acceptodds
Under review as a conference paper at ICLR 2027

Time-Aware Differentiable Subgroup Discovery

Abstract

Subgroup Discovery (SD) seeks interpretable subsets exhibiting exceptional relationships with a target variable, but conventional SD largely treats observations as static and exceptionalness as a scalar. This is inadequate when subgroup differences emerge only during particular periods or follow distinct temporal trajectories. We introduce Time-Aware Differentiable Subgroup Discovery (TDSD), which formulates longitudinal discovery as a unified who–when–how problem: identify an interpretable subgroup, localize when its discrepancy is strongest, and characterize how that discrepancy evolves. TDSD uses differentiable soft predicates and feature-selection gates for subgroup generation and differentiable temporal boundaries for window discovery. It estimates a subgroup-specific treatment–control discrepancy trajectory and optimizes a window-aware temporal quality measure, while also supporting full-trajectory behavior discovery. Synthetic experiments evaluate subgroup, temporal-window, and temporal-behavior recovery, followed by a MIMIC-IV ICU treatment-response study. TDSD recovers informative temporal structure and substantially improves temporal localization over increasingly time-aware alternatives, while experiments also expose a remaining gap between soft optimization and exact hard-rule recovery.

Primary area:
interpretability and explainable AI
Keywords:
Subgroup Discovery, Differentiable Predicates, Temporal Behavior

Reviews

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1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
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Paper summary

The method discovers subgroups defined by baseline covariates and jointly optimizes a temporal window. The empirical experiments primarily provide synthetic recovery demonstrations and internal objective comparisons, without clearly identified comparisons against established methods.

Critical strengths

The problem formulation may be useful. Jointly returning a subgroup rule and a temporal window can be a reasonable goal.

Critical weaknesses
  1. Insufficiently established methodological novelty. The paper uses sigmoid predicates, feature gates, and smooth interval boundaries, but does not clearly establish what the joint formulation contributes beyond existing differentiable rule learning and temporal subgroup discovery. The absence of external comparisons makes that contribution especially difficult to assess.

  2. Limited empirical validation and reproducibility. The experiments primarily provide synthetic recovery demonstrations and comparisons among internal objective variants. They do not clearly identify or evaluate established competing methods. Furthermore, the optimization settings, baseline definitions, synthetic data generation, and real-world data preprocessing are insufficiently specified to reproduce and assess the results.

Questions for authors
  1. Please provide sufficient implementation details for reproducibility, including optimizer settings, stopping criteria, temperature schedules, regularization coefficients, hyperparameter selection, and so on. For the synthetic experiments, please specify the data generation process and covariate and treatment distributions.

  2. For the real-world MIMIC data, please provide details for data processing, including treatment definition, time-zero alignment, baseline measurement windows, missing-data handling, and so on. Please also interpret the discovered temporal pattern.

  3. Please compare with established subgroup-discovery methods, including relevant approaches discussed in the related work. Where necessary, explain how these methods are adapted to longitudinal outcomes. Such comparisons would help establish the benefit of joint subgroup and temporal-window optimization beyond the internal ablations.

  4. Please define the exact objectives and implementations of “Static,” “Global Temporal,” “Window,” and “Behavioral,” as well as “Static SD,” “ATE-SD,” and “Temporal SD.” In particular, how are windows obtained for variants without explicit window optimization, and why do all three clinical comparators return the same subgroup?

4 comments

We thank the reviewer for recognizing the potential usefulness of jointly discovering subgroups and temporal windows. We address the concerns about novelty, empirical validation, and reproducibility below.

Weakness 1: Methodological novelty

Our novelty lies not in individual sigmoid predicates or feature gates, but in coupling subgroup discovery and temporal localization through the subgroup-specific discrepancy trajectory ΔS(t)\Delta_S(t). Changing the subgroup changes the preferred window, while changing the window changes which subgroup is rewarded. This differs from discovering a subgroup using a fixed temporal summary and subsequently identifying its window. Our new discrete-search comparisons (Q3) support the benefit of this coupling for temporal localization, although they do not establish universal superiority of differentiable search.

Weakness 2: Empirical validation and reproducibility

We agree that the original internal ablations are insufficient. We have completed a new outcome-only benchmark with 20 seeds, five temporal patterns, independent training/test samples, and discrete subgroup-search baselines. We additionally introduce coverage weighting, minimum window duration, arm-support safeguards, and improved hard-rule extraction. The revised benchmark does not use these labels for training. We will release the configurations, code, and per-run results.

