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Under review as a conference paper at ICLR 2027

Uniform Ensembles under Dependence: Calibration and Protected Replacement

Abstract

Temporal dependence does not by itself justify replacing uniform bagging. We separate the information available for learning, the intervention that changes an ensemble, and the evidence needed to approve that change. Uniform-bootstrap voting attains the minimax rate on a covariate-refresh family, while balanced spectral routing is exactly midpoint blocking on weighted paths, decreasing temporal kernels, and sufficiently large band graphs. For frozen replacements, independent-label certification has matching fixed-confidence cost in disagreement and improvement . A multiscale martingale certificate instead protects average conditional improvement along a dependent audit history. Across four chronological tasks, full residual stacking has the lowest mean later error on three, while graph projection improves on full stacking on none. Rolling-origin production evaluation records 23 approved replacements, including 2 forward-error reversals. A gradual within-audit drift experiment explains how a positive historical average can coexist with a harmful current predictor. Restarting at a predeclared recent window removes that outdated evidence but loses useful power under stable conditions. The resulting guarantee concerns the chosen audit window; future transfer still requires separate evidence or restrictions on drift.

Primary area:
learning theory
Keywords:
ensemble learning, learning theory, majority-vote ensembles, Markov dependence, minimax optimality, spectral routing

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_MtuyOpenReview ↗
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2
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1
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2
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Paper summary

This paper studies uniform bagging under temporal dependence through four stages: learning, intervention, certification, and transfer. It establishes the minimax excess-risk rate min⁡1,dT/n\min{1,\sqrt{dT/n}} for a covariate-refresh family and shows that finite uniform-bootstrap voting attains this rate when m≥n/(dT)m \geq n/(dT). It also provides a blocked learning bound for bootstrap-ERM voting over finite-VC classes under absolute regularity.​

The paper proves that balanced Fiedler routing coincides exactly with midpoint blocking on several structured temporal graphs, including band graphs satisfying s≥2w+1s \geq 2w+1. For frozen replacement candidates, it derives matching fixed-confidence sample-complexity bounds of Θ(ω/Δ2)\Theta(\omega/\Delta^2) for paired certification and develops a multiscale martingale-based confidence sequence for average conditional improvement under arbitrary adapted dependence.​

Experiments on four chronological prediction tasks (CO2, electricity demand, meat production, and housing sales) show that full residual stacking achieves the lowest mean later-period error on three tasks, whereas graph projection never outperforms full stacking. Additional within-audit drift and rolling-origin experiments demonstrate the limitations of transferring historical certification guarantees to future deployment.

Critical strengths
  1. Careful distinction between guarantees and strong reproducibility.

The paper explicitly separates population risk, historical conditional improvement, recent-window certification, and future transfer without overstating their implications. Negative results, implementation details, random seeds, and numerical diagnostics are reported transparently.

Critical weaknesses
  1. Limited theoretical novelty and significance.

The main results largely specialize established techniques from dependent-data learning, spectral seriation, matched-pair testing, and confidence sequences. Although some exact refinements are useful, none is convincingly established as a sufficiently substantial or broadly applicable technical advance, and their combination lacks a compelling unified contribution.

  1. Weak motivation for the evaluated interventions and insufficient empirical validation.

The paper does not establish that spectral routing or graph-projected residual stacking are representative methods previously proposed for temporal ensembles, making the negative comparisons difficult to interpret. Evaluation is limited to four tasks, shallow tree ensembles, and mostly single chronological splits, without strong comparisons to established blocked-validation or adaptive-window model-selection methods.

Questions for authors
  1. Which existing temporal-ensemble methods specifically motivate the Fiedler-routing and graph-projected residual-stacking interventions? If these are newly constructed alternatives, what practical hypothesis or established limitation makes their negative evaluation consequential?

  2. What substantial theoretical insight is obtained beyond the existing results on spectral seriation, dependent-data learning, and self-normalized confidence sequences? How broadly does it extend beyond the particular graph and refresh-process families studied here?

  3. Why are stronger dependence-aware model-selection and drift-adaptation baselines, such as blocked chronological validation and adaptive-window approaches, absent? Can the practical benefit of protected replacement be established across independent temporal environments rather than repeated learner seeds on fixed splits?

2 comments
AuthorsOpenReview ↗

Response to Reviewer Mtuy – Part 1

Thank you for the review. The table summarizes our answers, and the sections after it give the details.

