acceptodds
Under review as a conference paper at ICLR 2027

Active Discovery of Preference Cycles with Anytime-Valid Inference

Abstract

Preference-based A/B comparisons guide model updates, yet a sequence of locally winning updates can conceal declining underlying strength. Preference cycles expose matchup advantages that no single ranking preserves, but noisy comparisons require evidence for every direction. Uniform sampling can leave a promising cycle waiting on one unresolved pair. We develop an active procedure that targets cycles by estimated remaining evidence cost and shares observations across overlapping and later-proposed candidates. Under stationary independent Bernoulli streams, confidence sequences control the probability of any false report throughout the adaptive search. A fixed-order analysis charges the first positive cycle and the evidence needed to refute earlier candidates, counting shared pairs once. With identical confidence bounds and all initial labels charged, targeting reduces mean first-report cost by 15%-88% across four cyclic environments relative to a representative adaptive transitivity-testing method that we adapt to continued discovery. Updating priorities concentrates queries on cycles that can be completed, while shared evidence supports subsequent discoveries within the same budget.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
Anytime-valid inference, Preference cycles, Sequential discovery

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_bQwjOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies how to actively select pairs for comparison to discover statistically supported nontransitive preference cycles with as few comparisons as possible. The paper first builds a statistical model for pairwise comparisons and defines which cycles can be reported. It then constructs an anytime-valid confidence sequence for each pair. By sharing existing comparison data across cycles, the paper provides a theoretical guarantee that controls the overall probability of reporting any false cycle. Finally, the paper estimates the remaining evidence cost for each pair and uses these estimates to select the most promising cycle and the next pair to compare.

Critical strengths
  1. Traditional preference ranking methods usually rely on scalar scores, which cannot fully capture nontransitive preference relationships. This paper focuses on discovering such preference cycles with fewer pairwise comparisons, which is a relatively novel idea.

  2. This paper reuses existing comparison data and constructs a confidence sequence for each pair. Under the corresponding independence and stationarity assumptions, the method controls the probability of reporting at least one false cycle throughout the adaptive discovery process. The paper also provides solid theoretical guarantees for this error control.

  3. This paper performs well across various simulated datasets and significantly improves the sampling efficiency of discovering nontransitive preference cycles.

Critical weaknesses
  1. This paper only evaluates the proposed method on simulated datasets, without testing it on real-world data. This makes it difficult to fully demonstrate the practical value of the method.

  2. The proposed remaining evidence cost scoring strategy does not show a clear advantage over the simple greedy strategy, as the two strategies achieve very similar performance across the simulated datasets.

  3. The statistical assumptions in this paper are relatively strong, which limits the applicability of the proposed method in real-world settings. Could you consider relaxing these assumptions to make the method more broadly applicable?

Questions for authors
  1. Could you provide some valid theorems to prove the optimality of your method?

  2. You need to compare your method in some real-world datasets.

  3. Could you consider relaxing your assumptions to make the method more broadly applicable?

2 comments

Thank you for your careful review. We appreciate your constructive comments.

We have uploaded a revised version: changed text is in blue, new appendix sections have blue titles, and red margin notes name the review point each change addresses.

W1, Q2

We added a real-data evaluation on the public SUSHI human preference records; the protocol and full table are in our comment to all reviewers (item 1). On the 100-item task, with the same pilot, bounds, outcome streams and 60000-label cap for every method, targeting needs 6302.5 labels on average to find its first cycle, against 40267.5 for Greedy-margin and 33175 for Uniform-unresolved. At the cap, its reported cycles cover 215.60 distinct pairs, against 9.90 and 13.25. On the ten-item population, which has no positive cycle, no method makes a false report in 100 replays. The revised version adds this replay as a real-data section of the experiments.

W2

Targeting gains substantially over greedy on the misspecified matrices and on real data; on the low-rank matrices the gain is small. Table 6 gives 52.7 additional triangles over greedy for Misspecified 1, but 2.4 for Low-rank 1, where both rules nearly exhaust the same structure. Under matched information on all eight matrices (comment to all reviewers, item 2), targeting adds 35.40–52.35 distinct pairs and 7.70–11.90 edge-disjoint cycles on the four misspecified cases, so the gain persists after accounting for overlap. On SUSHI the score also cuts the first-report cost to less than a sixth of greedy's.