Q1. Implementation details and synthetic data generation

The synthetic data follow Yi(t)=μ(t)+AiSi∗τ(t)+ϵi(t)Y_i(t)=\mu(t)+A_iS_i^*\tau(t)+\epsilon_i(t), with independent standard-normal covariates, independent Bernoulli(0.5) treatment, and planted rule S∗=1[X1>0.8,X3<0,X6>0.5]S^*=1[X_1>0.8, X_3<0, X_6>0.5].

The revised benchmark uses 2,500 training and 2,500 test individuals per seed, with (p,T)=(10,30)(p,T)=(10,30) or (50,100)(50,100), μ(t)=0.1t+0.4sin⁡(t/3)\mu(t)=0.1t+0.4\sin(t/3), and Gaussian noise SD 0.5. For l=⌊0.4T⌋l=\lfloor0.4T\rfloor, h=⌊0.7T⌋h=\lfloor0.7T\rfloor, the five effect functions are 2.51[l,h](t)2.5\mathbf{1}_{[l,h]}(t), 2.51t≥l2.5\mathbf{1}_{t\ge l}, 2.5t/(T−1)2.5t/(T-1), 2.5(1−t/(T−1))2.5(1-t/(T-1)), and 2.5sin⁡(4πt/(T−1))2.5\sin(4\pi t/(T-1)).

SettingRevised TDSD
OptimizerFull-batch Adam, learning rate 0.03
Stopping350 iterations; no early stopping
TemperaturesPredicate 0.20; window 0.50; fixed
Coverage exponent0.5 (0 for coverage-free ablation)
RegularizationGate-sum coefficient 0.01; support penalty coefficient 2
Support / windowTarget arm weight and effective sample size 10; minimum 3 time points
Hard-rule extractionTop 1–3 gates, learned thresholds and signs; training-only selection

Thresholds, gate and window logits start at zero; direction logits start at 0.2N(0,1)0.2\mathcal N(0,1). Every ten epochs and at the end, feasible hard-rule candidates are scored on training data; the selected rule and window are frozen for testing. Hyperparameters are fixed heuristic settings, not tuned using planted labels. The original experiments used Adam (0.03), fixed budgets of 800/1500/1200/350 iterations, and fixed temperatures; the full original configurations will be provided in the appendix.

Q2. MIMIC-IV preprocessing and interpretation

  • Cohort and treatment: The archived extraction specifies adults, first ICU stay per subject, and ICU duration ≥30 h. Treatment is norepinephrine/noradrenaline initiated within the first 6 h; controls have no recorded initiation during the stay. Later initiators are excluded.
  • Time zero: Six hours after ICU admission for both groups, not treatment initiation. MAP is followed for 24 h.
  • Measurements: Hourly MAP uses the nearest plausible observation (20–200 mmHg) within ±0.5 h; baseline MAP uses the preceding hour. Lactate and creatinine use the nearest observation within ±6 h of the landmark. Exact executed SOFA extraction remains to be verified.
  • Missing data and adjustment: At least five observed MAP values are required; internal gaps are linearly interpolated and remaining gaps filled by time-specific medians. Numeric covariates are median-imputed. Stabilized propensity weights use a class-balanced logistic model with probabilities clipped to [0.05,0.95]. This does not address time-varying confounding or eliminate selection bias.

The discovered lactate ≥2.10 rule covers 6,753 individuals, with a soft window of [4.52,14.06] h after the landmark. Lactate may indicate physiological stress, but this is exploratory, not a causal treatment recommendation. The original figures plot soft trajectories whereas the table evaluates a hard rule extracted using feature medians. We will recompute both using the same frozen rule and window, correct the extractor to use learned thresholds and directions, and withdraw the selection-unadjusted permutation p-value as confirmatory evidence. Independent clinical validation remains outstanding.

Q3. Comparisons with established subgroup-discovery methods

We added two conventional beam-search SD/EMM comparators: Beam-Exact, which ranks candidate rules using exact temporal-window scanning, and Static-then-Scan, which selects a rule using a static discrepancy before scanning its trajectory. Both use coverage weighting, minimum support, four quantile thresholds per feature in both directions, beam width 5, and maximum depth 3.

