acceptodds
Under review as a conference paper at ICLR 2027

Transferable Evidence Reconstruction for Longitudinal Glucose Representations

Abstract

Long physiological recordings contain many routine measurements, while predictive information often lies in rare events, sustained burden, and recurring patterns. These properties can be computed as label-free evidence, but directly using them as features leaves limited labeled data to separate reproducible associations from sample-specific ones. Learning to reconstruct evidence can exploit unlabeled recordings, yet joint reconstruction does not explicitly require the decoding rule to transfer across individuals. We introduce transferable evidence reconstruction (TER): a Ridge regressor fits evidence from representations in one group and predicts it in an identity-disjoint group without refitting. The transfer error trains the encoder through the differentiable fit. For continuous glucose monitoring (CGM), clock-aware encoding preserves the multi-day content and timing needed for evidence recovery. Matched interventions connect the gains to reduced fitting-group sensitivity, with structured targets improving on raw recovery. Across ten leading CGM and time-series baselines, TER sets a new best metric on 12/14 phenotype tasks and exceeds the strongest prior overall PR-AUC/ROC-AUC/Macro-F1 by 4.95/4.43/0.66 percentage points; the PR-AUC and ROC-AUC gains are 2.6× and 2.2× the respective gaps between the two strongest baselines. Meal-response and future-CGM studies further demonstrate predictive utility. TER thus uses meaningful signal properties to supervise not only what a representation preserves, but how reliably it can be read across individuals.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
self-supervised learning, physiological time series, continuous glucose monitoring, representation learning, longitudinal modeling, AI for health

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_sY4uOpenReview ↗
Rating
1
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
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Paper summary

This paper proposes Transferable Evidence Reconstruction, which first computes 336 hand-crafted CGM summary statistics from up to seven days of data, trains a four-stage neural encoder to reconstruct those 336 statistics via cross-group Ridge regression into a 146-dimensional latent vector, and then fits an untuned linear logistic regression classifier on that latent vector for downstream tasks.

Critical strengths

Comprehensive appendix controls and code release: The authors provide 21 appendices and a full code/checkpoint archive testing linear re-expressions, observation dropouts, and objective swaps. Ironically, these controls show that the complex multi-stage neural pipeline is largely unnecessary once feature scaling and downstream regularization are accounted for.

Critical weaknesses
  1. The core claim is that neural reconstruction of 336 hand-crafted statistics beats using them directly. But it an artifact of an untuned linear classifier penalty, not denoising or representation learning:
  • Static linear re-scaling replicates the gain without a longitudinal neural encoder: In Table 25, feeding the 336 hand-crafted statistics plus daily features (482 dimensions) directly into the benchmark's fixed-penalty logistic regression (C=1) severely overfits on cohorts of 37 to 58 people, hitting 99.92–100% training PR-AUC (Appendix U.7) versus 56.49% test PR-AUC and 65.41% ROC-AUC. However, Appendix U.8 (Table 33) shows that simply multiplying those 482 raw features by a static unlabeled linear matrix to compress them to 146 dimensions boosts ROC-AUC to 70.37% (nearly matching TER's 71.13%) without adding any nonlinearity or new information—merely rescaling feature variances to change the effective regularization under C=1. Moreover, under 20% observation dropout (Appendix U.9, Table 35), TER degrades much more than the raw 336 statistics (-4.00 vs. -1.19 PR-AUC), refuting a denoising explanation.

  • Simple summary statistics and baselines match or beat TER on external and synthetic tasks: In the AIDE trial (Appendix I, Table 13), 21 basic 7-day summary statistics achieve a test MAE of 0.962, slightly beating TER (0.969). On synthetic pulses (Appendix R, Table 20), direct evidence statistics achieve 4x lower error (0.0238) than TER (0.0963). And on post-meal prediction with meal macronutrients included (Appendix J, Table 14 Panel B), X-CGM-JEPA beats TER on all four metrics.

