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Under review as a conference paper at ICLR 2027

Task-Supervised and Cost-Aware Koopman–Kalman Filtering for Recognition under Missing Observations

Abstract

Learning from partially observed sensor streams requires representations that preserve task-relevant information without reconstructing every missing measurement. Temporal predictions can compensate for incomplete observations, yet unreliable priors may also distort informative current measurements. We propose Task-Supervised and Cost-Aware Koopman–Kalman Filtering (TSCA-KKF), a unified framework for recognition under missing observations and sensing budgets. TSCA-KKF learns a task-supervised latent representation with approximately linear Koopman dynamics and recursively combines temporal predictions with current measurement states through a measurement-anchored update. A bounded, adaptive prior-use coefficient accounts for observation incompleteness, prior confidence, and innovation magnitude, thereby limiting prior intervention when measurements are sufficiently informative or strongly disagree with the prediction. We further couple the estimator with a budgeted observation policy that balances predicted task utility, update value, sensing cost, and sensor redundancy. Theoretically, we establish deterministic bounds on prior-induced representation displacement, derive finite-time estimation-error bounds, and characterize recursive stability under an explicit contraction condition. Experiments on four wearable activity-recognition benchmarks demonstrate favorable recognition–cost tradeoffs under incomplete sensing. On three incomplete-observation benchmarks, TSCA-KKF improves macro-F1 by 1.6–2.4 percentage points over the evaluated mask-aware routing baselines while using lower mean sensing cost. In a strong-observation regime, it preserves recognition performance where fixed prior fusion causes substantial degradation. These results demonstrate that task-supervised latent dynamics, controlled prior intervention, and cost-aware sensing provide a principled approach to recognition from incomplete sequential observations.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
representation learning;Koopman dynamics;filtering;missing observations;active sensing

Reviews

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1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_V6mcOpenReview ↗
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1
Confidence
2
Informativeness
2
Presentation
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1
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Paper summary

This paper proposes TSCA-KKF for recognition under incomplete wearable sensing. It couples (i) a task‑supervised Koopman‑style latent predictor, (ii) a measurement‑anchored “selective” update z ^+=z^m +ρ(z ^− − z^m ) whose scalar gain ρ is modulated by missingness and attenuated by large prior–measurement innovation, and (iii) a non‑anticipatory cost‑aware acquisition loop. It proves displacement/decision‑preservation bounds, a finite‑time recursion with a sufficient contraction condition, and budget/non‑anticipation guarantees. Four wearable HAR benchmarks report 1.6–2.4 pp macro‑F1 gains over a mask‑aware Transformer under limited sensing, plus matched isolation controls.