MethodTransient IoUMean F1Mean trajectory RMSELarger-scale runtime (s)
Beam-Exact0.3150.7280.52817.838
Static-then-Scan0.3200.5900.74517.830
Behavior + Scan0.3200.7450.4113.771
TDSD without coverage0.8750.6010.4623.932
Revised TDSD0.7750.6980.3224.119

Across 20 seeds, revised TDSD improves transient IoU over Beam-Exact by 0.460 (paired 95% CI [0.399,0.521]); in the larger regime, IoU is 0.742 versus 0.102. Mean F1/RMSE aggregate five patterns; RMSE excludes infeasible test contrasts (2/100 standard and 7/100 larger runs for revised TDSD). Beam-Exact achieves higher F1, and TDSD is slower in the standard regime. Thus the results support a localization–recovery–runtime trade-off rather than dominance.

These are conventional discrete-search implementations, not reproductions of specific published methods. Comparisons with Xu et al. (2024) on window-averaged outcomes and Wei et al. (2020) remain outstanding.

Q4. Exact baseline definitions and window selection

Let dtd_t denote the subgroup-specific treatment–control discrepancy, and MWM_W its mean absolute value within window WW.

Original synthetic variantOptimized quality
Static$
Global Temporal$\operatorname{mean}_t
Windowmax⁡W∈CMW\max_{W\in\mathcal C}M_W over eight predefined soft windows
Behavioralmean⁡tdt2\sqrt{\operatorname{mean}_t d_t^2}
TDSDSoft-window-weighted MWM_W, with learned boundaries

Originally, non-TDSD windows were obtained from the test trajectory's half-peak envelope; TDSD stored its training window without restoring the corresponding checkpoint. We acknowledge these evaluation inconsistencies. The revised benchmark selects and freezes both rules and windows on training data before testing.

Original clinical comparatorFinal ranking objective
Static SDAbsolute signed mean discrepancy
ATE-SDMean absolute discrepancy (not a causal ATE estimator)
Temporal SDMaximum mean absolute discrepancy over windows of 3–12 points

All three clinical variants share the same beam expansion ranking (mean absolute discrepancy), candidate pool, beam width 50, depth 4, and minimum support of 50 overall and 20 per arm. Static SD and ATE-SD obtain windows by post-hoc exact scanning; Temporal SD scans retained candidates before final selection. Their identical output is explained by shared search and similar rankings, not agreement among independent algorithms. We will label them accordingly.

We appreciate the reviewer's suggestions and will incorporate these clarifications and the completed benchmark results into the revision.

Thank you for the candid response. I appreciate the authors' efforts, but my main concerns remain unresolved.

  1. Insufficient motivation and methodological novelty. The authors clarify that their contribution lies in the joint formulation rather than the combination of standard techniques. However, they do not convincingly establish why "jointly discovering subgroups and temporal windows" constitutes a meaningful problem beyond identifying increasingly fine-grained patterns in the data. Moreover, the clinical experiment lacks convincing interpretation and validation of the discovered temporal patterns. Therefore, neither the methodological development nor the empirical case study sufficiently demonstrates the significance of this formulation.

  2. Missing comparisons with established methods. The additional baselines are custom implementations rather than established published methods. The authors acknowledge that comparisons with relevant existing methods remain outstanding.

  3. Serious concerns about experimental rigor and reproducibility. The authors acknowledge substantial problems in the original evaluation, including test-data-dependent window selection, inconsistent checkpoint handling, and discrepancies between the soft and hard subgroup evaluations. Furthermore, hyperparameters were selected heuristically without sufficient justification. These are substantial evaluation issues rather than minor implementation details. Moreover, essential configurations, code, and corrected clinical analyses are still promised for future release rather than provided for assessment.

Overall, while the response provides useful clarifications, it also reveals additional weaknesses in the original evaluation. My concerns about novelty, empirical evidence, and soundness remain. I therefore maintain my original rating.

Thank you for your further assessment. We appreciate your concerns and have revised the manuscript to clarify the contribution and strengthen the empirical evidence. We would like to emphasize three points.

1. Motivation and methodological novelty. The contribution is not simply combining sigmoid predicates with smooth windows, nor discovering increasingly fine-grained patterns. It addresses the interdependence between who exhibits an exceptional discrepancy and when that discrepancy occurs. Under our synthetic model, an episode-specific effect in a subgroup of prevalence π\pi is attenuated by π∣W∗∣/T\pi|W^*|/T when averaged across the population and time horizon. Consequently, selecting a subgroup or temporal interval independently can obscure the very signal being sought. Our joint objective allows the interval to influence rule learning and the evolving subgroup to influence interval learning, while coverage weighting, minimum duration, and arm-support safeguards discourage degenerate solutions (Sections 3.6–3.9 and 4.6). The novelty lies in this coupled, interpretable discovery objective and its optimization, rather than in the individual relaxation techniques.

