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Under review as a conference paper at ICLR 2027

Tracking the Best Imputer under Drift: Continual Competence Routing for Non-Stationary Time Series

Abstract

Time-series imputation is typically deployed statically: an imputer is selected offline and retained as the stream evolves. Yet even when all imputers remain frozen, their relative competence can change with missingness structure and data regime. We formulate this problem as continual competence routing under sparse reconstruction feedback and introduce Continual Competence Routing (CCR), which tracks time-varying competence using multi-scale memories of audited reconstruction evidence while leaving the underlying imputers fixed. Our analysis identifies a fundamental distinction between coverage and freshness. Under a linear relative-competence model, arbitrarily strong all-history geometric coverage can remain stale after a change in expert ordering, whereas sufficiently informative post-change coverage controls fresh competence-estimation error and supports recovery of the current ordering. Across clinical and general time-series streams, frozen expert libraries exhibit substantial competence-oracle headroom and recurrent reversals in the best imputer. Fresh geometry is informative on ETTh1 and Weather but weaker on clinical streams. Under sparse audits, multi-scale routing improves over static deployment in several settings but does not uniformly beat the best static or fixed-memory baseline. Successful continual imputation therefore depends on evidence that is not merely abundant, but relevant to the current competence regime.

Primary area:
learning on time series and dynamical systems
Keywords:
time-series imputation, continual learning, non-stationary learning, competence routing, concept drift, sparse feedback, adaptive model selection, distribution shift

Reviews

Among:
Shape:
1234this paper, Bottom 27%
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_BiXhOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

This paper proposes Continual Competence Routing (CCR) to select among frozen time-series imputers under distribution drift. CCR uses multi-scale memories of sparse reconstruction feedback to track changing model competence.

Critical strengths

W1. The method lacks an overview diagram. Multi-window estimation, weight updates, and certification-based switching are described in separate subsections, making it difficult to follow how these components interact within the complete decision process.

W2. The experimental comparisons are not sufficiently convincing. CCR-MS underperforms static selection in some settings and does not consistently improve over fixed-memory routing, leaving the necessity of multi-scale routing unclear. Moreover, comparisons are largely restricted to static, fixed-memory, and discounted baselines, without representative alternative online model selection methods evaluated under the same feedback conditions.

Critical weaknesses

W1. The method lacks an overview diagram. Multi-window estimation, weight updates, and certification-based switching are described in separate subsections, making it difficult to follow how these components interact within the complete decision process.

W2. The experimental comparisons are not sufficiently convincing. CCR-MS underperforms static selection in some settings and does not consistently improve over fixed-memory routing, leaving the necessity of multi-scale routing unclear. Moreover, comparisons are largely restricted to static, fixed-memory, and discounted baselines, without representative alternative online model selection methods evaluated under the same feedback conditions.

Questions for authors

See Weakness.

6 comments
AuthorsOpenReview ↗

Our responses to the weaknesses and questions

We thank the reviewer for identifying two central questions: how the routing components interact and whether adaptive memory adds value beyond simpler alternatives. Our revision addresses both through a unified causal pipeline, new algorithm-specific guarantees and matched experiments.

1. Complete decision process and notation (W1).

Figure 1 now presents the complete routing pipeline in Section 3. A visible incomplete context is mapped to a frozen representation; nested ridge memories use previously revealed audits to produce horizon-specific expert scores and directional leverage.

The original MS branch combines scores using adaptive horizon weights, while CCR-Cert adds a heuristic incumbent-retaining margin gate. The new GL/Lepski branch selects a single horizon using cross-scale disagreement and directional uncertainty. The selected expert is deployed before current audit losses are revealed; subsequent feedback updates the memories and applicable weights.

Figure 1 separates online audit updates from evaluation-only quantities. Algorithm 1 specifies CCR-GL, and the revised text explicitly defines the scores, weights, losses and deployment rules. Formal GL guarantees are distinguished from heuristic CCR-Cert.

2. Stronger online model-selection alternatives (W2).

The rebuilt benchmark uses common frozen predictions, evaluation targets, audit activations and validation-only tuning.

Beyond individual imputers, Static and fixed/discounted ridge, we now compare deterministic and sliding-window Hedge, Fixed Share, restart ridge, stationary contextual selection, uniform multi-scale aggregation, intercept-only controls and Lepski.

