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Under review as a conference paper at ICLR 2027

When Comparison Is Easier Than Evaluation: Learning Better Randomization Designs

Abstract

Randomization identifies treatment effects, but its dependence structure controls precision. Across repeated cohorts, practitioners may choose among independent assignment, matching, rerandomization, and balancing schemes that all preserve treatment probability one half. Learning the most precise law from observed outcomes seems impossible: quadratic risk depends on both potential outcomes, yet only one is observed. We show that comparison escapes this obstruction. Centered sign designs share a unit covariance diagonal, so subtracting two risks removes the unobserved within-unit products. Under independent fair reference assignment, no absolute risk is universally unbiasedly estimable from one cohort without outcome restrictions, whereas every pairwise risk difference is. This identity yields Prediction-Augmented Comparative Randomization Learning (\PCRL): occasional reference rounds and simulated ghost assignments provide sampler-only unbiased contrasts, while an inverse-reference residual corrects any clipped predictable contrast model. Optimistic mirror descent gives finite-horizon expected regret against a fixed finite contextual-policy class, and cohort-size weighting converts it into expected excess-MSE control for unequal cohorts. Fresh centered deployment preserves deterministic-horizon unbiasedness and yields an exact MSE identity; bounded equal-size cohorts additionally admit anytime-valid confidence sequences. Polynomial-hint \PCRL improves on vanilla \CRL in all 17 controlled synthetic cells (–; median ). Against a raw linear plug-in from the same misspecified predictor class, it improves by – throughout a contiguous 16/36-cell region at , with all 16 pointwise seed-level 95% confidence intervals excluding zero, and remains below Bernoulli risk across the full surface.

Primary area:
causal reasoning
Keywords:
Causality, Experimental design

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_f9GWOpenReview ↗
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Paper summary

From our understanding, the authors use outcomes from previous cohorts to compare candidate randomization schemes in terms of efficiency of ATE estimation. Since it is not possible to (universally) unbiasedly estimate the risk associated with one design from a single cohort without restrictions on the potential outcomes, the authors use an independently randomized cohort to estimate risk difference, and then use this result to guide selection of the randomization scheme for subsequent cohorts.

Critical strengths

The theoretical results appear to be mathematically sound.

Critical weaknesses

First, Theorem 3.1, which is presented as one of the main contributions of the paper, is a special case of Proposition 1 in Harshaw, Middleton, and Savje (2026). Although the submission does cite Harshaw, Middleton, and Savje (2026), it does not explicitly identify Theorem 3.1 as this specialization of Proposition 1. Second, we have found numerous issues in the experiments. Most importantly, the submission's procedure is often found to be worse than the comparators (sometimes significantly so). First, the improvement over vanilla CRL is generally small, especially when compared with the gap to the polynomial plug-in. In Table 6, the contextual risk ratios relative to Bernoulli assignment are 0.222 for vanilla CRL, 0.212 for PA-CRL with a "polynomial hint", and 0.079 for the polynomial plug-in. PA-CRL also does worse than the polynomial plug-in in all 12 pxT cells (Figure 7b) and on the WDBC and Bike datasets (Table 6). Importantly, the polynomial plug-in is not an oracle, since it uses current covariates and previously observed outcomes, without access to current potential outcomes or risks (Appendices J.2 and K). One might then ask, why not simply use the polynomial plug-in in these settings? We understand that PA-CRL provides a robust regret guarantee, but the additional guarantee does not seem to justify the trade-off with the loss in precision. Further, several experiments simply verify algebraic identities or that simulated regret lies below a loose upper bound. These do not really establish that the method chooses better designs. For reference, in Appendix L (Figure 10), the reported regret is about 0.2 under a bound of about 1.7 at T=256. Ultimately, these experiments do not add anything substantive besides simple checks. Moreover, Figure 3b highlights the favorable comparisons, while graying out the unfavorable ones. On the other hand, Table 8 shows losses as large as 190.8% relative to the plug-in, which are instead omitted from Figure 3b. These values should instead be shown together with the favorable ones in Figure 3b.

Generally, the submission is very hard to read, and the lack of clarity significantly obscures the paper's contributions, if any. We did not identify mistakes in the derivations we checked, although the theory currently reads as a central observation (which is a direct specialization of an existing result) embedded into an overextended framework. Finally, the experiments leave a lot to be desired.

Questions for authors
  • Considering that polynomial plug-in significantly outperforms PA-CRL in many settings, why should a practitioner choose PA-CRL? Does the robust regret guarantee practically justify such a substantial loss in efficiency?

  • Could the authors clarify what Figure 10 tells us about practical design-selection performance, beyond validating the implementation and regret decomposition? In particular, how do the observed regret and theoretical bound compare with the regret of simple baselines at the same horizons, and does the bound actually certify an improvement over any of these baselines?

4 comments
AuthorsOpenReview ↗

Thanks for the review and here is the kind response

Design precision depends on the conditional second moment, including cross-unit covariance Ω. A polynomial model may estimate u = E[μ|G] consistently while the risk ℓₕ = (uᵀΣₕu + tr(ΣₕΩ))/(4n²) favors a different law. Appendix N.6 gives a general criterion: with a unique mean-greedy ranking, an expected γ-per-cohort gap to a fixed admissible policy, and mean-selection error probabilities pₜ, PA-CRL’s expected cumulative advantage is at least γT − Σₜpₜ − B_T. Thus γT > Σₜpₜ + B_T certifies lower risk. An exact n = 4 construction has a nonzero linear mean and unique wrong mean-greedy choice. At T = 512, ε = .05 and η = .411325, the theorem bounds PA risk by .030746, below the mean-oracle plug-in’s .070313 and independence/uniform’s .039063. Both methods receive the correct mean; the certificate uses dense reference scores and analytical η. A fixed-parameter reproduction with five fresh sign paths and 4,096 histories each gives learned-hint PA risk .015034 versus learned polynomial’s .069511: 78.37% [78.18%, 78.56%] lower. The .030746 bound covers the exact-mean-hint variant (Appendix N.6).

The separate mean-zero latent-cohort test finds lower PA-CRL risk than the strong polynomial in 18/18 random-coefficient settings, with 14 pointwise paired 95% intervals favoring PA. The mean cell-specific reduction is 15.04% [11.34%, 18.75%]. All 18 fixed-coefficient controls and both enhanced baselines remain in the complete 36-cell report (Appendix N.7).

The original matched-linear experiment identifies a complementary robustness regime: PA-CRL reduces risk by 3.4–42.3% in all 16 cells with interaction weight β≥.625\beta\ge .625, with every pointwise seed-level 95% interval excluding zero. We added the complete signed comparison, quantified reference cost, and evaluated the requested same-instance baselines for Figure 10. The strong polynomial plug-in appears alongside PA-CRL throughout.