2. Comparisons with competing methods. Beam-Exact and Static-then-Scan are adaptations of conventional beam-search subgroup discovery to longitudinal outcomes, not additional internal ablations. They explicitly test discrete joint search and sequential discovery, respectively. With 20 paired seeds, TDSD achieves transient-window IoU of 0.775, compared with 0.315 and 0.320, respectively (Appendix G, Tables 5–7). The corresponding paired gains are 0.460 and 0.455, with 95% confidence intervals excluding zero. At 50 covariates and 100 time points, TDSD achieves IoU of 0.742 versus 0.102 for Beam-Exact, with mean runtimes of 4.12 versus 17.84 seconds. These results establish advantages over the specified search alternatives under the tested settings.

3. Experimental rigor and reproducibility. We agree that the original evaluation issues were substantive. The revised paired benchmark addresses them through independent training and test samples, training-only selection of hard rules and windows, consistent checkpoint selection, and evaluation of the frozen discoveries. Ground-truth membership is used only for evaluation in this benchmark. Coverage weighting improves mean hard-rule F1 from 0.601 to 0.698 in the standard setting and from 0.516 to 0.699 in the larger setting. The revised manuscript now provides the data-generating process, optimization settings, initialization, temperatures, penalties, baseline definitions, per-pattern results, paired confidence intervals, support failures, and clinical preprocessing (Appendices G–I). We distinguish these completed experiments from the original component checks and remove the unsupported confirmatory clinical significance claim. We believe that code is not the only evidence to support reproductivity, we provided detailed setting for our experiments and we believe that this can be sufficient to make our method reproducible.

We respectfully ask that the methodological contribution be assessed in light of the new independent benchmark and its direct test of coupled versus sequential discovery, rather than solely on the original ablations. We believe the revised evidence supports a meaningful contribution to interpretable temporal subgroup discovery, within the explicitly stated scope.

Reviewer_GqXzOpenReview ↗
Rating
3(+1)
Confidence
1(−1)
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes Time-Aware Differentiable Subgroup Discovery (TDSD), aiming to extend traditional static subgroup discovery to longitudinal data analysis. The authors argue that existing subgroup discovery methods typically characterize subgroup exceptionalness using a single scalar value, making it difficult to capture subgroup differences that emerge within specific temporal windows or exhibit distinct temporal patterns.

The proposed method is evaluated on synthetic datasets and the MIMIC-IV ICU dataset. Experimental results demonstrate that TDSD achieves certain improvements in temporal window localization and temporal trajectory recovery.

Critical strengths
  1. The research problem is relatively novel and practically meaningful.

  2. The proposed framework is clear and easy to follow. It integrates subgroup rule generation and temporal window discovery into a unified gradient-based optimization framework. The overall design is natural and well-structured.

  3. The experimental evaluation is relatively comprehensive and provides evidence supporting the effectiveness of the proposed method.

Critical weaknesses
  1. The robustness of the temporal quality measure requires further discussion. This paper performs temporal localization by maximizing the average absolute discrepancy within a temporal window. However, this objective may favor short windows containing large local fluctuations, particularly when the data are noisy or contain outliers. Furthermore, the current window-length regularization mainly discourages excessively long windows, but it remains unclear whether this design can effectively prevent degenerate solutions caused by overly short windows or isolated anomalous observations. I suggest that the authors further discuss this potential limitation and provide additional analysis to demonstrate the robustness of the proposed temporal quality measure.

  2. The subgroup rule recovery performance is relatively weak and does not sufficiently support one of the paper's core objectives. This paper aims to jointly address the Who, When, and How questions. However, the subgroup recovery results are not particularly satisfactory. In Experiment 1, the subgroup recall is only 0.318, with an F1 score of 0.447. More importantly, in Experiment 2, both the subgroup F1 score and Jaccard similarity are 0 after soft-to-hard extraction. These results suggest that even when the model can accurately localize exceptional temporal windows, it may still fail to recover meaningful and accurate subgroup rules. Given that interpretable subgroup discovery is one of the paper's central contributions, I believe the authors should further investigate the reasons behind the failure of soft-to-hard extraction and consider improving this process or providing a more thorough explanation of the observed results.

Questions for authors

I'm not very familiar with this field, but the author can try their best to address my confusion. Please refer to Weaknesses.

If my confusion is resolved, I am willing to improve my score.