Your pointOur answerWhere in the revision
First question: which methods motivate Fiedler routing and graph-projected stackingThey are the two natural ways to use a temporal dependence graph in an ensemble. One partitions the data along the graph's Fiedler vector, as in spectral partitioning and seriation. The other regularizes the stacking covariance with the graph, as in covariance shrinkage and forecast combination. Section 4 shows that the first reduces exactly to contiguous blocking on the standard temporal graphs, and the experiments show that the second never improves on full stacking.Sections 2 and 4; Table 1
Second question: theory beyond spectral seriation, dependent-data learning, and confidence sequencesFour results are new: exact partition equality rather than ordering recovery, with a sharp threshold for band graphs and a normalized-Laplacian extension; matching bounds showing that disagreement, not error, sets the certification budget; a proof that no audit-only guarantee identifies future transfer; and a matching minimax benchmark for classification under refresh dependence.Sections 3–5; Appendices D, F and G
Third question: blocked chronological validation, adaptive windows, and independent temporal environmentsBoth baselines are added under the same candidate library and label budget. Adaptive-window selection lowers later error relative to the temporal rule by 0.0006–0.0108 on three tasks and ties on climate, and neither makes a harmful approval. Only the temporal rule certifies its improvement on a dependent audit history. Rolling origins add 34 evaluation origins on three more tasks (reply to Reviewer XECQ).Section 6.3; Appendix M
Evaluation limited to shallow tree ensemblesThe revision adds L2-regularized logistic regression and a cellwise-voting learner. With both, the temporal rule approves replacements on all four tasks and lowers later error on each.Appendix M

The graph interventions test whether the specified temporal geometry improves replacement. They are controlled alternatives, not a representative sample of deployed temporal-ensemble methods. Their negative results therefore do not establish a general failure of graph-based forecasting. The equivalence results reach further than the experiments. On weighted paths, decreasing temporal kernels, and band graphs, any method that routes by the balanced Fiedler cut reduces to contiguous blocking. These graph classes include nearest-neighbour-in-time and exponential-kernel graphs.

The theoretical contributions are the exact midpoint identities and band-graph threshold, the disagreement-sensitive audit cost, and the distinction between historical and future targets. The certificate builds on established self-normalized supermartingale bounds, and its new parts are the audit target and the matching cost. The refresh and structured-graph results do not imply an unrestricted theorem for arbitrary temporal graphs or dependent learners.

Blocked-bootstrap training is not blocked chronological validation, and the fixed 120-month restart is not adaptive-window selection. The revision adds both selection rules. They share the candidate library and label budget, use a chronological selection portion, and reserve separate audit outcomes for the protected decision. Selecting windows on the audit outcomes instead requires simultaneous protection over the declared windows. The blocked rule uses an hvhv-block split, and the adaptive rule chooses among a prespecified grid of window lengths using only past observations.

Each entry is the deployed later error, with the number of approving learner seeds out of 10 in parentheses.

Selection ruleClimate later errorElectricity later errorProduction later errorHousing later errorHarmful approvals
Uniform bagging (Table 1).2800.3386.3239.23230
Reference rule.2800 (0).3264 (5).3162 (9).2323 (0)3
Temporal rule (Table 2).2800 (0).3386 (0).3090 (7).2323 (0)0
hvhv-block validation.2800 (0).3291 (3).3110 (6).2319 (1)1
Adaptive-window selection.2800 (0).3278 (4).3084 (7).2316 (1)0

Adaptive-window selection has the lowest later error on production and housing, the reference rule has it on electricity, and all rules tie on climate. The temporal rule is therefore not the most accurate selector. Adaptive selection improves on it by 0.0006–0.0108, and neither makes a harmful approval in these runs. The reference rule treats audit labels as independent and makes three harmful approvals. The temporal rule's role is its guarantee: it certifies an average conditional improvement over a dependent audit history, which neither chronological selector does.

AuthorsOpenReview ↗

Response to Reviewer Mtuy – Part 2

Later error, approval frequency, label cost, and harmful later replacements answer different questions; a method can achieve lower error without issuing a certificate.