Critical strengths

None

Critical weaknesses
  1. The evidence does not adequately validate the central “selective intervention” claim. The main deployment evidence is essentially descriptive three‑run macro‑F1/NLL/ECE (Table 1; repeated in Appendix Table 10), with no subject/recording‑level cluster bootstrap and with OPPORTUNITY having only four subjects (the paper itself calls the +0.1 pp result saturated and non‑meaningful). Robustness is not systematically established: there is no broad sweep over budget B , missing rate, block‑outage length, cost vectors, and no structured/correlated missingness, corruption‑vs‑missing disentanglement, or cross‑domain transfer. The mechanism argument leans on frozen‑representation harm/repair (Table 4) and a controlled latent perturbation (Table 8), but harm and repair have different denominators and are explicitly not comparable by subtraction; certificate coverage is mentioned but not reported as a bug‑free coverage value. Because the theory is a worst‑case envelope rather than an explanation of macro‑F1, the gap between bound and accuracy is never quantified, so the paper does not demonstrate that the structured gate—rather than task supervision, calibration regularization, or a favorable baseline—is responsible for the gain.
  2. Comparison set is dated and partly self‑defined, so the headline 1.6–2.4 pp gain lacks external validity. The principal “protocol baseline” mask‑aware Transformer is introduced by the authors and is small (two layers, four heads, width 64). External adaptations are mostly 2018–2023 (GRU‑D 2018; SAITS 2023; KalmanNet 2022; Li & Oliva 2021; K2VAE 2025), while recent directly related systems discussed but not run under the unified protocol include Olgúin et al. 2025, KALIKO 2025, information‑shaped Koopman (Cheng et al. 2026), and HyperEF 2026. The work also avoids strong modern missing‑time‑series/forecasting encoders and recent imputation/diffusion recovery baselines, arguing a formulation difference rather than reporting numbers. That may be defensible scientifically, but it means the measured gap could reflect a weak or under‑tuned comparator and a tailored information boundary rather than a robust advantage; the small selector AUPC margin (0.9132 vs. 0.9082, deterministic integration, no significance) further weakens the closed‑loop claim.
  3. Acquisition is admitted to be a density heuristic with no optimality or submodular approximation guarantee (Eq. 9). Given that “causal cost‑aware acquisition” is one of three headline roles, the paper should compare against a budget‑greedy/submodular selector when an appropriate objective exists and against a learned RL acquisition policy under identical information and budget, rather than only random/entropy/generative‑surrogate controls.
  4. Terminology should be downgraded throughout. “Task‑supervised” is clarified as recognition supervision rather than sufficiency, and “Koopman–Kalman filtering” is clarified to exclude posterior covariance/Bayesian optimality/exact invariance. Calling a bounded scalar gain a “Kalman” update and a convex correction an “intervention” risks mis‑setting reviewer/reader expectations; renaming (e.g., measurement‑anchored gated predictor‑corrector) would more accurately reflect the contribution.
Questions for authors
  1. The evidence does not adequately validate the central “selective intervention” claim. The main deployment evidence is essentially descriptive three‑run macro‑F1/NLL/ECE (Table 1; repeated in Appendix Table 10), with no subject/recording‑level cluster bootstrap and with OPPORTUNITY having only four subjects (the paper itself calls the +0.1 pp result saturated and non‑meaningful). Robustness is not systematically established: there is no broad sweep over budget B , missing rate, block‑outage length, cost vectors, and no structured/correlated missingness, corruption‑vs‑missing disentanglement, or cross‑domain transfer. The mechanism argument leans on frozen‑representation harm/repair (Table 4) and a controlled latent perturbation (Table 8), but harm and repair have different denominators and are explicitly not comparable by subtraction; certificate coverage is mentioned but not reported as a bug‑free coverage value. Because the theory is a worst‑case envelope rather than an explanation of macro‑F1, the gap between bound and accuracy is never quantified, so the paper does not demonstrate that the structured gate—rather than task supervision, calibration regularization, or a favorable baseline—is responsible for the gain.
  2. Comparison set is dated and partly self‑defined, so the headline 1.6–2.4 pp gain lacks external validity. The principal “protocol baseline” mask‑aware Transformer is introduced by the authors and is small (two layers, four heads, width 64). External adaptations are mostly 2018–2023 (GRU‑D 2018; SAITS 2023; KalmanNet 2022; Li & Oliva 2021; K2VAE 2025), while recent directly related systems discussed but not run under the unified protocol include Olgúin et al. 2025, KALIKO 2025, information‑shaped Koopman (Cheng et al. 2026), and HyperEF 2026. The work also avoids strong modern missing‑time‑series/forecasting encoders and recent imputation/diffusion recovery baselines, arguing a formulation difference rather than reporting numbers. That may be defensible scientifically, but it means the measured gap could reflect a weak or under‑tuned comparator and a tailored information boundary rather than a robust advantage; the small selector AUPC margin (0.9132 vs. 0.9082, deterministic integration, no significance) further weakens the closed‑loop claim.
  3. Acquisition is admitted to be a density heuristic with no optimality or submodular approximation guarantee (Eq. 9). Given that “causal cost‑aware acquisition” is one of three headline roles, the paper should compare against a budget‑greedy/submodular selector when an appropriate objective exists and against a learned RL acquisition policy under identical information and budget, rather than only random/entropy/generative‑surrogate controls.
  4. Terminology should be downgraded throughout. “Task‑supervised” is clarified as recognition supervision rather than sufficiency, and “Koopman–Kalman filtering” is clarified to exclude posterior covariance/Bayesian optimality/exact invariance. Calling a bounded scalar gain a “Kalman” update and a convex correction an “intervention” risks mis‑setting reviewer/reader expectations; renaming (e.g., measurement‑anchored gated predictor‑corrector) would more accurately reflect the contribution.
Reviewer_xLyDOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes Task-Supervised and Cost-Aware Koopman–Kalman Filtering (TSCA-KKF) for recognition under incomplete sensor observations and sensing budgets. The framework combines task-supervised Koopman-based temporal prediction, a constrained update that balances current measurements with predictions, and cost-aware sensor acquisition. The authors derive bounds on intervention and recursive estimation errors, along with guarantees for decision preservation under specified conditions and budget-feasible acquisition. Experiments on four wearable activity-recognition datasets demonstrate modest improvements over existing baselines, supported by ablation studies and controlled comparisons.