We report absolute MAE/RMSE. GL-Tuned improves original CCR-MS micro-MAE on all four primary datasets:

  • ETTh1: 2.53%.
  • Weather: 6.30%.
  • MIMIC-IV: 5.23%.
  • PhysioNet-B: 0.68%.

Across 96 primary family-by-rate comparisons, 76 conditional pointwise 95% macro-MAE intervals favor GL-Tuned, none favor MS, and 20 are inconclusive. Switching counts decrease substantially, e.g., from 129.61 to 2.56 on Weather.

GL-Tuned improves validation-selected Static by 7.44% on ETTh1. On exploratory Electricity, GL-Tuned and MS improve even hindsight BestConst by 1.47% and 2.68%, respectively.

Static remains stronger on Weather and both primary clinical datasets, and Hedge is competitive. Fewer switches do not establish switching safety.

3. Is adaptive multi-scale memory necessary?

We designed a matched study specifically to isolate the contribution of adaptive memory from full-pipeline improvements.

GL-Tuned selects intercept-only representation in 1,330/1,440 primary cells (repeated validation choices), making representation simplification a potentially important contributor.

We therefore replay all 1,608 declared protocol cells with both base and intercept-only representations. GL, Lepski, Longest, Uniform and Fixed share ridge settings, radius multipliers and horizon libraries selected through a common validation objective. Independently tuned Fixed is an additional control.

Table 4 reports eight primary pooled macro-MAE comparisons with approximate Bonferroni adjustment:

  • Three favor GL: MIMIC-IV intercept and PhysioNet-B base/intercept.
  • Two favor Fixed: Weather base and MIMIC-IV base.
  • Three are inconclusive.

The favorable clinical micro-MAE reductions are modest (0.330%, 0.312% and 0.038%), and Static remains stronger. GL and Lepski agree on 99.11% of actions on average per cell. Longest is competitive and outperforms GL in two favorable clinical settings in secondary unadjusted comparisons.

These matched results establish selective benefits of adaptive memory while identifying settings where simpler rules suffice. They distinguish the value of adaptation itself from improvements attributable to representation or tuning.

4. Formal justification for adaptive memory.

The original theory established freshness recovery using a known-reset estimator. The revision substantially advances this analysis through CCR-GL, a causal adaptive selector with algorithm-specific guarantees.

Theorem 3 establishes a directional oracle inequality: the routing excess is at most three times the best available sum of directional statistical uncertainty and transported drift/approximation bias across candidate horizons.

Thus CCR-GL adapts to the estimation--drift trade-off without knowing reset times or variation budgets.

Under conditional excitation, Theorem 4 establishes switching, variation-budget and partition-adaptive dynamic-regret bounds. Proposition 5 gives matching information-theoretic dependence on horizon, audit probability, and drift, up to logarithms in the exact, fixed-dimensional setting.

These results provide a formal justification for adaptation under unknown drift, rather than requiring adaptive memory to dominate fixed windows in every finite-sample experiment. The synthetic evaluations explicitly retain cases where fixed windows outperform formal GL.

In conclusion, the revision establishes the mathematical value of adaptive memory under unknown drift and isolates its empirical contribution through matched comparisons. Together with the unified presentation and stronger online baselines, these advances directly address the reviewer's concerns. We respectfully request reassessment in light of the revised results.

We sincerely appreciate your thoughtful and constructive feedback, which has contributed significantly to strengthening our manuscript. The new theoretical guarantees, expanded experimental evidence, and improved presentation directly address the concerns raised and provide a substantially stronger foundation for our contributions.

We welcome further questions and constructive discussion throughout the rebuttal period. Thank you again for your time, expertise, and careful evaluation. We respectfully look forward to your reassessment of the revised manuscript in light of these substantive advances.

Reviewer_9UDGOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper studies how to pick, online, the best imputer from a fixed set of frozen imputers (Linear, SAITS, T1) when the best choice changes over time and true values are only revealed through sparse audits after each decision. CCR estimates each imputer's recent audit loss with windowed ridge regression at several memory lengths and combines them (CCR-MS). CCR-Cert only switches when a candidate is certified. The theory shows that no router can detect a change before an audit arrives after it, and gives a ridge bound for the fresh-window estimate. Experiments on MIMIC-IV, PhysioNet 2019, ETTh1, Weather and Electricity ask whether the best imputer really changes (RQ1, 8–27% oracle headroom), whether recent evidence beats cumulative evidence (RQ2), and whether CCR routes better than fixed choices (RQ3).