The revision also repeats the comparison with two non-tree learners. The first is L2-regularized multinomial logistic regression with fitting-window standardization, C=1C=1, and the lbfgs optimizer for at most 2,000 iterations. The second is a cellwise-voting learner that follows the learning theorem's construction. It splits each continuous coordinate into three equal-frequency bins at the fitting-window tertiles and keeps categorical coordinates. Adjacent cells are merged until every fitting cell holds at least 20 records, and each cell predicts its majority label, with ties broken by the fitting-window class prior. Bin edges, merges, and tie rules are frozen before the audit.

LearnerRuleClimate later errorElectricity later errorProduction later errorHousing later errorHarmful approvals
Logistic regressionUniform bagging.2875.3492.3318.24100
Temporal rule.2868 (1).3447 (2).3189 (6).2398 (1)1
Cellwise votingUniform bagging.2964.3618.3421.24970
Temporal rule.2949 (1).3562 (2).3264 (5).2479 (1)2

With both learners, the temporal rule approves replacements on all four tasks and lowers later error on each. Its approvals are therefore not specific to tree ensembles.

The precise audit guarantee is as follows. For frozen candidates and Ur,i∈−1,0,1U_{r,i}\in\\{-1,0,1\\} equal to baseline error minus replacement error, define

=\frac{1}{t}\sum_{i=1}^{t}\mathbb{E}[U_{r,i}\mid\mathcal{F}_{i-1}].$$ Let $S_{r,t}=\sum_i U_{r,i}$, $D_{r,t}=\sum_i U_{r,i}^2$, and $\psi(\lambda)=-\log(1-\lambda)-\lambda$. For $J$ candidates and a fixed finite $\Lambda\subset(0,1)$, Theorem 6 gives, simultaneously over candidates and times, $$\Delta^{\mathrm{hist}}_{r,t}\ge \frac{1}{t}\max_{\lambda\in\Lambda} \left\\{ S_{r,t} -\frac{\psi(\lambda)}{\lambda}D_{r,t} -\frac{\log(J|\Lambda|/\alpha)}{\lambda} \right\\} =L_{r,t}.$$ This holds with probability at least $1-\alpha$. The inequality $$\exp(\lambda u-\psi(\lambda)u^2) \le 1+\lambda u$$ makes the corresponding centered product a nonnegative supermartingale; Ville's inequality and a union bound give the result. For future conditional gain $D^{\mathrm{future}}_{r,t,h}$, a separately justified restriction $$D^{\mathrm{future}}_{r,t,h} \ge \Delta^{\mathrm{hist}}_{r,t}-\rho_{r,t,h}$$ implies $$D^{\mathrm{future}}_{r,t,h} \ge L_{r,t}-\rho_{r,t,h}.$$ A probabilistic drift restriction needs its own error allocation. Without one, audit gains can all equal $+1$ and future gains all equal $-1$. The certificate remains valid for its stated historical target. Please let us know whether these changes address your concerns.
Reviewer_XECQOpenReview ↗
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3
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2
Informativeness
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Paper summary

This paper establishes minimax-rate attainability on a refresh model, identifies settings where spectral routing equals midpoint blocking, and develops disagreement-sensitive certification guarantees. Its key distinction is that temporal certification protects average conditional improvement during the audit, without guaranteeing future improvement. Across four chronological tasks, full residual stacking achieves the lowest mean later error on three, while graph projection never improves on it. Drift and rolling-origin experiments illustrate the gap between audit approval and future performance, and the power cost of using more recent evidence.

Critical strengths
  1. The distinction between average conditional improvement during an audit and future predictive performance. The temporal guarantee, impossibility result, and drift experiments establish why a valid certificate can coexist with subsequent deterioration. This substantially improves our understanding of how statistical guarantees should inform model replacement.

  2. For independent paired audits, the matching bounds connect the required sample size to candidate–baseline disagreement and improvement. The experiments further expose the power cost of using recent evidence. Together, these results provide useful guidance on when the available data can justify replacing a uniform ensemble.

Critical weaknesses
  1. The sharp minimax result concerns a refresh model and cellwise bootstrap voting, while the VC extension assumes exact empirical risk minimization. These results do not directly cover the shallow-tree score ensembles evaluated experimentally. I therefore find the learning-theoretic guidance limited on when uniform bagging should be competitive in a practical dependent-data problem.

  2. The ten seeds vary learner randomness on fixed data histories, and rolling-origin evaluation covers only the production dataset. Moreover, temporal certification approves replacements on only one of the four main tasks. Although these limitations are acknowledged, they leave the demonstrated practical benefit concentrated in one setting, limiting my confidence in its generality across deployment periods and dependence patterns.