Critical strengths
  1. A well-motivated constrained update mechanism. The measurement-anchored intervention rule addresses an important limitation of unconstrained prediction–measurement fusion: temporal predictions can be useful under incomplete observations but harmful when current measurements are already informative. The explicit preservation and bounded-intervention properties provide a meaningful inductive bias, supported by both theoretical analysis and controlled experiments.

  2. Careful efforts to isolate the proposed mechanisms. The paper goes beyond end-to-end performance comparisons by separately evaluating the estimator, acquisition policy, and update mechanism under matched conditions. The inclusion of strong and weak observation regimes, complete outages, and failure-case diagnostics makes the evaluation more informative and helps substantiate the claimed benefits of selective intervention.

Critical weaknesses
  1. Limited methodological novelty relative to the complexity of the framework. The proposed architecture combines well-established components, including learned Koopman dynamics, Kalman-inspired latent updates, adaptive gating, and cost-aware feature acquisition. Although the constrained intervention rule is interesting, its mathematical properties largely follow from the chosen parameterization. Similarly, several theoretical guarantees characterize the constructed algorithm rather than establish a fundamentally new result. The paper does not sufficiently demonstrate why the overall integration constitutes a substantial methodological advance beyond existing learned filtering and acquisition approaches. This is my principal concern regarding its significance for ICLR.

  2. Limited empirical gains and incomplete evidence for the practical claims. Improvements over the mask-aware Transformer are 1.6–2.4 percentage points on three benchmarks and negligible on the fourth. Although the controlled experiments are useful, some advantages over simpler learned interpolation are relatively small. The principal benchmark results lack subject-level uncertainty estimates, and Appendix D.2 acknowledges missing run manifests and configuration information needed for exact reproduction. Furthermore, sensing costs are normalized proxies rather than measurements of energy, latency, or communication overhead. Consequently, the evidence does not yet fully establish that the additional architectural and training complexity delivers a substantial practical advantage.

Questions for authors
  1. Novelty and necessity of the constrained intervention: What is the most important methodological property of TSCA-KKF that cannot be achieved by a comparably sized learned filtering or interpolation model? Beyond the imposed boundary conditions, is there evidence that the particular functional form of the intervention coefficient is essential to the observed improvements?

  2. Statistical reliability of the empirical gains: Can the authors provide paired uncertainty estimates for the main benchmark comparisons, preferably accounting for subject-level or recording-level dependence? This would help determine whether the reported improvements, particularly the smaller ones, are sufficiently robust to support the conclusions.

  3. Reproducibility of the primary results: Appendix D.2 states that the retained artifact lacks the primary run manifests, dataset-specific sensing-cost vectors, and operating-point selection information. Can these configurations be recovered and provided, or can the main comparisons be reproduced using the fully specified experimental protocol?

  4. Complexity versus benefit: Can the authors quantify the additional training and inference costs of TSCA-KKF relative to the strongest simpler baselines? Since cost-aware acquisition is a central motivation, understanding whether the sensing savings outweigh the additional computational overhead would materially affect the practical significance of the contribution.

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

This paper introduces TSCA-KKF, an online framework for budgeted multi-sensor time-series classification that couples a linear latent state predictor and a scalar prior-measurement interpolation gate with a greedy cost-aware sensor selection policy, evaluated on four human activity recognition benchmarks.

Critical strengths

The paper tackles an interesting, realistic, and practically important problem for real-world multi-sensor time-series deployments: how to dynamically select which sensors to query under a strict resource budget while maintaining robust recognition when sensor streams are missing or intermittently dropped. In wearable human activity recognition and edge IoT settings, continuously polling every sensor is often prohibitive due to battery, bandwidth, and latency constraints, yet aggressive subsampling degrades downstream accuracy. Formulating budgeted active sensor acquisition and temporal state estimation as a joint, online closed-loop problem, rather than treating missing-data imputation and active sensing completely in isolation, is well-motivated. Furthermore, the paper evaluates this setting across four standard multi-sensor benchmarks (UCI-HAR, RealWorld HAR, REALDISP, and OPPORTUNITY) and includes helpful module-level isolation studies (Tables 4–8) that allow readers to inspect the behavior of the predictor, interpolation gate, and acquisition rule independently.

Critical weaknesses
  1. The paper seems to be overclaiming a mathematical foundation, and it is unclear what it contributes to the methodological claims. For example,
  • Proposition 1 (Equation 11) is not a substantive theoretical result, as its proof in Appendix A.1 follows trivially from plugging the authors' rational attenuation definition (Equation 6) into Equation 5 and applying the basic AM–GM inequality (a² + b² ≥ 2ab).