Q1

For optimality, the revision adds a lower bound that every valid method must pay to find any cycle, proved by a change of measure on a set of pairs that meets all positive cycles (comment to all reviewers, item 3); matching this benchmark with the empirical score is the open question. Algorithm 1 itself has proved error control and a cost bound. The probability of ever reporting a false cycle stays at most alpha however the algorithm adapts (Theorem 4.1). Because Algorithm 1 samples only unresolved directions in unresolved candidates, Theorem 5.2 bounds its cost of completing a fixed finite family with nonzero gaps, and hence its first-discovery cost when a positive cycle exists; Theorem 5.1 sharpens this for initially fixed orders by charging failed prefixes. The revised version adds the lower bound as a theorem with its proof.

W3, Q3

We relaxed the binary-outcome assumption to bounded scores, including fractional ties, provided the queried pair's score has a stable mean conditional on the full history. The argument is item 4 of our comment to all reviewers; it covers score distributions that change with the history while that mean stays fixed. For noisy or inconsistent judges, the SUSHI replay with independent response reversals at rates 0.1 and 0.2 keeps targeting at 20/20 successes with mean first costs 6702.5 and 8577.5, while Greedy-margin succeeds in 11/20 and 1/20 runs and Uniform-unresolved in 0/20, with no false reports. The revised version states the bounded-score extension after the validity theorem.

Thank you for the positive assessment; we hope these clarifications strengthen your support for acceptance.

Thank you for the detailed responses and revisions. I appreciate the authors' efforts to address my previous concerns. The new experiments on the SUSHI human preference dataset provide useful evidence of the method's practical value. The additional comparisons with Greedy-margin, especially on the misspecified matrices and the real dataset, also show a clearer advantage of the remaining evidence cost strategy. These results largely address my first two concerns. The new theoretical results are also useful. Theorem L.2 provides a lower bound on the information required to discover a positive cycle. However, this does not establish the optimality or near-optimality of the proposed targeting strategy, since there is no guarantee that its sample cost is close to this lower bound. The bounded-score extension in Proposition L.1 also relaxes the original independence and binary-outcome assumptions. However, the method still requires a stable conditional mean, which may limit its use when preferences change over time. Overall, the revisions have addressed most of my concerns and significantly improved the paper. Although some theoretical limitations remain, they do not change my overall assessment. I therefore maintain my recommendation for acceptance.

Reviewer_EASCOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

The paper formulates sequential discovery of positive directed cycles in pairwise preference data, where a cycle is reportable only if every directed edge has population win probability above a fixed threshold of one half plus a margin. It maintains time-uniform confidence sequences for each physical pair in a shared registry, reports cycles when all directed lower bounds exceed the threshold, refutes candidates when any upper bound falls below it, and adaptively targets candidates by estimated remaining evidence. The paper proves simultaneous validity under stationary independent Bernoulli streams, gives a fixed-order cost bound for first discovery, a family-completion bound, and a prescribed-discovery lower bound, and evaluates the method on synthetic preference matrices against an adapted transitivity-test baseline and several sampling controls.

Critical strengths
  • The shared confidence-sequence registry is a clean way to reuse observations across overlapping and later-proposed cycles while preserving a simultaneous error guarantee. This directly addresses a real inefficiency in cycle discovery, where separate tests would spend labels repeatedly on shared pairs.

  • The fixed-order cost analysis separates the cost of failed candidate prefixes from the evidence required on each physical pair, and it identifies how shared pairs are charged once. This gives a useful diagnostic for understanding when candidate ordering matters.

Critical weaknesses
  • The novelty is limited and the advantage over existing methods is not established. Adapting the query rule of Haddenhorst et al. to continued discovery with the same confidence sequences is a natural baseline, and the main new ingredient is an empirical targeting score with constants fixed by the authors. The paper does not provide a lower bound for first discovery that matches the adaptive policy, nor does it show that the heuristic is necessary or near-optimal. A simpler shared-evidence uniform sampler with the same confidence bounds is not fully ruled out as competitive.