Questions for authors
  1. On the real datasets, graph stacking changes both the covariance representation and the objective through the additional d∥w∥22d\|w\|_2^2 penalty. Is an unprojected control with the same penalty available, analogous to Table 10? Does the disadvantage persist under this comparison? This would clarify whether the negative result is attributable to projection or regularization.

  2. Do the approval rates and subsequent error differences remain similar across alternative evaluation origins on the non-production datasets, under comparable fitting and audit budgets? A limited sensitivity analysis would materially affect my assessment of whether useful protected replacement extends beyond the production example.

2 comments
AuthorsOpenReview ↗

Response to Reviewer XECQ – Part 1

Thank you for the careful review. The table summarizes our answers, and the sections after it give the details.

Your pointOur answerWhere in the revision
First question: an unprojected control with the same penalty on the real tasksRun. With the penalty in place, adding the projection changes later error by only .0003–.0020, while the penalty alone raises it by .0021–.0167. The negative result is therefore due to the penalty, not the projection. Full covariance without the penalty is best on all four tasks.Table below; Appendix M
Second question: other evaluation origins on the non-production tasksRun on climate, electricity and housing with the production study's windows. Over 34 origins, the temporal rule approves 63 of 340 seed-origin decisions, and 4 of them do worse later, against 83 approvals and 14 worse outcomes for the reference rule. The 21 origins that deploy a temporal replacement change later error by −1.25% on average.Table below; Appendix M
The learning theorem does not cover the shallow-tree ensemblesCorrect. The tree experiments test the interventions and the replacement audit, not the learning theorem, and Appendix C.4 states this. The refresh simulation in Appendix H.3 runs the theorem's own setting: the refresh law with cellwise bootstrap-majority voting. The revision also runs a cellwise-voting learner that follows the theorem's construction on the four real tasks, and the temporal rule lowers later error on each (reply to Reviewer Mtuy).Appendices C.4, H.3 and M
Certification approves a replacement on only one of four tasksThat is the safeguard working. On housing, full stacking raises later error from .2323 to .2519, and every temporal decision keeps uniform voting. On the rolling origins, and with the two added learners, the temporal rule also approves replacements on climate, electricity and housing.Table 2; Section 6.3; Appendix M

The learning theorem and the experimental learners have different scopes. The sharp result uses the refresh model and cellwise voting; the VC extension requires exact ERM and Bayes containment. These assumptions do not automatically hold for shallow, feature-subsampled score trees. Appendix C.4 states this distinction. The tree experiments evaluate the interventions and replacement audit rather than directly validate the exact learning theorem.

The real-data graph comparison changes both projection and regularization. Its objective replaces Q^\widehat Q by PQ^PP\widehat QP and adds d∥w∥22d\|w\|_2^2, where d=∥PQ^P−Q^∥opd=\|P\widehat QP-\widehat Q\|_{\mathrm{op}}. Synthetic Table 10 includes an unprojected same-penalty control, and the table below adds the corresponding real-history control.

The control crosses the projection with the penalty. Every row uses the Table 1 fitting split, test split, seed aggregation, and error calculation, with the same head predictions and calibration data. The first and last rows are the full and graph residual stacking of Table 1.

Stacking ruleClimate later errorElectricity later errorProduction later errorHousing later error
Full covariance, no penalty (Table 1, full stacking).2742.3133.3062.2519
Projected covariance, no penalty.2760.3151.3078.2530
Full covariance, graph-matched penalty.2790.3300.3180.2540
Projected covariance, graph-matched penalty (Table 1, graph stacking).2793.3311.3200.2555

The projection alone raises later error by .0011–.0018, from the first row to the second. The penalty alone raises it by .0021–.0167, from the first row to the third. Adding the projection to the penalized fit changes it by a further .0003–.0020. The penalty, not the projection, therefore accounts for most of graph stacking's disadvantage, and full covariance without the penalty has the lowest later error on all four tasks. Comparisons are paired within fitted-head banks; banks trained on the same history do not constitute independent temporal environments.

The production extension is in Appendix K.3: seven origins yield 23 approvals, including two forward-error reversals. Table 2 reports 0/10, 0/10, 7/10, and 0/10 approvals on the four main tasks. The revision adds rolling origins on the other three tasks. They use fixed chronological fitting, selection, and audit windows, and overlapping origins are not counted as independent histories. Approval frequency and subsequent error are reported as separate outcomes.