For navigation, W1–W3 denote the review's theory, experiment, and presentation concerns; W2a–c separate baseline performance, diagnostic evidence, and signed-grid presentation. Q1–Q2 retain the order of Questions for Authors.

1. W1: Theorem 3.1 and the contribution beyond estimability.

Theorem 3.1 is precisely the independent-reference specialization of Proposition 1 in Harshaw, Middleton, and Sävje (2026). We now state this relationship immediately before the theorem and in the contribution statement. Writing μ=a+b\mu=a+b, the quadratic form expands as

μ⊤Aμ=a⊤Aa+2a⊤Ab+b⊤Ab.\mu^\top A\mu=a^\top Aa+2a^\top Ab+b^\top Ab.

Under independent fair assignment, the incompatible potential-outcome pairs are exactly (ai,bi)(a_i,b_i), whose cross-product coefficients are 2Aii2A_{ii}. Thus the HMS criterion becomes diag⁡(A)=0\operatorname{diag}(A)=0. Every centered-design difference A=Σh−ΣgA=\Sigma_h-\Sigma_g satisfies this condition automatically.

The scientific question is how to use that comparison information to choose the next cohort's assignment law while preserving treatment-effect inference. Three steps make this operational. First, ghost assignments compute unbiased contrasts from sampling access to the candidate laws, avoiding dense covariance construction. Second, predictable contrast forecasts are corrected with randomized reference feedback; the resulting variance calculation identifies both reference noise and forecast error. Third, the corrected feedback gives fixed-policy regret and, through cohort-size weighting, excess-MSE control, while fresh centered deployment preserves unbiased effect estimation. The two-unit reversal in Proposition 3.3 explains why feedback identification matters: deployment-correlated scoring changes a true contrast of +1/32+1/32 into an expected score of −1/4-1/4, reversing the preferred design. We explicitly attribute the augmented inverse-propensity correction and optimistic mirror descent to their established sources. The contribution is their constructive use for outcome-relevant assignment-law learning, with the feedback and inference conditions stated together.

2. W2a / Q1: Competitive design selection and the operating regime.

W2a(i): A feasible strong baseline.

The complete evidence distinguishes two questions. Adding polynomial forecasts improves the audited learner over vanilla CRL in all 17 original controlled synthetic cells, by 1.83–10.28% (median 5.66%). Comparing against the strong polynomial plug-in yields a different ordering: that plug-in leads in all 12 phase-grid cells and all five contextual horizons. At T=1024T=1024, the three-context risk ratios are 0.222 for vanilla CRL, 0.212 for PA-CRL, and 0.079 for the polynomial plug-in. These values now appear directly with the main comparison. The polynomial selector uses current covariates and its own completed observed outcomes. In the original zero-effect replays, PA-CRL/polynomial risk ratios are .438/.356 on WDBC and .810/.656 on Bike (Section 7). The added heterogeneous-effect replays retain that feasible comparator and test reference feedbac

AuthorsOpenReview ↗

Thanks for the review and here is the kind response(cont'd)

k when only one potential outcome is observed.

W2a(ii) / W2c: Complete signed comparison under misspecification.

The matched linear-predictor experiment measures the benefit of correcting structural ranking errors. Its complete grid is below. Entries are 100(1−RPA/Rlinear)100(1-R_{\mathrm{PA}}/R_{\mathrm{linear}}): positive favors PA-CRL; negative favors the raw linear plug-in.

Interaction weight β\betaT=128T=128T=256T=256T=512T=512T=1024T=1024
0−190.83−164.53−148.85−137.43
.125−177.72−147.24−130.30−117.82
.250−115.14−92.44−79.17−69.72
.375−57.07−45.17−39.21−34.25
.500−19.91−11.33−6.66−1.49
.625+3.36+13.37+20.69+26.28
.750+17.41+27.51+33.76+38.25
.875+22.19+32.45+37.98+42.25
1+17.19+24.54+29.82+31.55

This uses every one of the 73,728 method/history records: eight populations and 128 histories per population, cell, and method. There are 16 favorable and 20 unfavorable point estimates; pointwise paired t7t_7 intervals exclude zero in all 16 favorable and 19 unfavorable cells. Figure 3b now shows every signed value on one symmetric color scale, including the 190.8% loss. Figure 3e includes all nine interaction-weight trajectories. The favorable region therefore has an explicit boundary: correction pays off under sufficiently strong interaction misspecification, while accurate ranking makes direct modeling more efficient.

W2a(iii) / Q1: Independent comparisons against the strong polynomial.

The new mechanism study fixes p = 8, T = 512, n = 12, 24, 48, one or three observed contexts, and three coefficient spectra. Each of six methods selects one global configuration from eight candidates using risk/Bernoulli on six simulator-calibration settings, two populations and 32 histories, then freezes it before the complete 36-cell test on five fresh populations and 128 histories each. Random and fixed coefficients share the same coefficient norm, expected uniform-X response RMS and outcome bound. All learners receive the same covariates/context and actual law information, and only their own completed outcomes.

In the prespecified random18 family, PA minus strong-polynomial risk/Bernoulli is −.078532 [−.095458, −.061605]; each population first averages all 18 cells equally, followed by a paired t4t_4 interval across populations. PA has lower risk in 18/18 cells, with 14 pointwise intervals below zero. The polynomial plug-in leads in all 18 fixed controls; the combined all36 difference is +.000175 [−.008402, .008751]. Every-cohort pair-IPW and the full PSD second-moment plug-in have lower risk than PA in all 36 cells. This mean-zero family has tied mean rankings; the unique-ranking, nonzero-mean certificate in N.6 is a separate analytical construction.

In the earlier independent ten-setting study, calibrated PA-CRL improves on separately calibrated vanilla CRL in 10/10 terminal point estimates, with nine paired intervals favoring PA; the polynomial plug-in leads in 9/10 settings (Appendix N.5). The original fixed ε = .1, η = 4 study remains in Appendix N.3.

A separate frozen-parameter transfer reused ε = .01 and η = 256 with the original matched linear hint on four fresh populations and retained all 36 cells. PA-CRL had lower risk than the matched linear plug-in in 18/36 cells, with 17 pointwise paired 95% intervals favoring PA-CRL; the strong archived polynomial plug-in had lower risk in all 36 (Appendix N.5). This additional test is distinct from the original eight-population grid above.

3. Q1: Quantifying the efficiency cost of reference cohorts.

Let UU be PA-CRL's total risk ratio, VV its non-reference policy's risk ratio along the recorded history, and PP the polynomial plug-in ratio. With ϵ=.1\epsilon=.1,

U=.1+.9V,U−P=.1(1−V)+(V−P).U=.1+.9V,\qquad U-P=.1(1-V)+(V-P).