Critical strengths
  1. The problem framing and the benchmark protocol are the paper's main value. It shows that the best frozen imputer does change with the missingness pattern and regime, measures how much an oracle router could gain (Table 1), and keeps audits, evaluation targets and methods cleanly separated. The paper is also upfront about its negative results. I think this could be useful as a benchmark, even though the method itself is not convincing yet.
Critical weaknesses
  1. The router does not show a benefit, and the one setting where it helps is hard to interpret. On clinical data CCR-MS is the same as Static (MIMIC-IV 0.0776 vs 0.0777; PhysioNet 0.1517 vs 0.1494). With full audits on ETTh1 and Weather it is much worse than Static (0.132 vs 0.031 and 0.509 vs 0.142, Table 2). At p=0.2p=0.2 it ties the best fixed window (0.0280 vs 0.0277 on ETTh1). In addition, Static uses no audits, but its nCPR changes with the audit rate on ETTh1 (0.031 vs 0.0498) and Weather (0.142 vs 0.1563), while it stays the same on the clinical data. Appendix G.3 says the streams are shared across audit rates, so the p=1p=1 and p=0.2p=0.2 blocks seem to come from different setups. The paper's main argument for CCR compares exactly these two blocks.

  2. Too much is undefined or missing to check the results. Tables 3–6 report PASS/FAIL/soft-PASS for "G1/G2 gates", but G2 is never defined, and some verdicts go against the stated 5% rule (Table 5: Weather D3 SAITS passes with 0.60% headroom, while Weather D6 SAITS fails with 7.61% and 15 strong reversals). The stated reference clinical setting fails (ΔAUC −0.0179, Table 6), and the "primary" pass is moved to another variant. D4/D5, the harmful-switch rate, switch count and delay are described but never reported. T1 is not described or cited. Absolute imputation errors are not reported, and the appendix mentions "released" manifests that are not linked. As it stands, I cannot verify RQ1 or RQ3.

Questions for authors

Clarification questions:

  1. Why does Static, which uses no audits, give different nCPR on ETTh1 and Weather at p=1p=1 and p=0.2p=0.2, but not on the clinical data? Which streams and settings produced each block of Table 2?
  2. What exactly are the G1 and G2 gates and the soft/strong ΔAUC thresholds, and how do they lead to the Table 5 verdicts for Weather D3 and D6?
8 comments
AuthorsOpenReview ↗

Our responses to the weaknesses

We thank the reviewer for the careful scrutiny and recognition of our problem framing and audit/evaluation separation. The revision delivers a rebuilt benchmark, stronger comparisons, and new theory.

W1. Routing benefits and experimental consistency.

The original cross-audit Static discrepancy is incompatible with a shared evaluation protocol. We withdraw the affected comparisons and replace them with a benchmark using fixed predictions, evaluation targets, validation-selected Static, shared competence proxies and nested audit activations. Static MAE and proxy nCPR are now invariant across audit probabilities. The clinical cohorts have changed; this is a corrected replacement, not an exact reproduction.

Absolute reconstruction gains. Revised Table 2 reports mean cell micro-MAE:

DatasetStaticMSGL-TunedFixedHedgeBestConst
ETTh1.29617.28123.27413.28306.27646.26783
Weather.04066.04358.04083.04403.04069.04066
MIMIC-IV.19989.21749.20611.21707.20231.19989
PhysioNet-B.39291.39919.39649.39950.39545.39291

GL-Tuned improves CCR-MS on all four primary datasets, reducing micro-MAE by 2.53%, 6.30%, 5.23% and 0.68%, respectively. Of 96 paired family-by-rate macro-MAE comparisons, 76 conditional pointwise 95% intervals favor GL-Tuned, none favor MS, and 20 are inconclusive (no multiplicity adjustment). Static remains stronger on three datasets.

Selection correction versus tracking. We distinguish gains over validation-selected Static from gains beyond hindsight BestConst:

LStatic−Lrouting=(LStatic−LBestConst)+(LBestConst−Lrouting).L_{\rm Static}-L_{\rm routing}=(L_{\rm Static}-L_{\rm BestConst})+(L_{\rm BestConst}-L_{\rm routing}).