  • The empirical validation is too narrow and too synthetic to support the paper's claims. All experiments use small synthetic matrices with known population truth, and the motivating application to LLM judge evaluation is not tested on real judgments. Continued discovery is measured by counting overlapping true triangles as separate reports, which can inflate the apparent benefit. The comparisons use adapted baselines and different initial samples, so fairness is not fully established. The paper also does not report false-report calibration on real or dependent data.

Questions for authors
  1. What is the minimal novel algorithmic contribution beyond applying simultaneous confidence sequences to cycle discovery and adapting the existing query rule to continued reporting? Can you compare against a simpler shared-evidence uniform sampler with the same bounds and show that adaptive targeting is necessary?

  2. The targeting score uses fixed constants such as w = 20, d_min = 0.015, and c0 = 200. How sensitive are the reported gains to these values, and were they tuned on the same matrices used for evaluation?

  3. Counting overlapping true triangles as separate reports may overstate the value of continued discovery. Can you report distinct edge coverage, vertex coverage, or a non-overlapping cycle basis? Do the gains over controls persist under such metrics?

  4. Can you provide a real-data experiment with LLM judges or human preferences under the stated protocol, including false-report calibration, label cost, and sensitivity to judge inconsistency?

3 comments

Thank you for your thoughtful review. We appreciate your detailed questions.

We have uploaded a revised version: changed text is in blue, new appendix sections have blue titles, and red margin notes name the review point each change addresses.

W1 (novelty), Q1

The contributions are a remaining-cost targeting rule and a cost analysis that charges failed candidate prefixes and counts shared pairs once, built on standard confidence sequences and union bounds. The rule targets the candidate with the lowest estimated remaining cost, samples its costliest unresolved direction, and updates after each batch.

Under the same confidence bounds, the shared-evidence uniform sampler needs several times as many labels as targeting. With initial labels charged to every policy, the five settings in Table 4 (Appendix C.1, p. 16) give mean first-report costs of 4942, 3314, 5123, 2700 and 13447 labels for Uniform-unresolved, versus 961, 1107, 573, 405 and 817 for targeting, in table order. The Sparse-RPS saving is 3980 [3663,4297]. With identical pilots, bounds, streams and caps on all eight matrices (comment to all reviewers, item 2), uniform needs 3235.25 labels for its first report on Misspecified 1 against targeting's 477.75, and on SUSHI it needs 33175 against 6302.5. These comparisons show targeting's label savings under matched information and cost accounting; validity comes from the shared confidence bounds.

On theory, Theorem 5.2 bounds Algorithm 1's finite-family completion, Theorem 5.1 concerns initially fixed orders and Theorem J.1 prescribed discoveries. The revision adds a lower bound on the labels any valid method needs for its first report (comment to all reviewers, item 3), the benchmark for the score's efficiency. The revised version states the contribution in these terms.

Q2

The constants (w,d_min,c0)=(20,0.015,200) were chosen in advance, before any evaluation run, and are used unchanged on all eight synthetic matrices (Section 5.1) and in the SUSHI replay. First-report costs change little with the constants; continued counts are more sensitive. In an added analysis, halving and doubling each constant on all eight matrices over ten paired runs gives misspecified-family mean first costs of 470.25–483.38, against 475.25 at the default. For continued counts, d_min=.0075/.015/.03 gives 56.25/59.55/78.38. The revised version adds this sensitivity table.

Q3

The gains persist for distinct edges and edge-disjoint cycles; for vertex coverage the difference is inconclusive. Under matched information on the four misspecified matrices, targeting adds 45.20/47.20/35.40/52.35 distinct physical pairs and 9.80/9.50/7.70/11.90 greedy edge-disjoint cycles over Greedy-margin. On Misspecified 1 its binary cycle-incidence rank gain is 42.50, while its vertex gain is 0.35, and Uniform can cover more vertices. On SUSHI, targeting's reported cycles cover 215.60 distinct pairs against 9.90 for greedy. The revised version reports distinct pairs, edge-disjoint packings and cycle rank alongside triangle counts.