The counting unit is a seed-origin decision, as in Appendix K.3, where 7 origins and 10 learner seeds give 70 decisions. The main split is origin 0 of each grid and keeps its 0/10 temporal approvals.

AuthorsOpenReview ↗

Response to Reviewer XECQ – Part 2

TaskOriginsSeed-origin decisionsReference approvals (worse later)Temporal approvals (worse later)Origins deploying a temporal replacementMean later-error change at those origins
Climate1212010 (2)9 (1)6−1.40%
Electricity1212042 (7)34 (2)8−1.30%
Housing1010031 (5)20 (1)7−1.05%
Total3434083 (14)63 (4)21−1.25%

The temporal rule approves fewer replacements than the reference rule, 63 against 83, and fewer of its approvals do worse later, 4 against 14. The total mean weights each task by its number of deploying origins. Appendix K.3's production study is a separate evaluation set, so its two forward-error reversals are not part of these counts.

Please let us know whether these results answer your questions.

Reviewer_ra3wOpenReview ↗
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Paper summary

I found this manuscript absolutely incomprehensible. I cannot begin to give you a coherent account of what the high-level claims are, or how they relate to the actual math. I cannot even tell you what some key pieces of jargon like "refresh" are supposed to mean, not with any exactitude. Now, I have been working in the field of machine learning methods for time series and spatio-temporal data since the 1990s. I have published (pretty good, IMHO) papers on risk bounds for mixing and non-mixing processes, on bootstrap and cross-validation, and, specifically, on ensemble methods for time series. I mention this for only one reason: I do not think the problem is on my end. The authors may have a correct, an interesting, or even an important idea in mind. They, and their LLM, have completely failed to communicate it in this MS.

Critical strengths

None.

Critical weaknesses

See above.

Questions for authors

None.

1 comment
AuthorsOpenReview ↗

Response to reviewer ra3w

Thank you for the frank review. We agree that the submission did not communicate its claims clearly. The revision rewrites the introduction and Section 3 around the three claims in the general response, and the table below answers the points you raised.

Your pointOur answerWhere in the revision
The high-level claims and their relation to the math are unclearThere are three claims, each tied to one result and one experiment: uniform voting attains the minimax rate (learning), Fiedler routing equals midpoint blocking (routing), and certification has a matching label cost and an audit-window target (replacement).Section 1, first paragraph
What "refresh" meansAt each step, the current covariate–label pair is kept with probability 1−1/T1-1/T, and with probability 1/T1/T it is replaced by a fresh draw from the stationary law. At T=10T=10, the pair persists to the next step with probability 0.9.Section 1; Section 3.1, Equation 2
What "frozen replacement" meansThe candidate predictor and every fitting choice are fixed before any audit outcome is seen.Section 1; Section 5

The revised introduction opens as follows.

We study when uniform bagging should be replaced under temporal dependence, and make three claims. First, dependence alone does not call for a different ensemble. In the covariate-refresh model of Equation 2, the current covariate–label pair is kept at each step with probability 1−1/T1-1/T and otherwise redrawn from the stationary law. An observation therefore persists for TT steps on average. With dd observable feature cells and nn observations, a finite cellwise bootstrap vote attains the minimax excess-risk order min⁡{1,dT/n}\min\lbrace 1,\sqrt{dT/n}\rbrace (Section 3). Dependence thus limits the information in the sample without necessarily adding a penalty for uniform resampling. Second, balanced spectral routing repeatedly splits the training sequence into halves along the Fiedler vector of a dependence graph. On weighted paths, decreasing temporal kernels, and sufficiently large band graphs, it is exactly midpoint blocking and adds nothing beyond contiguous blocks (Section 4). Third, consider a frozen replacement, meaning a candidate whose fitting choices are all fixed before any audit outcome is seen. Certifying it from independent audit labels costs Θ(ω/Δ2)\Theta(\omega/\Delta^2) labels, where ω\omega is the probability that it disagrees with uniform bagging and Δ\Delta is its risk improvement. On a dependent audit history, a multiscale martingale certificate protects the average conditional improvement during the audit, but no audit-only guarantee certifies future improvement (Section 5).