  1. Unfair 7-day vs. 1-day baseline comparisons, contradictory ablations, and failure on core diabetes physiology:
  • Asymmetric context length and 24-candidate selection: In Table 1, TER uses up to seven days of CGM history and selects among 24 candidate checkpoints via supervised inner cross-validation on downstream labels, whereas external baselines receive 1-day windows and use a single fixed checkpoint.
  • Negligible objective effect in BiLSTM, target reversal, and failure on insulin resistance: Holding a BiLSTM architecture fixed and switching its objective to TER adds only +0.42 PR-AUC / +0.24 ROC-AUC while hurting 5 of 14 tasks (Section 5.6, Table 31). Furthermore, Appendix R.4 (lines 1880–1884) admits that on the final daily input used in the released model, the 336 structured evidence targets actually underperform raw hourly reconstruction targets (-0.85 PR-AUC / -0.86 ROC-AUC). Finally, TER loses to prior baselines on both Insulin Resistance and beta-cell dysfunction (Figure 7), including a worse-than-random 38.8% ROC-AUC on Shanghai Insulin Resistance (Table 4).
Questions for authors
  • What are the 14-task test scores for the raw 336 Direct evidence features and 482 Daily + evidence features when the downstream logistic regression regularization strength (or an elastic-net / PCA-logistic pipeline) is tuned via the same inner cross-validation used to select TER's 24 candidates, rather than fixed at C=1?
  • Why does Appendix R.4 (lines 1880–1884) show that structured evidence targets underperform raw hourly targets by -0.85 PR-AUC and -0.86 ROC-AUC on your final daily input, and doesn't this contradict the main text's claim (Figure 4A) that structured evidence improves over raw recovery?
  • How do the external baselines in Table 1 perform when given the same 7-day history as TER (for example, via multi-day pooling or the linear Ridge projection of Appendix U.8)?
  • Why does TER underperform baselines on both Insulin Resistance and beta-cell dysfunction overall (Figure 7) and score 38.8% ROC-AUC (worse than chance) on Shanghai Insulin Resistance (Table 4), where cross-group scoring degrades ROC-AUC by 9.49 points (Table 32)?
Reviewer_fXnPOpenReview ↗
Rating
3
Confidence
4
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper introduces Transferable Evidence Reconstruction (TER), a bi-level self-supervised representation learning framework for longitudinal continuous glucose monitoring (CGM) time series. The core idea is to incorporate manually designed clinical evidence bank H(x)H(x) into a fit-and-reconstruct objective: an encoder learns latent representations Z, while an inner-loop ridge regression fits these representations to reconstruct handcrafted physiological evidence, with subject-level IID splitting used during pre-training to encourage cross-subject generalization.The authors validate TER on both public and private CGM datasets. Main experiments and ablation studies demonstrate that TER outperforms conventional self-supervised and meta-learning baselines on IID cross-subject generalization tasks.

Critical strengths

1.This work proposes a bi-level fit-and-reconstruct self-supervised objective, TER, for longitudinal glucose time series to learn subject-invariant evidence representations. Extensive ablation studies and comparisons against strong baselines (conventional self-supervised methods, meta-learning approaches, and time-series representation learners) on CGM datasets demonstrate that TER consistently improves cross-subject generalization under IID settings. The experimental setup is comprehensive, incorporating both public and private CGM data sources with rich supplementary results in the appendix. The empirical evidence is solid and offers practical insights for representation learning on physiological time series. 2. The paper integrates established clinical physiological evidence patterns into a self-supervised learning framework, offering a novel perspective that combines clinical priors with representation learning. This paradigm provides a viable new recipe for leveraging domain knowledge in self-supervised pre-training for medical time series. The figures are clearly presented, and systematic ablation studies decompose the contribution of each component of TER, making it easy for readers to understand the function of each module.

Critical weaknesses
  1. The TER optimization objective is only supported by heuristic intuition without rigorous theoretical analysis. The paper relies solely on ablation experiments to show performance gains, and Appendix C merely provides a weak existence argument. It fails to establish the statistical assumptions required to prove that TER learns generalizable representations instead of simply memorizing the training set. Bi-level optimization and meta-learning literature have documented meta-overfitting risks for differentiable inner loops, yet the paper does not analyze failure regimes for TER. It remains unknown under which data distributions TER degrades, or whether TER may learn spurious cross-subject correlations from unlabeled pre-training data. The absence of such theoretical boundaries weakens the reliability of the proposed method and undermines the persuasiveness of its core contribution.
  2. The evidence bank H(x)H(x) is entirely hand-crafted using clinical domain knowledge, introducing strong manual inductive bias, while the risk of implicit information leakage remains unquantified. The 336-dimensional evidence features are manually engineered, and the paper does not compute the raw correlation between these hand-designed evidence features and downstream phenotypic labels. Although downstream labels are not directly fed into pre-training, the clinical knowledge used to construct the evidence may already encode biomarkers predictive of the target task. This creates a major confounding risk: performance improvements may come from manually predefined evidence rather than representations learned from raw CGM signals. The paper lacks critical ablation experiments to rule out this confounder, for instance removing hand-tuned thresholds such as 70/180 mg/dL, testing lower-dimensional evidence sets, or adopting purely data-driven evidence banks.
Questions for authors

