reference leaves every absolute error unchanged. This expresses the same evaluation as comparing target-policy value predictions constructed from Group A alone against the held-out Group B mean.

Paired uncertainty, A/B group sizes and reference precision

Please refer to Section III in the general response.

Comments on the paper

5 comments
AuthorsOpenReview ↗

General Response and Revision Summary

We thank the reviewers for their careful reading and constructive feedback. Their comments have helped us clarify the scope of our theoretical guarantees and strengthen the empirical evaluation.

The following two concerns were raised across the reviews:

  • The weak connection between the theory and the experiments.
  • The limited insights provided by the existing experiments on both synthetic and real data.

To address these concerns, we have made the following main changes in this revision:

  • Extended the theory to more practical settings (Sections J.5 and J.6).
  • Substantially expanded the simulated-data experiments (Section 7).
  • Repositioned the Web OPE experiment as an encouraging case study (Section D).

Meanwhile, additional Web OPE experimental results have not yet been incorporated into the paper because clearance is taking time.

Below, we summarize the main points of these changes. Section I presents the additional theoretical analyses, and Section II summarizes the additional empirical results. Finally, Section III discusses the prospects for disclosing additional information about the Web OPE experiment. These additions strengthen the connection between our theory and its practical application, while providing a more comprehensive empirical evaluation.

I. Additional theoretical results

We have added theoretical results to bridge the gap between theory and experiments. First, we address issues that arise when combining Wald CIs with OACIS on real data. Next, we address discrepancies between the theory and the specific setting of the Web OPE experiment.


I.1 Extension of the MAE bound for plug-in Wald intervals

Plug-in Wald intervals are approximate confidence intervals based on the central limit theorem and an estimated scale. When they are directly supplied to OACIS, two issues prevent direct application of the MAE bound (Proposition 5.2). First, condition iii), namely σ^v∈[c,C]\widehat \sigma_v \in [c,C] almost surely, may not hold. Second, because m^v\widehat m_v is generally not normally distributed in finite samples, the coverage condition (Eq. (11)) may not hold. We show that the conclusion of Proposition 5.2 continues to hold under certain regularity conditions even in this case, and that, together with the results in Section I.2, the MAE of OACIS in all experiments, including the additional experiments, is covered by our theoretical guarantees. For the theoretical details, please refer to Appendix J.5 of the revised paper; for the applications to each experiment, see B.2, C.3, and D.7.


I.2 Analysis for Web OPE experiment

Here, we have added two theoretical analyses.

Order-compatible bias bound. Under assumptions based on Hu and Wager's notion of uniform mixing, we can derive a bias bound between the Web OPE candidate estimand ηt,h,ℓ\eta_{t,h,\ell} and the daily policy effect θt⋆\theta_t^\star that is monotone in both the history length hh and the impression-effect duration ℓ\ell. Under suitable assumptions, there exist constants C≥0C\ge0 and 0<β<10<\beta<1, and a finite positive measure independent of h,ℓh,\ell, denoted by Pˉ\bar P, such that

∣ηt,h,ℓ−θt⋆∣≤bt(h,ℓ):=C2βh+∫(1−Eℓ)rt dPˉ.|\eta_{t,h,\ell}-\theta_t^\star|\le b_t(h,\ell):= \frac{C}{2}\beta^h+ \int (1-E_\ell)r_t\,d\bar P.

holds. Here, EℓE_\ell indicates whether an impression occurred within the past ℓ\ell days. The first term decays geometrically in hh, and the second is nonincreasing as ℓ\ell increases. Furthermore, under an additional assumption concerning impressions,

lim⁡h→∞,ℓ→∞bt(h,ℓ)=0.\lim_{\substack{h\to\infty,\\ \ell\to\infty}}b_t(h,\ell)=0.

Thus, this bias bound is nontrivial and can be regarded as informative in this sense.