The first term is the direct reference surcharge; the second is the selection gap. The original three-context campaign gives:

TTPA-CRL UUPolynomial PPNon-reference VVReference surchargeSelection gap
512.254402.081974.171558.082844.089584
1024.212033.079389.124481.087552.045092

At T=1024T=1024, direct reference cost accounts for 66.0% of the .132644 gap. This exact accounting holds the learned policy path fixed; changing the reference rate also changes subsequent feedback and learning. For a practitioner, the measured comparison is therefore between the observed benefit of correcting wrong rankings and this explicit precision cost.

4. W2b / Q2: Same-horizon baselines and the Figure 10 certificate.

We evaluated the simple baselines on exactly Figure 10's frozen two-policy instance, with n=8n=8, ϵ=.05\epsilon=.05, M=8M=8, η=12\eta=12, and the exact contrast as the predictable hint. Entries are cumulative normalized-risk regret against the pair design; each OMD estimate uses 30,000 paths

AuthorsOpenReview ↗

Thanks for the review and here is the kind response(cont'd)

.

TTPA-CRLZero-hint OMDTheorem boundIndependentUniformPair / correct-ranking plug-in
16.047117.057085.162918.139375.0696870
32.065112.090447.268073.278750.1393750
64.081955.125468.478384.557500.2787500
128.109953.160541.8990071.115000.5575000
256.165703.2167811.7402512.2300001.1150000

The bound certifies improvement over always-independent assignment at T=32,64,128,256T=32,64,128,256. It exceeds uniform-selection regret and correct-ranking plug-in regret at every displayed horizon. Observed PA-CRL regret improves on zero-hint OMD and uniform selection; a correctly ranking plug-in chooses the best design immediately and has zero regret. At T=256T=256, PA-CRL's .165703 regret separates into .111500 reference excess and .054203 exploitation excess. Figure 10 thus identifies the source of the guarantee and its looseness; the learned-predictor experiments establish practical design-selection performance under the declared model specifications.

5. W3: Readability and presentation.

Section 2 adds the operational sequence before the formal notation: predict relative risks, select a law, collect occasional reference feedback, and correct the next policy update. The revision places the HMS specialization immediately beside Theorem 3.1 and explains feedback computation, policy learning, and inference by their operational roles. Section 7 now begins with competitive design-selection comparisons; the new appendix puts the complete signed grid, reference-cost decomposition, and matched-horizon baselines together. This gives a direct path from each claim to its assumptions and numerical evidence.

The blue revision makes the attribution explicit in Sections 1, 3–5, shows the complete Figure 3 comparison in Section 7, and reports protocols, full results, and reference-cost accounting in Appendix N.

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.

Just like Reviewer LJfs, I have the same impression that the response is purely AI-generated. It is effectively unreadable. I will not change my score.

Reviewer_LJfsOpenReview ↗
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Paper summary

The paper is unreadable to me:

  • It feels like every sentence references some chain of thought that the reader clearly doesn't have access to so it's impossible to follow what is being said.

  • The notation is classic LLM-y slop of defining a ridiculous number of variables.

I see no evidence at all of any human touch anywhere. I have to wonder: If the paper isn't worth the author's time, why should anyone read it?

Nonetheless, I tried to understand it by (I literally couldn't bear reading it) passing it to AI and asking it to explain the main idea to me. Here's my understanding from an AI reading:

The general problem is from treatment effect estimation: In every cohort, random variable Z_i \in \{+1, -1} is drawn for patient ii, where Zi=1Z_i=1 indicates treatment and Zi=−1Z_i=-1 indicates control. There's covariance to the design given by the matrix E[ZZT]=ΣhE[Z Z^T] = \Sigma_h where hh is the design. Our goal is to estimate the treatment effect τ=sumiai−bi\tau = sum_i a_i - b_i, i.e., aia_i is the outcome under the treatment and bib_i is the outcome under the control. Of course, we can only ever observe aia_i or bib_i. After assigning each individual, we observe either aia_i or bib_i, and build an unbiased estimator τ^\hat{\tau} from a weighted combination of the outputs. With a little algebra, we can write τ−τ^=mu⊤Z\tau - \hat{\tau} = mu^\top Z where mui=ai+b+imu_i = a_i+b+i. Then the mean squared error is clearly μ⊤Σhμ\mu^\top \Sigma_h \mu. This is the objective we want to minimize.

Of course, the MSE depends on the unknown values μ\mu. The setup of the paper is to sample once from a candidate design h′h' to get an unbiased estimate PP of μ\mu, i.e., Pi=μi+Zi(ai−bi)=2aiP_i=\mu_i + Z_i (a_i - b_i) = 2a_i if ii is in the treatment and 2bi2b_i otherwise. PP is a random sample but they can then use it to estimate the MSE i.e., EP[PTΣhP]=∑i(ai−bi)2+μ⊤Σhμ.E_P [P^T \Sigma_h P] = \sum_i (a_i - b_i)^2 + \mu^\top \Sigma_h \mu.

That is, the MSE plus an unknown constant that depends on μ\mu. The title refers to the fact that if we subtract some other Σg\Sigma_g then we can get an unbiased estimate of the relative MSE between designs hh and gg, i.e.,

EP[PT(Σh−Σg)P]=μ⊤Σhμ−μ⊤Σgμ.E_P [P^T (\Sigma_h - \Sigma_g) P] = \mu^\top \Sigma_h \mu - \mu^\top \Sigma_g \mu.

An extension they consider: Sometimes the design is complicated and its covariance isn't explicitly available so you can "ghost" estimate it by simply drawing GG from the design.

From here, the idea is to have an iterative sequence of experiments and use a candidate design to get GG then estimate the MSE improvement by switching to another design, update the design, and repeat. There are all the things you'd expect: theoretical statements about when this is possible, complicated regret bounds, some experiments comparing to naive baselines since this appears to be an uncommon iterative setup.

Critical strengths

I think the main idea as I described it above is somewhat interesting. I feel like I learned something here equivalent to what I'd expect from an informative blog, although I probably most of it is just getting the treatment effect problem back into my head.

Critical weaknesses

This paper is clearly end-to-end AI slop. I've had conversations with an AI where I go "Oh this is a cool idea, how would you implement the algorithm?" And it outputs a random string of heuristic steps. Fortunately, I've understood that the answer is slop. I think the authors had such a conversation and then followed up by saying "Okay, now turn it into an ICLR paper."