1.The title and main text of the paper claim that TER learns "transferable evidence". However, the pre-training stage uses an IID split by subject ID, which is only a proxy setup to simulate cross-population generalization and is not equivalent to real-world cross-cohort distribution shift. Moreover, results in Appendix T demonstrate that pre-training on a single-source dataset leads to substantial performance degradation, confirming that cross-cohort distribution shift exists in practice. Please clearly answer: what is the strict definition of "transferability" as used in your paper? In addition, to what extent does this IID cross-subject split used in pre-training approximate real-world cross-cohort distribution shift? 2. The introduction frames TER as a general method for longitudinal physiological time series, yet all real-data experiments are only conducted on CGM blood glucose data without validation on other physiological signals. Please answer whether this fit-reconstruct evidence objective of TER can be extended to other physiological modalities such as PPG, ECG, and wearable activity time series. If yes, please provide preliminary experimental results. If extension is not feasible at this stage, please revise the manuscript and remove overstated claims such as "general paradigm". 3. Multiple mathematical notations (e.g., x,Z,E,H(x),LTER,M,θe,ϕx, Z, E, H(x), \mathcal{L}_\text{TER}, \mathcal{M}, \theta_e, \phi) are used in Figure 1 and Figure 2, but their definitions are only provided in the main text or appendix rather than the figure captions. Figures should be self-contained so readers can understand them solely by viewing the figure and its caption. Please revise the captions of both figures to include definitions for all notations shown in the figures, so readers do not need to navigate to the main text or appendix for explanation. 4. The evidence function H(x)H(x) constructs evidence features using manually fixed thresholds (70/180 mg/dL). Please quantify the raw correlation between these hand-designed evidence features and downstream prediction labels. Also, please add ablation experiments: evaluate TER performance when these handcrafted thresholds are removed and the evidence bank is built using purely data-driven statistics. This is needed to rule out the possibility that performance gains come from implicit label leakage embedded within the manually defined evidence. 5. TER adopts a bi-level optimization framework with closed-form ridge regression for the inner loop. It is well-known in meta-learning that differentiable inner-loop optimization of this type is prone to meta-overfitting, where the model memorizes spurious correlations from the training population. Please provide training curves (evidence reconstruction loss on training/validation sets over training epochs) to illustrate whether meta-overfitting is observed during TER training, and discuss the data conditions under which TER fails.

Reviewer_uujROpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper proposes TER for learning longitudinal CGM representations. It fits a differentiable Ridge regressor on one group of participants to recover signal-derived evidence on another group, combined with a custom multi-day encoder and clock-aware memory. It builds on a growing body of work on glucose foundation models.

Critical strengths

The paper addresses a meaningful problem: learning CGM representations that capture multi-day burden and recurring patterns. The fit–transfer framing is clear and well-motivated. I liked the matched factorial and same-solver experiments. The authors also do a good job showing cross-group recovery within the pipeline.

Critical weaknesses

The main baseline comparisons seem a bit uneven. TER uses up to seven days of history and inner-fold candidate selection, while the CGM baselines keep their single-day native interfaces without multi-day adaptation or comparable tuning. Even in the public-only setup, the data are matched, but not the history window or optimization budget. Since the core task is multi-day representation learning, it would be much more convincing to pretrain and compare against a native multi-day CGM baseline such as GluFormer (cited in Related Work but omitted from the experiments) on the same data and history length. Similarly, the large gain over BiLSTM changes both the architecture and the objective, whereas swapping only the objective inside the same BiLSTM improves average PR-AUC by just 0.42 points. While the internal controls are useful, how competitive are CGM baselines when given matched history lengths and comparable tuning?

I'm still not fully convinced about how much the structured evidence bank itself adds. While Table 3 shows a clear gain over raw episodic recovery, in Appendix R.4 repeating the comparison with a later daily-input retraining actually flips the result in favor of raw recovery, and the fine-raw comparison also looks unfavorable. Even though these come from different training trajectories rather than a direct contradiction, the overall evidence supports the general fit–transfer setup much more reliably than the specific evidence bank. Could you clarify what drives this reversal?

The meal experiment turns off TER’s longitudinal modules, which means it is only testing the daily encoder rather than the core fit–transfer components. The comparison also seems unfair to the external baselines: most of the participants in this private cohort contributed unlabeled CGM to TER’s pretraining pool. Even with this advantage, when given the same recent CGM and meal context, X-CGM-JEPA still gets lower mean errors on all four endpoints. Similarly, in the AIDE trial, which predicts Weeks 7–12 summary outcomes from Weeks 5–6 within the same treatment period, the model doesn't clearly beat simple seven-day summary statistics on the held-out hypoglycemia task, with the CI crossing zero. Reporting this simple statistical baseline across all seven outcomes in Table 12 would make it much easier to see the method's real added value.

Questions for authors

How competitive are CGM baselines when evaluated with matched multi-day histories and comparable candidate selection?

What explains the reversal in Appendix R.4 where structured evidence falls behind raw episodic recovery under the later daily-input retraining, and how stable is the structured-target advantage across random seeds?

Could you report the seven-day statistics baseline from the appendix across all AIDE outcomes in the main text?

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

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