MAE bound with zero-width abstention. As pointed out, Proposition 5.2 assumes positive scales and therefore cannot be applied directly when the inputs include zero-width abstention. However, a similar MAE bound continues to hold. Let V\mathcal V denote the candidate family excluding abstention, and adjoin a zero-width candidate with fixed output η⊤\eta_\top as the greatest element ⊤\top. Then, for κ≥1\kappa\ge1 and under the corresponding conditions of either Proposition 5.2 or Section I.1 above,

\le\lbrace2\kappa+o(1)\rbrace \min_{v\in\mathcal V}\lbrace b_v+\bar u_v(t^\star)\rbrace$$ holds. Here, $\widetilde\theta_{\widehat t}$ is the OACIS output after adding abstention, and the calibration and calibrated uncertainty $\bar u_v(t)$ are defined on the original candidate family $\mathcal V$. In other words, the zero-width candidate acts as a “harmless” prior-like anchor: it pins the OACIS aggregate to $\eta_\top$ whenever $\eta_\top$ lies in every original input interval, while preserving the oracle MAE bound over the original candidates for $\kappa\ge1$. For details of the bias bound, please refer to Appendix D.6 of the revised paper; for the zero-width abstention result and its application, see J.6 and D.7.

II. Additional empirical results

The previous synthetic-data experiments covered only three scalar estimation settings and did not provide a comprehensive quantitative evaluation. In addition, the Web OPE experiment is based on 25 dependent days of data, making it difficult to establish a statistically supported performance advantage. Accordingly,

  • We removed the previous synthetic-data experiments and moved the Web OPE experiment to the appendix as an encouraging case study.
  • In their place, we expanded the numerical experiments as follows to evaluate performance more reliably and from multiple perspectives.
Analysis \ ExperimentMobile HealthSpatial Adaptation
Main analysisFigure 7.1(a), Appendix BFigure 7.1(b)–(e), Appendix C
Matched confidence calibrationFigure 7.1(a), Appendix A.2Figure 7.1(b)–(e), Appendix A.2
Bias-order ablationFigure 7.2(a), Appendix A.3Figure 7.2(b)–(e), Appendix A.3

Sections II.1 and II.2 below give an overview of the two new benchmark tasks and their results. Sections II.3 and II.4 summarize the objectives and results of matched confidence calibration and bias-order ablation.


II.1 Mobile Health (MH)

We evaluated performance using the setting of an existing study on OPE in POMDPs [1]. The candidate estimators are very similar to those used in Web OPE, but their bias ordering has already been established in the original study, allowing direct application of the result in Section I.1. The results show that OACIS/d-OACIS achieve lower MAE than Mean, SLOPE, and SLOPE++ at all sample sizes. For details, please refer to Section 7.1 and Appendix B of the revised paper.


II.2 Spatial Adaptation (SA)

We evaluated performance on four classical benchmark tasks for local adaptivity in regression: Doppler, Bumps, HeaviSine, and Blocks [2]. We establish a simple bias upper bound that respects the product order on the bandwidth and ridge penalty of Gaussian kernel ridge regression, theoretically justifying the bias order supplied to OACIS. The results show OACIS's competitive performance against other local adaptation methods across all tasks. In particular, OACIS/d-OACIS achieve lower MAE than all other comparison methods on Bumps and Blocks, which feature narrow peaks and abrupt jumps, respectively, demonstrating their ability to adapt locally. Meanwhile, LOOCV, which performs global adaptation, achieves the lowest MAE on HeaviSine, whose localized irregularities are relatively few and mild. These results illustrate both the advantages and limitations of the proposed methods. For details, please refer to Section 7.2 and Appendix C of the revised paper.


II.3 Matched Confidence Calibration

In both benchmarks, we added comparisons in which SLOPE and SLOPE++ receive the same intervals as OACIS, labeled (calibrated). The results show that OACIS's performance gains cannot be explained by confidence-level calibration alone. For details, please refer to Figure 7.1 and Appendix A.2 of the revised paper.


II.4 Bias-order Ablation

In response to several questions about how useful the oracle bias bound is, we conducted additional analyses on MH and SA. Specifically, we measured the performance degradation caused by randomly shuffling the candidate estimators on the theoretically derived bias-order DAG, quantifying the usefulness of the correct bias order. The results show that the MAE averaged over random assignments significantly increases for OACIS/d-OACIS in MH and all four SA signals, supporting the usefulness of the supplied bias order. The effects on SLOPE/SLOPE++ were less consistent across random assignments. For details, please refer to Figure 7.2 and Appendix A.3 of the revised paper.


References

[1]: Yuchen Hu and Stefan Wager. Off-policy evaluation in partially observed Markov decision processes under sequential ignorability. The Annals of Statistics, 51(4):1561–1585, 2023.

[2]: David L. Donoho and Iain M. Johnstone. Ideal spatial adaptation by wavelet shrinkage. Biometrika, 81(3):425–455, 1994.

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