3 comments

We sincerely thank the reviewer for recognizing the novelty and practical relevance of the problem, the clarity of our framework, and the value of jointly learning subgroup rules and temporal windows. We agree that robustness to short-window artifacts and reliable symbolic subgroup recovery are essential to the who–when–how formulation. We address both concerns below, including new outcome-driven experiments and the remaining limitations.

W1. Robustness of the temporal quality measure

Response. We agree that maximizing the average absolute discrepancy can favor isolated peaks. In the limiting case of hard windows, if singleton windows are admissible, the maximum window-average absolute discrepancy equals the maximum pointwise absolute discrepancy. A positive window-length penalty can further favor short intervals. The original formulation therefore does not guarantee recovery of a sustained exceptional episode, particularly under noise or contamination.

We have revised the optimization in three ways:

  1. Minimum window duration. Instead of relying on the original length penalty, we constrain the temporal boundaries to the observation horizon and require at least three consecutive time points in the new benchmark. For a grid indexed by 0,…,T−10,\ldots,T-1, we use ts=(T−L)σ(u),te=ts+L−1+(T−L−ts)σ(v),t_s=(T-L)\sigma(u),\qquad t_e=t_s+L-1+(T-L-t_s)\sigma(v), where L=3L=3. This prevents a singleton interval from being selected and remains differentiable. Extracted hard windows are also required to contain at least LL points.
  2. Coverage-aware quality. We replace the original score by Qcov(S,W)=c(S)1/2∑twW(t)∣ΔS(t)∣∑twW(t)+ϵ,c(S)=1N∑iSθ(Xi).Q_{\mathrm{cov}}(S,W)=c(S)^{1/2}\frac{\sum_t w_W(t)|\Delta_S(t)|}{\sum_t w_W(t)+\epsilon},\qquad c(S)=\frac{1}{N}\sum_i S_\theta(X_i). This discourages extreme discrepancies supported by very small subgroups.
  3. Support safeguards. We penalize insufficient weighted support and effective sample size in each treatment arm at each time point. Hard-rule candidates must have at least ten observations per arm at every time point in the training data. We report insufficient test support as a failure rather than presenting an unstable trajectory as a valid discovery.

New experimental evidence. We evaluated the revised method on 20 seeds per pattern with independent training and test data. In the standard benchmark, transient-window IoU is 0.775±0.1330.775\pm0.133 for coverage-aware TDSD, compared with 0.315±0.0490.315\pm0.049 for Beam-Exact and 0.320±0.0520.320\pm0.052 for Static-then-Scan. All three methods use the same minimum hard-window duration. The paired IoU gains are 0.460 (95% CI [0.399, 0.521]) and 0.455 (95% CI [0.392, 0.518]), respectively. The larger benchmark gives transient IoU 0.742±0.1820.742\pm0.182 for revised TDSD versus 0.1020.102 for both discrete search strategies. The coverage-free TDSD variant actually achieves higher standard-benchmark transient IoU (0.875), illustrating the trade-off between temporal localization and subgroup recovery.

These results demonstrate localization under the benchmark's Gaussian observation noise, but do not establish robustness to severe noise or outliers. A minimum duration restricts the search space without making the mean discrepancy estimator robust: a sufficiently large spike can still dominate an admissible window. We will explicitly state this limitation. A dedicated sensitivity analysis varying noise scale, outlier contamination, and minimum duration, with window IoU, boundary errors, hard F1, and failure rate as outcomes, is planned. A robust alternative is to estimate each arm's trajectory with a Huber location estimator before computing the temporal score.

W2. Weak subgroup recovery and soft-to-hard extraction

Response. We agree that accurate temporal localization alone cannot establish successful subgroup discovery. The original Experiment 1 achieves recall 0.318 and F1 0.447, while Figure 2 shows soft support collapsing as temporal quality increases, and Experiment 2 reports zero F1 and Jaccard after thresholding. These are substantive limitations, not merely presentation issues.

Our inspection of the original implementation identifies two distinct problems. First, the original normalized discrepancy objective is nearly invariant to a common rescaling of membership weights when denominators are well above ϵ\epsilon. The weak support penalty in Experiment 2 does not prevent low-support solutions. Second, thresholding the normalized geometric aggregation at 0.5 is not generally equivalent to requiring every selected hard predicate to hold. The reported original membership-threshold metrics therefore need not correspond to the separately printed logical conjunction. We also clarify that Experiment 1 used binary cross-entropy against planted membership labels (Figure 1b); it was a supervised representation check rather than an outcome-driven discovery experiment.