W2 (empirical validation), Q4

We ran the protocol on human preferences, the public SUSHI records (comment to all reviewers, item 1). Targeting's first-report cost is 6302.5 labels against 40267.5 and 33175 for the controls. On the cycle-free ten-item population every method makes zero false reports in 100 replays (one-sided 95% upper bound 2.95%). With independent judgment reversals at rates 0.1 and 0.2, targeting still succeeds in every run, at mean costs 6702.5 and 8577.5, and no method makes a false report. These replays use historical human judgments, with a respondent sampled independently for each query.

On fairness, the principal comparison charges all labels, including targeting's 720- or 294-label pilot, and the shared-information controls equalize that pilot. Section 6.3 reports the original global test, with its distinct stopping objective and gap input, including the oracle-gap Ordered-cycle case where it wins, 695 versus 1804 labels.

We hope these responses and the revision address your concerns, and we respectfully invite you to reassess the paper in light of them.

Thanks for your reply. I would like to increase my score to 2.

Thank you for your follow-up and for raising your score. We are glad the revision was helpful.

The revised version tests the method on real human preferences from the SUSHI data, including false-report calibration. It also compares all methods under the same initial labels and budget, and adds a lower bound on the labels any valid method needs.

We would like to resolve whatever still holds the paper back in your view. Could you tell us which concerns remain? There is time left in the discussion period, and we are ready to provide further analyses or clarifications.

Reviewer_M8jzOpenReview ↗
Rating
2
Confidence
2
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper studies active discovery of preference cycles from noisy pairwise comparisons. Its algorithm estimates the remaining evidence needed to confirm each candidate cycle, prioritizes inexpensive candidates, and samples their bottleneck comparisons. Shared per-pair confidence sequences allow observations to support overlapping and newly proposed cycles while controlling the probability of any false report throughout the adaptive search. The main contributions are this shared-evidence discovery framework, an adaptive sampling heuristic, and sample-complexity analyses for first discovery under a fixed priority order and for finite-family completion.

Critical strengths

Strength 1: All methods use the same confidence bounds and share the same random outcome streams, and every method’s cost includes its initial sampling labels. Under these conditions, targeting lowers first-report cost by 15–88% against the adapted π* baseline. The gains hold on eight independently generated matrices. These designs make it more trustworhty on the claims and see which part of the method is responsible. The benefit is credible but specific: it comes mainly from continued discovery, not from the first report.

Strength 2: The paper keeps one anytime-valid confidence sequence per pair and splits the error budget across pairs with one union bound (Thm 4.1). As a result, the chance of any false cycle report during the whole run stays at or below α, even when candidate cycles are proposed after looking at the data, priorities change after every batch, and stopping is adaptive. This is what makes ongoing, interactive cycle discovery statistically trustworthy. Without it, adaptive targeting would just be a heuristic with uncontrolled false reports. The construction is simple and correct, and it carries over to other adaptive evaluation settings.

Critical weaknesses

1: Practical relevance remains unvalidated on real comparisons. Experiments use synthetic Bernoulli environments with only 9–30 objects. There is no fresh LLM-judgment or self-play evaluation demonstrating useful discoveries in practice. The introductory declining-strength example is constructed: discovering a cycle establishes nontransitivity, but does not itself establish that model quality declined.

  1. The theory doesn’t explain why the proposed adaptive rule is efficient, and its empirical edge over simple baselines is narrow. The first-discovery theorem analyzes a policy whose candidate and direction orders are fixed initially. The proposed algorithm continually changes those orders. The general completion bound applies broadly to unresolved-edge policies and therefore does not establish why this particular scoring rule is efficient. Likewise, the prescribed-family lower bound does not establish optimality for finding any cycle. It seems that there is some theoretical gap.
Questions for authors

Clarification questions

  1. Theory–algorithm connection: Does any first-discovery efficiency guarantee apply to the adaptive policy in Algorithm 1, beyond the general family-completion bound? Please clarify which theoretical conclusions extend to the evaluated algorithm.
  2. Incremental benefit of the scoring rule: Tables 4–6 suggest that Greedy-margin and fixed priority capture much of the first-discovery improvement, while adaptive remaining-cost scoring mainly improves continued discovery. Is this the intended interpretation of the algorithm’s contribution, and how consistently does the continued-discovery advantage hold across the tested environments?
  3. Sensitivity to initialization: How sensitive are the gains to the amount and coverage of the initial sample, particularly when it misses the edges of an inexpensive positive cycle? If existing results address this, they would help assess whether the reported gains depend on favorable initialization.