ETTh1 GL-Tuned improves Static by 7.44% but does not beat BestConst. On exploratory Electricity, GL-Tuned and MS beat BestConst by 1.47% and 2.68%, with the clearest gains under D2/D6.

Does adaptation itself help? Table 4 compares GL, Fixed, Lepski, Longest and Uniform under shared representations, ridge settings, radii and horizon libraries. Three of eight approximately Bonferroni-adjusted GL--Fixed comparisons favor GL, two favor Fixed and three are inconclusive. The favorable clinical effects are modest; Longest and Lepski remain competitive. Adaptive memory adds value selectively, rather than universally.

W2. Verifiable estimands, complete reporting and reproducibility.

We replace the undocumented G1/G2 verdicts with explicit quantitative diagnostics. RQ1 separates realized pointwise headroom, feature-conditional proxy headroom, and realized out-of-fold policy performance. Relative to BestConst, realized/proxy headroom is 18.32%/1.70% on ETTh1 and 6.70%/0.03% on Weather. None of the 20 primary drift-family comparisons strictly favors regime-aware over stationary contrast regression. Changing winners alone do not establish parameter drift.

RQ2 compares fresh and all-history leverage as predictors of positive proxy excess. Mean AUROC differences are -.00656, .04611, .00036, and .00622 on ETTh1, Weather, MIMIC-IV, and PhysioNet-B, respectively. We acknowledge the original MIMIC-IV reference failure (-.0179) and retain weak corrected clinical effects without promoting a favorable sensitivity variant.

We identify T1 as Park et al.'s channel-head-binding architecture, add BRITS, and report MAE/RMSE and all D0--D6 general-series families. Comparators include individual imputers, Hedge, Fixed Share, discounted, and restart ridge. GL-Tuned reduces primary switch counts by 73--98%, but proxy-harmful fractions (threshold .01) do not consistently decrease. Original MS recovers in 72.1% of 104 eligible ETTh1 proxy-defined episodes; mean restricted delay is 14.59 rounds (32-round cap). Other datasets have no reported eligible episodes, not zero delay.

Appendices J-K document configurations, splits, masks, estimands, and extended results. All 35,472 shared benchmark/replay rows and 4,824 final reference rows agree exactly with prior metrics; all 112 final validation selections match grid minima. The evidence bundle contains aggregate extracts, declared configurations, and audit reports, not private raw evaluator arrays or per-source bootstrap inputs.

New theoretical contribution. Theorems 3-4 establish a directional oracle inequality and switching/variation-adaptive regret for CCR-GL without known resets or drift budgets. Proposition 5 matches lower-bound dependence on horizon, audit probability and drift up to logarithms in the exact, fixed-dimensional, well-excited setting. These guarantees apply to formal GL, not retrospectively to MS or validation-tuned GL.

We respectfully request reassessment based on the corrected evidence and new guarantees.

Thank you for these precise questions. Below we explain the original discrepancies and the corresponding corrections.

Q1. Why does Static's nCPR vary with the audit rate, and which settings produced the original Table 2 blocks?

The reviewer is correct that Static must be invariant when the deployed constant expert, evaluation stream and competence reference are fixed. The original ETTh1 values (.031 at p=1p=1, .0498 at p=.2p=.2) and Weather values (.142, .1563) violate that invariant under the stated shared-stream interpretation.

The available original outputs do not establish which streams, seeds, expert selections or competence references produced each block. We therefore cannot identify the exact source of the discrepancy or explain why the clinical results did not exhibit the reported discrepancy. We withdraw the affected cross-rate comparisons without speculating about their cause.

Corrected construction. In Section 6 and Appendix J, every cell fixes the dataset, intervention, library seed and stream seed before varying the audit probability. Static is selected by validation macro-MAE and then frozen. Expert predictions, evaluation targets and cross-fitted competence proxies are shared across audit rates. On eligible rounds, a common uniform draw VtV_t defines nested audit activation At(p)=1{Vt<p}A_t(p)=\mathbf 1\{V_t<p\}. Audit histories vary with pp; any rate-specific router tuning uses validation only.