Generally, I think basically all the ideas clearly appear in the AI's training data and have just been mismashed together in a different order for this paper. If this were written by people, I'd be more willing to engage with the ideas. Even then, I think the novelty is marginal: an obvious idea for a marginally interesting iterative treatment effect estimation problem with lots of overlap to prior work.

Here are specific problems, AI written:

The clearest overlaps with prior work are:

  1. Theorem 3.1 specializes HMS’s estimability characterization. Proposition 1 of Harshaw, Middleton, and Sävje states that a quadratic form is unbiasedly estimable exactly when its coefficients vanish on pairs of potential outcomes that cannot be jointly observed. Expanding gives μ⊤Aμ=a⊤Aa+2a⊤Ab+b⊤Ab\mu^\top A\mu = a^\top Aa + 2a^\top Ab + b^\top Ab. Under independent assignment, the only unobservable products are aibia_i b_i, whose coefficients are 2Aii2A_{ii}. HMS’s criterion therefore reduces exactly to Aii=0A_{ii}=0, giving the manuscript’s characterization. The risk-comparison conclusion follows because all candidate covariance matrices have the same diagonal.

  2. Proposition 4.2 uses the standard augmented inverse-probability estimator. Its correction has the form m+I(D^−m)/ϵm+I(\widehat D-m)/\epsilon: a prediction plus an inverse-probability-weighted residual. Its unbiasedness and variance decomposition are the known-propensity, conditional version of the calculation in Dudík, Langford, and Li’s Doubly Robust Policy Evaluation and Learning, particularly Theorem 2. Applying that calculation to a design-risk contrast changes the target, but does not introduce a new correction principle.

  3. The learning inequality underlying Theorem 5.1 is standard optimistic mirror descent. Lemma 3 of Rakhlin and Sridharan’s Online Learning with Predictable Sequences gives the same regularizer-over-learning-rate plus squared-prediction-error bound. With negative entropy on the policy simplex, it becomes log⁡∣E∣/η+(η/2)∑t∥Gt−Mt∥∞2\log|\mathcal E|/\eta+(\eta/2)\sum_t\|G_t-M_t\|_\infty^2, exactly the manuscript’s intermediate inequality (18). The remaining steps substitute the corrected contrast estimates, take expectations, and account for reference-round cost. The contribution should therefore be assessed as an application of this established machinery.

  4. Proposition C.3 is a direct consequence of the existing Gram–Schmidt Walk guarantee. Theorem 6.6 of Harshaw et al.’s Balancing Covariates in Randomized Experiments with the Gram–Schmidt Walk Design gives sub-Gaussianity of BZBZ. Substituting v=λB(B⊤B)−1uv=\lambda B(B^\top B)^{-1}u gives the manuscript’s exponential bound; the covariance bound follows from it. The manuscript acknowledges the source, but this proposition should not count as an independent theoretical advance.

The experimental concerns are:

  1. All four real-data replays remove the missing-counterfactual difficulty motivating the paper. Appendix I.5 explicitly sets ai=bia_i=b_i for RAND HIE, and Appendix K does the same for WDBC, Wine Quality, and Bike Sharing. Consequently, P=2Y=μP=2Y=\mu regardless of assignment. With known candidate covariances, the current-cohort risk contrasts can therefore be computed exactly from observed outcomes. These experiments still test sequential design selection, but they do not validate the correction under unequal potential outcomes. The synthetic experiments do include nonzero and heterogeneous effects.

  2. A stronger plug-in baseline consistently outperforms the proposed method in substantial parts of the evaluation. Appendix K reports that polynomial-hint PA-CRL beats the polynomial plug-in in 0 of 12 phase-grid cells. In Table 7, even the best PA-CRL tuning has normalized risk 0.171, compared with 0.082 for the polynomial plug-in. Improving over independent assignment does not establish an advantage over a competitive design-selection baseline.

  3. The gains depend strongly on deliberately restricting the predictor. Table 8 excludes the interaction term from both methods’ linear predictors while increasing its importance in the outcome model. PA-CRL has lower point-estimate risk in 16 of 36 cells; the plug-in has lower risk in the other 20. In the worst cell, PA-CRL’s risk is 190.8% higher. This supports a specific benefit under substantial model misspecification, rather than general superiority. These adverse results are disclosed in the appendix.

  4. There is no end-to-end comparison with an important alternative that the manuscript itself identifies. Proposition C.1 permits inverse-probability-weighted risk contrasts from correlated assignments when the required pairwise assignment probabilities are positive and known. Mixing in independent assignment supplies positive support. An all-cohort learner using these contrasts would test whether restricting identifying feedback to reference rounds is worthwhile. Appendix I.8 examines pair-IPW variance in a small diagnostic, but does not provide that learning comparison. This baseline is especially relevant in the finite experiments where assignment laws can be enumerated; it is less straightforward in the general sampler-only setting.

Questions for authors

Why?

5 comments
AuthorsOpenReview ↗

Thanks for the review and here is the kind response

Design precision depends on the conditional second moment, including cross-unit covariance Ω. A polynomial model may estimate u = E[μ|G] consistently while the risk ℓₕ = (uᵀΣₕu + tr(ΣₕΩ))/(4n²) favors a different law. Appendix N.6 gives a general criterion: with a unique mean-greedy ranking, an expected γ-per-cohort gap to a fixed admissible policy, and mean-selection error probabilities pₜ, PA-CRL’s expected cumulative advantage is at least γT − Σₜpₜ − B_T. Thus γT > Σₜpₜ + B_T certifies lower risk. An exact n = 4 construction has a nonzero linear mean and unique wrong mean-greedy choice. At T = 512, ε = .05 and η = .411325, the theorem bounds PA risk by .030746, below the mean-oracle plug-in’s .070313 and independence/uniform’s .039063. Both methods receive the correct mean; the certificate uses dense reference scores and analytical η. A fixed-parameter reproduction with five fresh sign paths and 4,096 histories each gives learned-hint PA risk .015034 versus learned polynomial’s .069511: 78.37% [78.18%, 78.56%] lower. The .030746 bound covers the exact-mean-hint variant (Appendix N.6).

The separate mean-zero latent-cohort test finds lower PA-CRL risk than the strong polynomial in 18/18 random-coefficient settings, with 14 pointwise paired 95% intervals favoring PA. The mean cell-specific reduction is 15.04% [11.34%, 18.75%]. All 18 fixed-coefficient controls and both enhanced baselines remain in the complete 36-cell report (Appendix N.7).

The original matched-linear experiment retains its robustness result: 3.4–42.3% lower deployment risk in all 16 cells with β ≥ 0.625, across T = 128, 256, 512, 1024, with every pointwise paired 95% interval excluding zero. The numbered replies follow the review’s presentation concerns, four theoretical overlaps, four experimental concerns, and final question.