Suggestions for future work: maybe real preference-data evaluation, scalable candidate generation, and extensions to dependent or nonstationary judgments would strengthen practical applicability.

1 comment

Thank you for your detailed review. We appreciate your helpful suggestions.

We have uploaded a revised version: changed text is in blue, new appendix sections have blue titles, and red margin notes name the review point each change addresses.

W1

A reported cycle certifies pairwise nontransitivity at the declared margin. Such cycles can arise from cyclic interactions among models with equal scalar strength, as well as in the strength-style construction in Figure 1 and Appendix D.1. The revised introduction states this directly.

On real comparisons, we replayed public human preference records (SUSHI; comment to all reviewers, item 1). With the same 5000-label pilot, bounds, streams and 60000-label cap, targeting finds its first cycle after 6302.5 labels on average, against 40267.5 for Greedy-margin and 33175 for Uniform-unresolved, and the cycle-free population gives no false report in 100 replays per method. These replays use recorded human judgments. The revised version adds this replay as a real-data section.

W2, Q1

Two guarantees cover Algorithm 1 exactly as evaluated, with its changing priorities and proposals. False-report control holds throughout (Theorem 4.1). The completion bound of Theorem 5.2 also applies, because Algorithm 1 samples only unresolved directions in unresolved candidates; for a fixed finite family with nonzero gaps it caps the first-report cost when a positive candidate exists. Theorem 5.1's sharper failed-prefix bound requires initially fixed orders, and Theorem J.1 is a prescribed-discovery lower bound. For finding any cycle, we add a lower bound valid for every alpha-valid procedure (comment to all reviewers, item 3); it gives the allocation that any method must pay.

So the theory guarantees validity and bounded cost for the adaptive policy, while the efficiency of the remaining-cost score in particular is shown by the experiments. The revised version adds a short table mapping each theorem to the policies it covers.

Q2

The score contributes mainly to continued discovery, and on real data also to the first report. On the synthetic matrices, favorable-candidate selection, which greedy shares, accounts for much of the early gain. Table 6 reports 52.7 more triangles for targeting than for greedy on Misspecified 1, versus 2.4 on Low-rank 1. In Table 5, fixed priority reaches the first report earlier on Block-RPS (1080.9 versus 1106.6 labels), with equal output of 27.

The continued-discovery advantage holds consistently. Against the adapted π* baseline, Appendix B.4 (pp. 15–16) reports positive paired output differences on all eight independent 18-object matrices, 159.1–165.6 triangles for Low-rank 1–4 and 12.8–33.0 for Misspecified 1–4. Under matched information (comment to all reviewers, item 2), targeting adds 35.40–52.35 distinct pairs and 7.70–11.90 edge-disjoint cycles over greedy on all four misspecified matrices, while both rules nearly complete the low-rank structures. On real data the score also matters for the first report: on SUSHI, Greedy-margin needs 40267.5 labels against targeting's 6302.5.

Q3

Targeting uses a small labeled pilot, charged to its cost, and its gains persist with half or double the default pilot and when the pilot misses the cheapest positive cycle. For this reply we tested 0, 147, 294 and 588 pilot labels on all eight matrices (ten paired runs, total cap 12000). A separate stress mask removes the pilot labels on the cheapest positive cycle; only the mask uses truth. Targeting then reports 58.42 cycles versus greedy's 8.68 in the misspecified family. Half, default and double pilots yield 59.05, 59.55 and 61.45; with no pilot, targeting yields 13.22 versus uniform's 37.88. The default pilot of 294 labels is 2.5% of the cap and is included in every reported cost.

Suggestions

For dependent scores, item 4 of our comment to all reviewers extends reporting validity to scores in [0,1] with a stable mean conditional on the full history; this covers fractional scores and score distributions that change with the history while the conditional mean stays fixed. For candidate generation, the O(n+R) graph search finds a cycle in the supported graph, while explicit triangle scoring still requires cubic candidate storage and scans.