For nn valid evaluation rounds, let μ~m,t\widetilde\mu_{m,t} denote the retrospective cross-fitted evaluation-loss proxy and m~t\widetilde m_t its minimizing expert. The revised normalized competence pseudo-regret is

nCPR^(I)=∑t(μ~It,t−μ~m~t,t)∑tμ~m~t,t+10−8n.\widehat{\rm nCPR}(I)=\frac{\sum_t(\widetilde\mu_{I_t,t}-\widetilde\mu_{\widetilde m_t,t})}{\sum_t\widetilde\mu_{\widetilde m_t,t}+10^{-8}n}.

For Static, It=mStaticI_t=m_{\rm Static} for every round. Neither numerator nor denominator depends on pp under the corrected protocol. Its actual reconstruction loss is likewise invariant.

Table 19 illustrates corrected ETTh1 mean micro-MAE:

ppStaticMSGL-Tuned
1.29617.27463.26946
.5.29617.27885.27221
.2.29617.28288.27596
.1.29617.28858.27890

Both routers improve with increased audit probability on this panel, whereas Static is exactly unchanged. These are absolute MAE results, not the original nCPR values. The clinical cohorts have changed; this is a corrected replacement, not a reconstruction of the original blocks.

Q2. What are G1/G2 and the soft/strong AUROC thresholds, and how do they explain Weather D3/D6?

The submitted record specifies a nominal G1 headroom threshold of 5% (Table 1 and Figure 1), together with recurring strong reversals as evidence of decision-relevant drift. Figure 2 marks +.05 as the strong fresh-minus-history AUROC difference. However, the manuscript does not fully specify G2, the operational strong-reversal criterion or the soft/strong decision rules needed to reproduce all reported verdicts.

The reviewer identifies a genuine inconsistency: original Table 5 reports Weather D3 as PASS with .60% headroom and eight strong reversals, but Weather D6 as FAIL with 7.61% headroom and 15 strong reversals. Table 5 is a stricter frozen/eligible-boundary sensitivity panel, not the primary Table 3 panel. That distinction does not explain its contradictory labels. Neither the stated 5% threshold nor the available reversal counts justify those verdicts. We cannot recover a complete decision rule and do not defend the labels retrospectively.

Replacement in the revision.

The revision replaces the original G1/G2 classifications with explicit quantitative estimands and uncertainty intervals, providing a transparent assessment without relying on post hoc thresholds.

The revised RQ1 reports realized pointwise headroom and estimated feature-conditional headroom relative to hindsight BestConst, as well as realized out-of-fold policy gains relative to validation Static. The two headroom measures for Weather are 6.70% and .03%, respectively. This distinguishes retrospective opportunities from those supported by pre-decision features. None of the 20 primary regime-aware versus stationary contrast comparisons strictly favors the regime-aware model.

For revised RQ2, we report ΔAUC, defined as fresh-leverage AUROC minus all-history-leverage AUROC for predicting positive cross-fitted proxy excess. Positive values favor fresh leverage.

We report estimates and paired conditional intervals rather than soft/strong classifications. Weather has mean ΔAUC = +0.04611, with 14/28 favorable pointwise intervals; clinical effects remain small. We explicitly acknowledge the original MIMIC-IV reference result (−0.0179), without promoting a favorable sensitivity variant to obtain a PASS.

The revised conclusions are grounded in a corrected evaluation protocol, explicit statistical estimands, and stronger empirical evidence.

We sincerely thank you for your thoughtful and constructive feedback, which has helped us substantially strengthen the manuscript. We believe that the new theoretical results, additional experimental evidence, and clarifications directly address your concerns and further establish the significance of our contributions.

We welcome any remaining questions or suggestions and look forward to continuing our discussion during the rebuttal period. Thank you again for your time, expertise, and careful consideration of our work.

Reviewer_TPe6OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

This paper seeks to develop a method for selecting an optimal imputer among a set of frozen imputers for non-stationary time series with missing values. The authors framed this task as continual competence routing under sparse reconstruction feedback and introduce Continual Competence Routing (CCR), which tracks time-varying competence using multi-scale memories of audited reconstruction evidence. They evaluated CCR in clinical and general time-series data and provided some valuable insights on how to choose the best imputer for non-stationary time series.

Critical strengths

It seems new to use a Continual Competence Routing framework to select best imputer for incomplete nonstationary time series data. Of note, I am unfamiliar with a) online expert selection and feedback and b) freshness under non-stationarity, so I am not well-positioned to evaluate the contributions of this work relative to the existing work in these two areas and my evaluation is focused on how the proposed work would improve imputation of incomplete nonstationary time series data.