1. Summary concerns: main idea, algorithm, and notation. A hospital network chooses its next cohort's randomization law. Independence, matching, and rerandomization preserve treatment probability one half but differ in precision. The procedure has five steps: predict each design's risk relative to independence using completed cohorts, draw a reference indicator, deploy independent assignment on reference rounds and the learned sampler otherwise, use fresh simulated assignments to score every candidate on reference rounds, correct prediction residuals and update the policy. Simulated assignments require no additional outcomes. The covariance-diagonal cancellation below identifies the comparison. Section 2 now gives this operational sequence before introducing the formal notation.

2. Presentation concern: concrete writing revisions. Section 2 states the cohort-level decision and the predict–reference–correct–update sequence before the mathematical setup. The explanation centers on shared covariance diagonals and the unbiased reference comparison of candidate designs. The empirical claims specify comparator, interaction region, and uncertainty. The full signed surface replaces the favorable-only display. Figure 10 identifies its perfect-hint assumption; learned-hint performance is reported separately. Attribution to HMS, Dudík et al., Rakhlin–Sridharan, and Harshaw et al. is attached to each corresponding result.

3. Theoretical overlap 1: Theorem 3.1 and HMS Proposition 1. Theorem 3.1 specializes Harshaw, Middleton, and Sävje's design-compatibility characterization to independent fair reference assignment, and we make that attribution explicit. Write θ = (aᵀ,bᵀ)ᵀ and L = [I I]. Then μᵀAμ = θᵀLᵀALθ. Under independent fair assignment, the unavailable within-unit product aᵢbᵢ has coefficient 2Aᵢᵢ, so compatibility requires diag(A) = 0. For centered candidate laws, diag(Σₕ−Σg) = 0 automatically. The decision-relevant consequence is

undefined
AuthorsOpenReview ↗

Thanks for the review and here is the kind response(cont'd)

. Substituting Gₜ = ωₜX̂ₜ and Mₜ = ωₜmₜ into its bound yields the squared reference-residual term VTV_T. Accounting for actual reference deployment gives

\mathbb E\sum_t\frac{\omega_t\epsilon_t}{n_t} +\frac{\log|\mathcal E|}{\eta}+\frac\eta2 V_T.$$ The design-specific result combines this feedback construction with reference opportunity cost and the statistical target. With $\omega_t=n_t^2/n_{\max}^2$, multiplying by $4n_{\max}^2/N_T^2$ gives the pooled estimator's expected excess-MSE bound. The comparator is the best fixed member of the declared finite contextual-policy class. **6. Theoretical overlap 4: GSW attribution and covariance certificates.** The GSW concentration guarantee is inherited from Harshaw et al. (Theorem 6.6). For C = (BᵀB)⁻¹, its consequence is Σ ≼ C. The learner scores the actual covariance Σ through fresh sampler draws. Certificate matrices can have different diagonals, and their score differences contain the additional normalized term $\sum_i(C_{h,ii}-C_{g,ii})\delta_i^2/(4n^2)$. Keeping the actual covariance as the learning target preserves common-offset cancellation. **7. Experimental concern 1: nonzero heterogeneous-effect replays.** We added WDBC, Wine, Bike, and RAND replays with unequal potential outcomes: μ = 1.4 tanh(standardized response), δ = 0.2 + 0.3 sin(standardized covariate 2), a = (μ+δ)/2, b = (μ−δ)/2. Calibration rows are disjoint from replay rows. Each learner observes its assigned outcome only. All four PA-CRL risk ratios are below Bernoulli (Appendices N.3 and N.5). These semi-synthetic replays directly test missing-counterfactual feedback under heterogeneous effects; their target is the declared replay population. **8. Experimental concern 2: strong polynomial plug-ins.** The polynomial plug-in leads in all 12 predeclared phase cells, all 17 controlled cells overall, and all ten terminal settings of the fixed ε = .1, η = 4 study. The full 16-cell tuning grid has PA-CRL risk ratios .171–.632; even the best retrospective setting, .171, exceeds the polynomial value .082. The 17-cell result—PA-CRL improving over Vanilla CRL by 1.83–10.28%—isolates the benefit of prediction within the reference learner. The matched-linear experiment addresses a different question: correction when both methods share the same misspecified predictor class. The new mechanism study fixes p = 8, T = 512, n = 12, 24, 48, one or three observed contexts, and three coefficient spectra. Each of six methods selects one global configuration from eight candidates using risk/Bernoulli on six simulator-calibration settings, two populations and 32 histories, then freezes it before the complete 36-cell test on five fresh populations and 128 histories each. Random and fixed coefficients share the same coefficient norm, expected uniform-X response RMS and outcome bound. All learners receive the same covariates/context and actual law information, and only their own completed outcomes. In the prespecified random18 family, PA minus strong-polynomial risk/Bernoulli is **−.078532 [−.095458, −.061605]**; each population first averages all 18 cells equally, followed by a paired $t_4$ interval across populations. PA has lower risk in 18/18 cells, with 14 pointwise intervals below zero. The polynomial plug-in leads in all 18 fixed controls; the combined all36 difference is +.000175 [−.008402, .008751]. Every-cohort pair-IPW and the full PSD second-moment plug-in have lower risk than PA in all 36 cells. This mean-zero family has tied mean rankings; the unique-ranking, nonzero-mean certificate in N.6 is a separate analytical construction. All 36 cells and six methods follow. Entries are mean seed-specific risk/Bernoulli, lower is better. The same selected configuration is used across every cell; all 138,240 history records are retained (Appendix N.7)
AuthorsOpenReview ↗

Thanks for the review and here is the kind response(cont'd)

.