We hope these responses address your concerns, and we would be grateful if you would consider raising your score.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Comment to all reviewers

We thank the reviewers. Four results requested by more than one reviewer are collected here once, and the individual replies refer to them. The revised version adds all four. In the uploaded revised version, changed text is in blue, new appendix sections have blue titles, and red margin notes name the review point each change addresses.

  1. Real human preferences (Section 6.4; Appendix M, Tables 9–10)

We replayed the public SUSHI preference records (Kamishima, 2003): 5000 complete ten-item rankings and 5000 partial rankings over 100 items. Each query independently samples a recorded respondent whose ranking contains the queried pair, so costs count replayed judgments, and truth is the full-record preference matrix. The design used the paper's threshold 0.55, alpha 0.05 and constants, and was fixed before any outcome was computed. On the 100-item task all methods receive the same 5000-label pilot, confidence bounds, outcome streams and 60000-label cap. Over 20 paired repetitions, targeting finds its first cycle with less than a fifth of the labels that either control needs:

MethodMean first costSuccessDistinct pairsEdge-disjoint packing
Remaining-cost targeting6302.520/20215.6040.30
Greedy-margin40267.520/209.903.20
Uniform-unresolved33175.019/2013.253.80

Failed runs are charged the full budget. The paired saving over greedy is 33965 labels (95% interval [30419,37511]). The "Distinct pairs" column counts the physical pairs in reported true cycles; the packing is a fixed-order greedy selection of edge-disjoint reported cycles. Both columns average all 20 runs at the cap. The ten-item population has no positive cycle, and there every method makes zero false reports in 100 independent replays (one-sided 95% upper bound 2.95%). With independent response reversals at rates 0.1 and 0.2, and truth recomputed, targeting succeeds in 20/20 runs at mean first costs 6702.5 and 8577.5, Greedy-margin in 11/20 and 1/20, and Uniform-unresolved in 0/20, again with no false reports.

  1. Matched information on the eight synthetic matrices (Section 6.4; Appendix N.1, Tables 11–12)

All methods receive identical 294-label pilots, bounds, streams and a 12000-label cap, over 20 paired runs. On the four misspecified matrices targeting adds 35.40–52.35 distinct physical pairs and 7.70–11.90 edge-disjoint cycles over Greedy-margin, with every paired 95% interval positive, so the gain persists after overlap is removed. On Misspecified 1, the first costs of targeting, greedy and uniform are 477.75/507.75/3235.25 and their final triangle counts 66.85/14.15/32.80. On the low-rank matrices both adaptive rules nearly exhaust the same structure (Low-rank 1: 561.50/617.75/5312.75 and 216.00/213.60/49.35).

  1. A lower bound for finding any cycle (Section 5.3; Appendix L.2, Theorem L.2)

Suppose a procedure's probability of ever reporting a false cycle is at most alpha in every environment, and it reports some cycle with probability at least 1−alpha at p. Then every set H of physical pairs that meets all positive allowable cycles satisfies

sum_{e in H} E_p[N_e] kl(mu_e,theta0) >= kl(1−alpha,alpha),

where mu_e is the positive directional probability on e and N_e counts all labels on e, pilot included. The labels must be conditionally Bernoulli given the whole transcript, with decision and non-label kernels unchanged across environments. Proof: moving H's positive directions to theta0 removes every positive cycle and creates none, so the report event has probability at least 1−alpha at p and at most alpha in the altered environment; the transcript chain rule and data processing give the inequality. Minimizing the total allocation subject to these constraints gives a cost lower bound for every valid method.

  1. Bounded scores (paragraph after Theorem 4.1; Appendix L.1, Proposition L.1)

Reporting validity extends from binary outcomes to scores Y in [0,1], including fractional ties, whenever E[Y | full pre-observation history] = p_e for the queried pair. For fixed q and p in (0,1), (q/p)^Y((1−q)/(1−p))^(1−Y) is at most its linear chord Y(q/p)+(1−Y)(1−q)/(1−p), whose conditional expectation is one. The registration-fixed beta mixture is therefore a nonnegative supermartingale, and Ville's inequality with the original predictable error allocation preserves simultaneous validity. This permits history-dependent score distributions with stable conditional means.

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