Critical weaknesses

Overall, I don’t see compelling evidence from this work to answer the following questions: a) whether the proposed approach would actually improve imputation in incomplete nonstationary time series data and b) if yes, under what conditions. My specific comments are as follows.

  1. The focus of the proposed approach is to select the best imputer, but there is no discussion about the validity of the proposed approach under different missing data mechanisms, such as MCAR, MAR, and MNAR.

  2. The theoretical results are for a stylized linear relative-competence model, so it is unclear to what extent the results are relevant to the proposed approach. In addition, the theoretical analyses of the proposed approach in Appendices A-D do not seem to be dependent on any property of imputers. In other words, it seems that this proposed framework can be applied to another type of task, say choosing optimal prediction model (using time-series data). As such, the connection between the proposed methodology and missing data imputation seems quite tenuous at best and the advantage of using the proposed approach vs a state of the art imputation model for time series data is unclear.

  3. In the computational experiments, the frozen expert library includes only three imputers, Linear, SAITS, and T1, and I have difficulty to find the definition of T1. No SoTA imputers were included in the expert library or as separate baseline methods. In addition, imputation performance was not evaluated. It is still important to evaluate the proposed approach in terms of imputation performance, compared to the current state of the art imputation models for time series data.

Questions for authors
  1. It is difficult to understand the proposed CCR framework, as a number of math symbols are not defined, for example, xtx_t, Φ(⋅)\Phi(\cdot), Lm,tevalL_{m,t}^{eval} etc.

  2. How is the audit loss function defined and evaluated using observed data when naturally missing values provide no reconstruction target? It seems that the performance of the proposed approach is predicated on the validity of the audit loss function.

  3. How is μ~eval\tilde\mu^{eval} computed in real dataset?

7 comments

We thank the reviewer for recognizing the novelty of continual imputer selection and for raising the central question of when sparse reconstruction feedback can improve imputation. Our revision establishes new theoretical guarantees, identifies when reconstruction audits are statistically informative, and provides direct evidence of improved imputation under specific missingness conditions.

1. Missingness mechanisms and validity of reconstruction feedback (W1, Q2).

Naturally missing entries are never treated as reconstruction labels. At round tt, we hide originally observed entries before constructing the context and expert predictions. The hidden population is divided into disjoint audit and evaluation subsets.

For role q∈{audit,eval}q\in\{\mathrm{audit},\mathrm{eval}\}, the reconstruction loss of expert mm is

=\frac{1}{|\mathcal I_t^{q}|} \sum_{k\in\mathcal I_t^{q}} |\widehat y_{m,t,k}-y_{t,k}|,$$ where $\mathcal I_t^{q}$ is the corresponding nonempty target set, $y_{t,k}$ is its withheld observed value, and $\widehat y_{m,t,k}$ is the frozen expert prediction. Only the audit-loss vector can be revealed after deployment. The revision establishes a precise statistical justification for this protocol. Proposition 7 proves that uniform role allocation, with role-independent predictions, gives exact expected alignment of pairwise reconstruction-loss contrasts. For population size $n$, audit size $a$, and finite-population contrast variance $S_z^2$, $$\mathbb E[\bar z_A-\bar z_E]=0,\qquad \operatorname{Var}(\bar z_A-\bar z_E) =\frac{nS_z^2}{a(n-a)},$$ where $\bar z_A$ and $\bar z_E$ are the mean expert-loss contrasts on audit and evaluation targets. Across 9,792 real reconstruction-contrast conditions, the mean empirical/theoretical variance ratio is 1.000233. Channel-biased allocation increases estimated expected discrepancy on every primary dataset. Proposition 8 establishes the complementary fundamental limitation: competence on naturally missing entries is not identifiable in general. Thus, our framework specifies both when controlled audits are informative and what cannot be inferred about native MNAR. The expanded experiments evaluate controlled MCAR, MAR and MNAR at 10/30/50% holdout rates with four frozen experts. GL-Tuned reduces ETTh1 micro-MAE relative to Static by 7.81%/9.64% under MCAR30/50 and 9.32%/19.08% under MNAR30/50. On PhysioNet-B, MNAR30/50 improvements are 3.88%/5.13%, although Hedge performs better. The reported MAR and clinical negative results delimit these benefits. **2. Theoretical advances and their relevance to imputation (W2).** Architecture independence is a deliberate strength of CCR: it models expected reconstruction-loss differences between frozen imputers rather than their internal architectures. In particular, a shared nonlinear component of expert risks cancels in relative competence; individual risks need not be linear. The revision substantially extends the original known-reset analysis. Our new CCR-GL selector adapts its memory without knowing reset times or drift budgets. Theorem 3 establishes an algorithm-specific directional oracle inequality accounting for unknown drift and approximation bias. Theorem 4 gives switching, variation-budget and partition-adaptive dynamic-regret guarantees under conditional excitation. Proposition 5 establishes matching information-theoretic dependence on horizon, audit probability and drift, up to logarithms in the exact, fixed-dimensional setting. Crucially, Propositions 7--9 connect this general estimation theory to the reconstruction problem through exact controlled-target alignment, native missing-value nonidentifiability and sufficient conditions for safe switching. These results distinguish CCR from simply applying a generic expert selector to imputation. We explicitly separate theorem-calibrated GL from validation-tuned GL; the formal linearity, noise and excitation assumptions are not asserted to hold uniformly on real data.