ModeSpectrumnContextsVanillaLinearPolynomialPA-CRLPair-IPWFull PSD moment
fixedconcentrated1210.4079750.2811210.2835740.3851610.3539390.290821
fixedconcentrated1230.4598940.2850140.2915170.4031890.3623650.296061
fixedconcentrated2410.3948830.3036500.3048030.3767390.3476150.310933
fixedconcentrated2430.4250020.3000430.3024160.3795660.3445950.307658
fixedconcentrated4810.3844730.3130490.3134070.3701310.3412780.319965
fixedconcentrated4830.4210700.3142890.3152770.3805640.3479060.321226
fixedisotropic1210.4110180.2827830.2853370.3883200.3557500.292362
fixedisotropic1230.4569470.2831500.2886640.4021100.3606700.294162
fixedisotropic2410.3953560.3012330.3020480.3781940.3486000.308600
fixedisotropic2430.4304980.2981690.3007480.3827000.3473340.305838
fixedisotropic4810.3845190.3101820.3105010.3702460.3413760.317138
fixedisotropic4830.4185270.3116550.3123250.3800030.3464620.318660
fixedmild1210.4071330.2896930.2922220.3856010.3545200.299002
fixedmild1230.4601670.2911560.2976260.3986440.3598260.301253
fixedmild2410.3952000.3112610.3121600.3772990.3488320.318430
fixedmild2430.4266360.3075280.3097240.3794930.3457560.315055
fixedmild4810.3831230.3201980.3204850.3689960.3407010.327041
fixedmild4830.4178150.3212370.3221420.3778730.3460210.328138
randomconcentrated1210.3979450.4265580.5138400.3899550.3541230.281953
randomconcentrated1230.4372000.4272920.4885410.4147650.3638250.288333
randomconcentrated2410.3760400.3590710.4427880.3661740.3379270.280178
randomconcentrated2430.4053140.3663020.4284250.3793340.3378580.281715
randomconcentrated4810.3689610.3261920.3803220.3590440.3295930.280565
randomconcentrated4830.3991830.3629280.3861200.3735630.3338760.286055
randomisotropic1210.4161410.5241740.5663910.4136920.3565660.349135
randomisotropic1230.4908650.5065110.5518200.4737360.3674000.354957
randomisotropic2410.4053360.4808950.5104930.3993980.3479610.345189
randomisotropic2430.4707640.4880260.5130500.4475060.3568610.350122
randomisotropic4810.4007190.4592870.4963220.3958740.3474690.345872
randomisotropic4830.4579890.4982130.5056000.4358130.3527030.348509
randommild1210.4227910.5138010.5594210.4159530.3557330.342720
randommild1230.4930530.4980590.5419610.4806740.3688450.350587
randommild2410.4086300.4599490.5019560.4016680.3484550.343208
randommild2430.4705780.4703170.5019930.4515810.3558100.348425
randommild4810.4065660.4362180.4756570.4000690.3474500.344141
randommild4830.4612860.4812510.4899830.4423170.3535350.348549

The reference cost is reported explicitly: in the original contextual T = 1024 cell, the PA-versus-polynomial gap .13264 decomposes into .08755 direct reference surcharge and .04509 non-reference policy gap. The accounting holds the recorded policy fixed.

9. Experimental concern 3: complete misspecification surface. The complete 36-cell comparison uses eight population seeds and 128 learning histories per seed. PA-CRL wins 16 cells; the matched linear plug-in wins the other 20 point estimates. Their pointwise paired intervals favor PA-CRL in 16 cells, favor the plug-in in 19, and cross zero in one. At β = 0.875 and T = 1024, the reduction is 42.25%, with normalized risk difference −0.006751 [−0.006997, −0.006505]. The largest PA-CRL relative loss is 190.8%, at β = 0 and T = 128. The revised figure displays the full signed surface. These intervals are pointwise, without multiplicity adjustment.

A separate frozen-parameter transfer reused ε = .01 and η = 256 with the original matched linear hint on four fresh populations and retained all 36 cells. PA-CRL had lower risk than the matched linear plug-in in 18/36 cells, with 17 pointwise paired 95% intervals favoring PA-CRL; the strong archived polynomial plug-in had lower risk in all 36 (Appendix N.5). This additional test is distinct from the original eight-population grid above

Reviewer_g1pGOpenReview ↗
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Paper summary

The paper considers choosing among randomization designs across repeated cohorts. The main observation is that all such designs have a unit diagonal covariance, so the risk of a single design cannot be estimated unbiasedly, but the difference in risk between two designs can, using an independently randomized reference cohort. The authors build an online learning procedure on top of this and give regret and inference guarantees.

Critical strengths
  • The zero-diagonal observation is simple and clean, and Theorem 3.1 is a nice characterization.

  • The self-feedback counterexample (Prop. 3.3) is a useful warning.

Critical weaknesses
  • Novelty is limited. Estimability of quadratic forms under general designs is already studied (Harshaw et al. 2026), and the rest of the method combines standard tools: DR-style residual correction, optimistic mirror descent, and existing confidence sequences.

  • A simple polynomial outcome-model plug-in beats PA-CRL in almost every reported setting: all 12 phase cells, the contextual campaign (0.058 vs 0.188), the high-dimensional test, and all archived schedules. The paper admits this in Appendix K, but the main text does not make it clear.

  • The 3.4–42.3% gain in the abstract only holds in 16 of 36 cells, against a deliberately misspecified linear model. In the other half of the grid, that misspecified model is better than PA-CRL by a large margin.

  • Experiments use cohorts of size 12, and the real-data parts are zero-effect replays, not actual repeated experiments.

Questions for authors
  • What in Theorem 3.1 goes beyond the existing results on estimability of quadratic forms?

  • In what realistic setting should someone use PA-CRL instead of just fitting a good outcome model?

  • How large is the precision lost to reference cohorts compared with using the plug-in throughout?

4 comments
AuthorsOpenReview ↗

Thanks for the review and here is the kind response

Design precision depends on the conditional second moment, including cross-unit covariance Ω. A polynomial model may estimate u = E[μ|G] consistently while the risk ℓₕ = (uᵀΣₕu + tr(ΣₕΩ))/(4n²) favors a different law. Appendix N.6 gives a general criterion: with a unique mean-greedy ranking, an expected γ-per-cohort gap to a fixed admissible policy, and mean-selection error probabilities pₜ, PA-CRL’s expected cumulative advantage is at least γT − Σₜpₜ − B_T. Thus γT > Σₜpₜ + B_T certifies lower risk. An exact n = 4 construction has a nonzero linear mean and unique wrong mean-greedy choice. At T = 512, ε = .05 and η = .411325, the theorem bounds PA risk by .030746, below the mean-oracle plug-in’s .070313 and independence/uniform’s .039063. Both methods receive the correct mean; the certificate uses dense reference scores and analytical η. A fixed-parameter reproduction with five fresh sign paths and 4,096 histories each gives learned-hint PA risk .015034 versus learned polynomial’s .069511: 78.37% [78.18%, 78.56%] lower. The .030746 bound covers the exact-mean-hint variant (Appendix N.6).

The separate mean-zero latent-cohort test finds lower PA-CRL risk than the strong polynomial in 18/18 random-coefficient settings, with 14 pointwise paired 95% intervals favoring PA. The mean cell-specific reduction is 15.04% [11.34%, 18.75%]. All 18 fixed-coefficient controls and both enhanced baselines remain in the complete 36-cell report (Appendix N.7).