  • Proposition 2 (Equation 12) follows directly by definition from the authors' own assumptions of Lipschitz continuity and classification margin (Appendix A.1): if the winning class leads by a margin γ_m and each logit can shift by at most L_g |Z⁺ - Z^m|_F, then keeping the perturbation below (γ_m)/(2L_g) trivially guarantees the winning class cannot be overtaken.

  • Theorem 1 and Corollary 1 (Equations 13–15) fail to hold in the authors' own experiments. Because the derivation replaces the data-dependent gate ρ_t with a loose worst-case constant ρ_(max), the resulting asymptotic stability condition (κ_L = ρ_(max) max_(1 ≤ h ≤ L+1) ‖A‖₂^h < 1, Equation 14) is violated by the paper's own default training configuration (‖A‖₂ ≤ 1.1, ρ_(max) = 0.6, Equation 27), which yields κ₈ ≈ 1.415 > 1 (Appendix A.3, line 683) and leaves the L=8 outage regime in Table 7 theoretically uncertified.

  1. While I appreciate the authors' candor in Section 1 (lines 90–97) clarifying that "Koopman–Kalman" does not imply covariance tracking or Bayesian filtering, I think it still implies an overstating, especially as this is within the title without context. In general, I am also of the opinion that the text is written in an overly mathematical way that makes it difficult for readers to intuit how the methodology really works, which is further reflected in over-assuming that I discussed my Weakness 1. Writing out that causal is defined by “non-anticipatory with respect to the acquisition information set rather than causal-effect identification” in Line 094 is extreme overkill. Causal could simply be defined as only dependent on past features, and this is well understood throughout the time-series and NLP literature. I am not sure why the authors are seemingly obfuscating the framing of the paper. It seems like they are prioritizing falsifly elevating it rather than clarity. As such, much of the rest of the paper is very difficult to digest and interpret.

  2. The cost-aware experiments are neither reproducible in the main benchmark nor actually cost-heterogeneous in the controlled ablations, which undermines a central claim of the paper's title. Specifically, while Table 1 (and Appendix Table 10) reports the primary deployment benchmark under heterogeneous sensor costs c = (c₁, …, c_M), the authors disclose in Appendix D.2 (lines 947–953) that "the retained submission artifact does not contain the corresponding run manifests identifying the three primary seeds, numerical dataset-specific proxy vectors, or the per-dataset operating-point selection." Leaving out the actual numerical sensor cost vectors c_i, budget thresholds B, and random seeds used to generate the main results makes it impossible to verify or reproduce the paper's core cost-aware claims. Furthermore, when the authors do isolate the acquisition policy in a reproducible five-seed study (Section 6.5, lines 384–390; Table 6 and Table 13), they set all sensor costs to be uniform (c_i = 1/M) and disable the STOP action. Because every sensor has the exact same cost in this ablation, the cost denominator in the acquisition rule (r_t^i(S) = Δ_t^i(S) / c_i, Equation 9) is constant across candidates, meaning heterogeneous cost-awareness is never reproducibly isolated. Even in this simplified uniform-cost setting, the proposed full policy (0.9132 ± 0.0067 AUPC) improves over the existing Generative-surrogate acquisition baseline (0.9082 ± 0.0073) and the simpler Novelty + uncertainty ablation (0.9096 ± 0.0072) by only 0.0036–0.0050 AUPC, which is well within one standard deviation.

  3. There is a disproportionate engineering and hyperparameter complexity. The framework requires tuning a six-term loss objective (Equation 10), three multiplicative gating heuristics with reference thresholds (ρ_(max), m_(ref), η_(ref) in Equation 6), a spectral cap (‖A‖₂ ≤ 1.1 in Equation 27), and a three-part acquisition score trained with REINFORCE (Equations 8–9; Table 9). Yet the paper's controlled five-seed ablations reveal that stripping away these bespoke mechanisms barely affects performance: a plain MLP gate comes within 0.3–0.8% Macro-F1 of the Equation (6) gate across all four datasets (Table 5) while achieving a higher error-repair rate (18.5%–21.0% vs. 14.8%, Table 4) and better robustness to noisy sensors (0.855 vs. 0.828, Table 8); a standard GRU matches the Koopman predictor within 0.2% F1 at L=1 (0.754 vs. 0.756, Table 7); and an existing generative-surrogate acquisition baseline matches the full acquisition policy within 0.005 AUPC (0.9082 vs. 0.9132, Table 6). The marginal empirical payoff does not justify the heavy architectural and hyperparameter overhead.

Questions for authors

See Weaknesses Above

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