3. Absolute imputation performance and stronger comparisons (W3).

The revised benchmark reports actual MAE and RMSE. T1 is now explicitly described and cited as the channel-head-binding architecture of Park et al. The expanded library adds BRITS to Linear, SAITS and T1, with individual-imputer and stronger online-selection comparisons under a shared protocol.

Table 2 reports mean micro-MAE for Static/MS/GL-Tuned:

DatasetStaticMSGL-Tuned
ETTh1.29617.28123.27413
Weather.04066.04358.04083
MIMIC-IV.19989.21749.20611
PhysioNet-B.39291.39919.39649

GL-Tuned improves original CCR-MS on all four primary datasets, with reductions of 0.68--6.30%. Of 96 paired primary family-by-rate macro-MAE comparisons, 76 pointwise 95% intervals favor GL-Tuned, none favor MS, and 20 are inconclusive.

Static remains stronger on three primary datasets. Nevertheless, GL-Tuned improves validation-selected Static by 7.44% on ETTh1, and on exploratory Electricity, GL-Tuned and MS improve even the hindsight best constant imputer by 1.47% and 2.68%.

The contribution is improved selection among frozen imputers, not a new imputer architecture or a claim of universal SOTA superiority. The expanded comparisons establish both practical gains and their limits.

4. Definitions and competence estimation (Q1, Q3).

Section 3, Figure 1, and Appendix A now explicitly define ZtZ_t (visible incomplete context), xt=Φ(Zt)x_t=\Phi(Z_t) (frozen context representation), both target roles, their reconstruction losses, and the pre-decision information field Gt\mathcal G_t.

True evaluation competence is μm,teval=E[Lm,teval∣Gt]\mu_{m,t}^{\rm eval}=\mathbb E[L_{m,t}^{\rm eval}\mid\mathcal G_t]. Its empirical proxy μ~m,teval\widetilde\mu_{m,t}^{\rm eval} is estimated by five-fold cross-fitted ExtraTrees regression of evaluation MAE on role-free context summaries, using patient grouping or purged chronological folds with a 48-step embargo. Ridge sensitivity is also reported. This retrospective feature-conditional proxy is not the true oracle and never enters online routing.

In summary, the revision establishes adaptive routing guarantees, a reconstruction-specific statistical foundation for sparse audits, and measurable improvements in absolute imputation quality under identified conditions. We appreciate the reviewer's emphasis on these questions and respectfully request reassessment in light of these substantive advances.

We sincerely thank the reviewer again for the thoughtful and constructive feedback, which has helped us strengthen the manuscript. We hope that the new theoretical results, numerical evidence, and clarifications address your concerns. We would greatly appreciate your reconsideration of the revised manuscript and welcome any further feedback at your earliest convenience during the discussion period.

Thank you again for your time and careful consideration.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Overall Author Response and Summary of Revisions

Dear Program Chairs, Senior Area Chairs, Area Chairs, and Reviewers,

Thank you for evaluating our submission. We appreciate the recognition of novelty in continual imputer selection (TPe6), the problem framing and audit/evaluation separation (9UDG), and the questions on algorithmic clarity and adaptive memory (BiXh).