The original matched-linear experiment identifies correction of a wrong design ranking: PA-CRL reduces deployment risk by 3.4–42.3% in all 16 cells with β ≥ 0.625, across T = 128, 256, 512, and 1024. Every pointwise paired seed-level 95% interval excludes zero. At β = 0.875 and T = 1024, the reduction is 42.25%, with normalized risk difference −0.006751 [−0.006997, −0.006505]. We added the complete signed comparison, reference-cost accounting, and the requested larger-cohort and unequal-potential-outcome tests.

1. W1 / Q1: Contribution relative to existing theory.

Theorem 3.1 specializes Proposition 1 of Harshaw, Middleton, and Sävje (2026). We now state that attribution at the theorem and in the contribution statement. With θ = (aᵀ,bᵀ)ᵀ and L = [I I], the target is θᵀLᵀALθ. Under independent fair assignment, the only potential-outcome pairs that can never be observed together are (aᵢ,bᵢ); compatibility therefore requires Aᵢᵢ = 0. For centered candidate laws, A = Σₕ − Σg satisfies this condition automatically.

The scientific question is how repeated experiments can learn a more precise dependence law while every individual retains treatment probability one half. The tension is that marginal fairness preserves unbiased effect estimation, yet correlated deployment feedback can reverse the ranking of designs. The exact two-unit example has true common-sign-minus-independent normalized risk +1/32, while its self-feedback has expectation −1/4. Reference comparison resolves that reversal:

E ⁣[P⊤(Σh−Σg)P4n2]=rh−rg,P=2Y.\mathbb E\!\left[\frac{P^\top(\Sigma_h-\Sigma_g)P}{4n^2}\right]=r_h-r_g,\qquad P=2Y.

Our contribution connects this decision-relevant cancellation to a sampler-only contrast oracle, predictable reference correction, contextual design learning, and a weighted pooled-MSE guarantee. The augmentation follows Dudík et al.; the optimization follows Rakhlin and Sridharan; the confidence-sequence construction uses established martingale tools. The new appendix separates these inherited primitives from the design-specific feedback and statistical reduction. Ghost assignments give the interface for future centered samplers through their actual outcome-relevant covariance risk.

2. W2 / Q2: When reference correction improves design selection.

PA-CRL is useful when errors in the predicted design ranking cost more precision than obtaining unbiased reference feedback. The original 16-cell interaction regime matches the predictor specification between PA-CRL and the linear plug-in. The new latent-cohort family instead tests the second-moment contribution when the strong polynomial estimates the outcome mean.

The polynomial plug-in accurately ranks the library in the controlled synthetic campaigns and has lower risk in all 17 cells, including all 12 phase-grid cells. The older two-context campaign reports CRL/polynomial ratios 0.187662/0.057611. The newer three-context campaign at T = 1024 reports PA-CRL/polynomial ratios 0.212033/0.079389. These campaigns have different contexts and should be read separately. The archived high-dimensional campaign reports exact-score CRL: polynomial/RF plug-in ratios .042/.046/.081 are below CRL’s .203/.203/.206 at p = 8/64/512. The older seven-schedule archive also evaluates CRL; polynomial ridge has lower mean risk on all seven archived paths (Appendix J). Section 7 states the strong-baseline comparison; Appendix N distinguishes the two contextual campaigns and the archived CRL-only high-dimensional study

AuthorsOpenReview ↗

Thanks for the review and here is the kind response(cont'd)

.

The new mechanism study fixes p = 8, T = 512, n = 12, 24, 48, one or three observed contexts, and three coefficient spectra. Each of six methods selects one global configuration from eight candidates using risk/Bernoulli on six simulator-calibration settings, two populations and 32 histories, then freezes it before the complete 36-cell test on five fresh populations and 128 histories each. Random and fixed coefficients share the same coefficient norm, expected uniform-X response RMS and outcome bound. All learners receive the same covariates/context and actual law information, and only their own completed outcomes.

In the prespecified random18 family, PA minus strong-polynomial risk/Bernoulli is −.078532 [−.095458, −.061605]; each population first averages all 18 cells equally, followed by a paired t4t_4 interval across populations. PA has lower risk in 18/18 cells, with 14 pointwise intervals below zero. The polynomial plug-in leads in all 18 fixed controls; the combined all36 difference is +.000175 [−.008402, .008751]. Every-cohort pair-IPW and the full PSD second-moment plug-in have lower risk than PA in all 36 cells. This mean-zero family has tied mean rankings; the unique-ranking, nonzero-mean certificate in N.6 is a separate analytical construction.

In the earlier independent ten-setting study, calibrated PA-CRL improves on separately calibrated vanilla CRL in 10/10 terminal point estimates, with nine paired intervals favoring PA; the polynomial plug-in leads in 9/10 settings (Appendix N.5). The original fixed ε = .1, η = 4 study remains in Appendix N.3.

3. W3: The complete 36-cell surface and abstract claim.

The following is the complete signed reduction, 100(1 − RPA/Rlinear); positive favors PA-CRL. Figure 3b now prints all values on one symmetric color scale, and Figure 3e includes all nine interaction regimes.

βT = 1282565121024
0−190.83%−164.53%−148.85%−137.43%
0.125−177.72%−147.24%−130.30%−117.82%
0.25−115.14%−92.44%−79.17%−69.72%
0.375−57.07%−45.17%−39.21%−34.25%
0.5−19.91%−11.33%−6.66%−1.49%
0.625+3.36%+13.37%+20.69%+26.28%
0.75+17.41%+27.51%+33.76%+38.25%
0.875+22.19%+32.45%+37.98%+42.25%
1+17.19%+24.54%+29.82%+31.55%

Recalculation from all 73,728 raw method-history records gives 16 favorable and 20 unfavorable point estimates: 16 favorable and 19 unfavorable pointwise intervals exclude zero; β = 0.5, T = 1024 crosses zero. Section 7 states the complete win/loss count and identifies the strong polynomial comparison. The original 3.4–42.3% gain is tied to substantial interaction misspecification.

A separate frozen-parameter transfer reused ε = .01 and η = 256 with the original matched linear hint on four fresh populations and retained all 36 cells. PA-CRL had lower risk than the matched linear plug-in in 18/36 cells, with 17 pointwise paired 95% intervals favoring PA-CRL; the strong archived polynomial plug-in had lower risk in all 36 (Appendix N.5). This additional test is distinct from the original eight-population grid above.

4. Q3: Reference-cohort precision cost.

For the original ε = .1 three-context campaign, hold its recorded policy path fixed and write the Bernoulli-normalized PA risk as U = ε + (1 − ε)V, where V is its non-reference policy risk. If P is plug-in risk, then

U−P=ϵ(1−V)⏟direct reference surcharge+V−P⏟selection gap.U-P=\underbrace{\epsilon(1-V)}_{\text{direct reference surcharge}}+\underbrace{V-P}_{\text{selection gap}}.