“Refresh” means retaining the entire current covariate–label pair with probability 1−1/T1-1/T and independently redrawing a pair from the stationary law with probability 1/T1/T (Section 3.1, Equation 2). At T=10T=10, for example, the pair persists at the next step with probability .9. The process starts in stationarity. Appendix A.1 gives the kernel, and Appendix H.3 specifies the simulation.

This is a stylized dependence model used to obtain a sharp learning result, not a claim that general time series literally repeat observations. Likewise, “frozen replacement” means that candidate predictors and fitting choices are fixed before their audit outcomes are revealed. The revision introduces these two operations in words before the formal notation. The resulting message is not that uniform bagging always wins, but that dependence alone does not justify replacing it.

Please let us know whether the revised introduction makes the claims clear.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response

We thank the reviewers. Reviewer XECQ found that the separation of audit-window improvement from future performance "substantially improves our understanding of how statistical guarantees should inform model replacement". Reviewer Mtuy noted the careful separation of guarantees and the transparent reporting of negative results. Reviewers ra3w and Mtuy found the paper hard to follow. The revision rewrites the introduction around the three claims below and defines each term in words before its notation.

What the paper shows

QuestionAnswerWhere
Does temporal dependence by itself call for a different ensemble?No. On a covariate-refresh family, where each covariate–label pair is kept with probability 1−1/T1-1/T and redrawn otherwise, uniform-bootstrap voting attains the minimax rate.Section 3; Appendix A
Does routing the ensemble along a temporal graph help?Not on the standard temporal graphs. Balanced spectral (Fiedler) routing is exactly midpoint blocking on weighted paths, decreasing temporal kernels, and sufficiently large band graphs.Section 4; Appendix D
What evidence justifies replacing uniform voting with a fitted candidate?With independent audit labels, certification costs Θ(ω/Δ2)\Theta(\omega/\Delta^2) labels, where ω\omega is the candidate–baseline disagreement and Δ\Delta the improvement, with matching lower and upper bounds. On a dependent audit history, a multiscale martingale certificate protects the average conditional improvement during the audit. No audit-only guarantee can certify future improvement.Section 5; Appendices F and G

On four chronological tasks, full residual stacking has the lowest later error on three, and graph projection never improves on it (Table 1). The certificate approves a replacement on production and refuses it on housing, where full stacking would raise later error in all ten seeds (Table 2).

New results in this response

  • Projection against penalty on real data (XECQ). With the same heads and data, the graph projection alone raises later error by .0011–.0018, while the graph-matched penalty alone raises it by .0021–.0167. The penalty, not the projection, explains graph stacking's disadvantage, and full covariance without the penalty is best on all four tasks.
  • Other evaluation origins (XECQ, Mtuy). Over 34 rolling origins on climate, electricity and housing, the protected temporal rule approves 63 of 340 seed-origin decisions, and 4 of them do worse later. The reference rule approves 83, and 14 of them do worse. The 21 origins that deploy a temporal replacement change later error by −1.25% on average.
  • Selection baselines (Mtuy). Adaptive-window selection lowers later error relative to the temporal rule by 0.0006–0.0108 on three tasks and ties on climate. Neither rule makes a harmful approval, while the reference rule makes three. Only the temporal rule certifies its improvement on a dependent audit history.
  • Other learners (XECQ, Mtuy). With L2-regularized logistic regression, and with a cellwise-voting learner that follows the theorem's construction, the temporal rule approves replacements on all four tasks and lowers later error on each. It makes one and two harmful approvals, respectively.

Revisions at a glance

ChangeRequested byWhere in the revision
Introduction rewritten around three claims, with every term defined in words before its notationra3w, MtuySection 1; Section 3.1
Projection-and-penalty control on the four real tasksXECQSection 6.3; Appendix M (new)
Rolling origins on climate, electricity and housingXECQ, MtuySection 6.3; Appendix M
Blocked chronological validation and adaptive-window baselinesMtuySection 6.3; Appendix M
Logistic-regression and cellwise-voting learnersXECQ, MtuySection 6.3; Appendix M
Motivation for the routing and graph-stacking interventions, and a statement of what is new in the theoryMtuySections 1 and 2

What the paper claims

The paper separates three questions: when uniform voting is statistically competitive, what a graph-based replacement changes, and what evidence justifies accepting that replacement. The learning results have explicit model assumptions, and the replacement audit protects average conditional improvement during its audit window. Neither claim is a distribution-free guarantee of improvement after deployment. This separation explains why a replacement can pass a valid historical audit and then deteriorate.

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

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