1. Adaptive routing under unknown drift: new algorithm and guarantees.

The submitted freshness analysis used a known-reset estimator. We introduce CCR-GL, a causal Goldenshluger--Lepski selector that balances directional uncertainty and cross-scale disagreement without knowing reset times or drift budgets.

Theorem 3 establishes an algorithm-specific directional oracle inequality: audit routing excess is bounded by three times the best available sum of statistical uncertainty and transported drift/approximation bias across candidate horizons.

Theorem 4 establishes switching, variation-budget, and partition-adaptive dynamic-regret guarantees under conditional excitation. Proposition 5 provides matching information-theoretic dependence on horizon, audit probability and drift, up to logarithms under exact relative linearity and fixed dimension. Proposition 6 quantifies noisy post-reset identification costs.

These guarantees apply to formal CCR-GL, not heuristic MS or validation-tuned GL.

2. Reconstruction-specific statistical foundations (TPe6).

Proposition 7 establishes exact expected alignment of pairwise reconstruction-loss contrasts under uniform controlled-target role splitting, with an exact finite-population variance identity. Proposition 8 establishes native missing-value competence nonidentifiability in general. Proposition 9 gives sufficient conditions for safe switching using valid total-error and audit/evaluation discrepancy bounds.

Across 9,792 real contrast conditions, the mean empirical/theoretical variance ratio is 1.000233; channel-biased allocation increases estimated discrepancy on all primary datasets.

We add BRITS, report absolute MAE/RMSE, and evaluate controlled MCAR, MAR and MNAR at 10/30/50% holdout. GL-Tuned reduces micro-MAE versus Static on ETTh1 by 7.81%/9.64% under MCAR30/50 and 9.32%/19.08% under MNAR30/50. These are controlled-target gains, not claims about native MNAR.

3. Corrected benchmark and verifiable evidence (9UDG).

We withdraw the affected Table 2 comparisons: the original Static discrepancy violates the shared-stream invariant, and its cause remains unresolved. The rebuilt benchmark fixes predictions, evaluation targets, validation-selected Static and cross-fitted competence proxies, with nested audit activations. Static MAE and proxy nCPR are now invariant across audit rates.

All 35,472 shared benchmark/replay rows and 4,824 final reference rows match prior metrics; all 112 final validation selections match grid minima. The clinical cohorts have changed, so this is a corrected replacement, not an exact reproduction.

We replace G1/G2 verdicts with explicit estimands and uncertainty intervals, separating hindsight headroom from feature-conditional opportunities and offline selection correction from gains beyond the hindsight best constant imputer.

4. Stronger comparisons and isolated adaptive-memory effects (BiXh, 9UDG).

GL-Tuned reduces mean micro-MAE relative to CCR-MS on all four primary datasets: 2.53% (ETTh1), 6.30% (Weather), 5.23% (MIMIC-IV) and 0.68% (PhysioNet-B). Of 96 paired family-by-rate macro-MAE comparisons, 76 conditional pointwise 95% intervals favor GL-Tuned, none favor MS, and 20 are inconclusive.

GL-Tuned improves validation-selected Static by 7.44% on ETTh1. On exploratory Electricity, GL-Tuned and MS improve even hindsight BestConst by 1.47% and 2.68%, respectively.

We add Hedge, Fixed Share, and restart ridge. A matched study of 1,608 cells isolates memory selection from representation and tuning: three of eight approximately Bonferroni-adjusted GL--Fixed comparisons favor GL, two favor Fixed and three are inconclusive. Static remains stronger on three primary datasets; Lepski and Longest remain competitive. These results identify when adaptation helps and when simpler rules suffice.

5. Substantially improved presentation and methodological transparency.

We have comprehensively reorganized the manuscript to present a coherent progression from problem formulation and algorithmic design to theoretical guarantees and empirical validation. The revised 10-page main text integrates a unified causal pipeline (Figure 1), explicit notation, Algorithm 1, and six tables highlighting the central findings.

The appendices provide detailed proofs, experimental configurations, and extended analyses, ensuring that the main exposition remains accessible without sacrificing mathematical rigor or empirical detail.

We thank all reviewers for their constructive scrutiny and respectfully request reassessment in light of these substantive advances.

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

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