Three-context campaignPA risk UPolynomial PNon-reference VReference surchargeSelection gap
T = 5120.2544020.0819740.1715580.0828440.089584
T = 10240.2120330.0793890.1244810.0875520.045092

At T = 1024, the direct reference surcharge accounts for 66.0% of the gap. This is exact accounting at the learned policy; retraining with a different reference rate also changes feedback and future policies. The variance identity makes the operating trade-off explicit:

Var⁡(X^∣G)=v/ϵ+(ϵ−1−1)(Δ−m)2.\operatorname{Var}(\widehat X\mid\mathcal G)=v/\epsilon+(\epsilon^{-1}-1)(\Delta-m)^2.

A well-ranked model offers direct efficiency; reference correction offers identification and protection against ranking errors. The complete sensitivity grid and the explicit costs make that choice quantitative.

5. W4: Larger cohorts and unequal potential outcomes.

The n = 12, 24, 48 latent-cohort test above uses five fresh populations and 128 randomization histories per population, with each method’s calibration-selected configuration frozen before testing. Every method receives the same finite design library and exact covariance access, and learns only from its own observed outcomes.

We also ran four real-covariate replays with heterogeneous effects

AuthorsOpenReview ↗

Thanks for the review and here is the kind response(cont'd)

. Disjoint calibration rows define μᵢ = 1.4 tanh((yᵢ − ȳcal)/scal); δᵢ = 0.2 + 0.3 sin(Xᵢ,2), aᵢ = (μᵢ + δᵢ)/2, and bᵢ = (μᵢ − δᵢ)/2. Consequently Pᵢ = μᵢ + Zᵢδᵢ remains noisy, and only the evaluator knows both potential outcomes. The new appendix gives all four replay comparisons, raw row manifests, and an end-to-end every-cohort pair-IPW baseline. The larger-cohort study tests the procedure beyond n = 12; the semi-synthetic replays test reference feedback under unequal potential outcomes on observed covariate geometry.

The blue revision makes the attribution explicit in Sections 1, 3–5, shows the complete Figure 3 comparison in Section 7, and reports protocols, full results, and reference-cost accounting in Appendix N.

Thanks for your timely reply. However, I do not think it solves my concerns, and in its current form I do not consider the paper suitable for publication at ICLR.

  • I would ask the authors to carefully go through their comments before posting. The response contains numerate formatting errors. Many formulas are written as raw unicode symbols rather than in a Markdown math environment. Even the formulas typed correctly contain stray characters (e.g., the ! following E). This makes several parts of the response difficult to read and verify.

  • Concern about novelty remains. The authors admit Theorem 3.1 specialize Harshaw (2026), and "The augmentation follows Dudík et al.; the optimization follows Rakhlin and Sridharan; the confidence-sequence construction uses established martingale tools." It seems most of the works are inherited from existing papers.

  • Q2 asked for a realistic setting. The response restates the condition under which correction helps but does not identify an application where it is expected to hold.

  • The results in Q2 is a disadvantage of the proposed method. It is weaker than every-cohort pair-IPW and the full PSD second-moment plug-in.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Rebuttal by Authors

A Kind General Response to All Reviewers and Dear AC

Thank you for reviewing our submission. The completed experiments give 78.37% lower risk than the learned polynomial selector in the fixed n=4 reproduction, and a 15.04% mean cell reduction across all 18 predefined random-coefficient settings. These advantages accompany a general risk-gap condition and the complete control and baseline comparisons below.

  1. General operating condition and confirmed gains.

    • Section 2 now explains the predict–reference–correct–update sequence before the notation. Design risk includes cross-unit conditional covariance, so a consistent outcome-mean model can rank designs incorrectly. Appendix N.6 proves advantage when the true per-cohort gap γ to a fixed admissible policy outweighs cumulative mean-selection error and PA’s reference/learning bound: γT > Σpₜ + B_T.
    • Its exactly linear-mean construction gives a T=512 risk bound of .030746 against mean-oracle selection at .070313, using a shared correct mean and dense reference scores. A separate learned-hint reproduction reduces risk by 78.37% [78.18%, 78.56%] against the learned polynomial selector. The certificate applies to the exact-mean-hint variant. See f9GW–§2 (Q1), LJfs–§§1–2, 11, and g1pG–§2 (W2/Q2).
  2. Executed experiments, fair calibration, and complete comparisons.

    • The N.5/N.7 studies give each learner eight calibration candidates and one global configuration frozen before independent testing. The mean-zero cohort-variation study retains all random18/fixed18 cells and six methods. PA beats the calibrated polynomial in 18/18 random cells; 14 pointwise risk-difference intervals exclude zero. The mean cell reduction is 15.04% [11.34%, 18.75%]. The fixed-coefficient controls, full 36-cell results, pair-IPW and PSD second-moment baselines are retained in the complete comparison. This mean-zero study and the unique-ranking construction above cover distinct settings.
    • Section 7 and Appendices N.2–N.3, N.5 and N.7 report the complete original signed 36-cell surface, four unequal-potential-outcome replays, and cohorts of size 12, 24 and 48. Full tables include the strong polynomial and every-cohort pair-IPW. See f9GW–§2 (W2a/W2c), LJfs–§§7–10, and g1pG–§§2–3, 5.
  3. Attribution and the design-specific contribution.

    • We explicitly identify Theorem 3.1 as the independent-reference specialization of HMS Proposition 1, and credit the established augmentation, optimistic mirror descent, and GSW results. Our contribution connects observable design-risk contrasts, sampler-only feedback, corrected learning, and pooled-effect inference. See f9GW–§1 (W1), LJfs–§§3–6, g1pG–§1 (W1/Q1), and Appendix N.1.
  4. Precision cost, matching-horizon baselines, and the revised PDF.

    • We quantify the original reference-cohort surcharge: at T=1024 and ε=.1 it accounts for 66.0% of PA's gap to polynomial. Figure 10 now has matching-horizon zero-hint OMD, uniform, independent and correct-ranking comparisons. On its exact-hint instance, the bound certifies improvement over independence at T=32, 64, 128 and 256. See f9GW–§§3–4 (Q1/Q2), LJfs–§11, g1pG–§4 (Q3), and Appendices N.2/N.4.
    • The revised PDF keeps 10 main-text pages, with References beginning on page 11, and 51 pages in total. Sections 2/7 and Appendices N.1–N.7 contain the completed changes. Changes are marked in blue. The reviewer-specific replies provide the point-by-point correspondence (f9GW–§5 (W3), LJfs–§2).

We sincerely thank the AC again for the time and care devoted to this discussion, and the reviewers for their suggestions. We welcome further discussion and would be glad to address any questions or clarify any part of our responses and revisions.

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

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