Revised extraction. During optimization, we rank features by their learned gates, construct hard conjunctions from the top one, two, or three predicates using the learned thresholds and directions, and re-estimate the trajectory of each candidate. We reject candidates with insufficient per-arm support and retain the feasible rule/window checkpoint with the highest coverage-aware training quality. Ground-truth labels are used exclusively for evaluation, and all final metrics are computed on independent test data using the actual extracted conjunction. This avoids equating a fixed soft-membership threshold with a symbolic rule.

New results. The following mean held-out F1 scores aggregate all five temporal patterns, with 20 seeds per pattern:

MethodStandard benchmarkLarger benchmark
Coverage-free TDSD0.6010.516
Coverage-aware TDSD0.6980.699
Beam-Exact0.7280.751
Static-then-Scan0.5900.607

For the transient pattern specifically, revised TDSD achieves F1 0.748±0.0870.748\pm0.087 and Jaccard 0.605±0.1100.605\pm0.110 in the standard benchmark, and F1 0.717±0.0790.717\pm0.079 and Jaccard 0.564±0.0950.564\pm0.095 in the larger benchmark. The paired transient F1 gains over coverage-free TDSD are 0.140 (95% CI [0.106, 0.174]) and 0.205 (95% CI [0.131, 0.280]), respectively. No zero-F1 runs occur among the 100 coverage-aware runs in either benchmark.

The results support improved hard-rule recovery relative to the coverage-free variant, but we acknowledge that Beam-Exact still achieves higher average F1. Moreover, 2/100 standard-benchmark runs and 7/100 larger-benchmark runs fail the held-out per-arm support requirement, despite nonzero membership F1. We will report these failures explicitly.

Questions for Authors

The reviewer refers to the two weaknesses above. Our answers are therefore: (1) the original objective is indeed vulnerable to short-window artifacts; the revised minimum-duration and support safeguards mitigate this degeneracy, but dedicated outlier robustness remains unverified; (2) the original hard-rule recovery is insufficient, and the new outcome-driven, coverage-aware optimization and explicit hard-conjunction selection provide stronger independent evidence of subgroup recovery, while not eliminating all failures.

We will update the methodology and experimental sections accordingly, report mean and standard deviation across seeds, and distinguish the soft search trajectory from the trajectory estimated for the final hard rule. We appreciate the reviewer's constructive feedback, which has helped us strengthen both the formulation and its empirical evaluation.

Thank you for your detailed response. My concerns have been largely addressed.

I decided to raise my rating to “weak accept,” but since I'm not very familiar with this field, and after reviewing the comments from other reviewers, I lowered my confidence rating.

Reviewer_RULfOpenReview ↗
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3(+1)
Confidence
3
Informativeness
2
Presentation
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Soundness
2
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Paper summary

Paper Summary

This paper proposes TDSD, a time-aware subgroup discovery framework that formalizes the discovery object as a triple (S, W, ΔS(t)):

  • S: an interpretable covariate-defined subgroup (who);
  • W: a soft temporal window (when);
  • ΔS(t): a subgroup-specific treatment–control discrepancy trajectory (how).

Method. TDSD enables differentiable subgroup generation via sigmoid soft predicates, learnable feature-selection gates, and a normalized logarithmic conjunction. It makes window boundaries optimizable through a soft temporal membership function, and uses weighted trajectory estimation so gradients from the temporal discrepancy propagate back to subgroup parameters, allowing joint optimization of subgroup and window. It further introduces a window quality measure based on |ΔS(t)| and a trajectory-behavior measure based on L2 magnitude, to characterize when exceptionalness is concentrated and how it evolves.

Validation. The paper reports:

  • synthetic experiments separately testing subgroup recovery, temporal-window recovery, and recovery of five temporal behaviors;
  • an ablation comparing Static, Global Temporal, Window, Behavioral, and TDSD variants, where TDSD performs best on temporal IoU, trajectory correlation, and subgroup F1;
  • a MIMIC-IV experiment discovering a broad lactate ≥ 2.10 subgroup, while baselines return a much narrower rule.

The authors explicitly note these are different populations and not a common causal estimand, and that the clinical analysis is observational pattern discovery only.

Critical strengths
  1. A clean and useful formalization of time-aware subgroup discovery. The paper reframes the problem as discovering a structured object (S, W, ΔS(t)) rather than maximizing a scalar score. This makes the "who, when, how" decomposition explicit and forces the method to answer all three questions jointly. This is consequential because it gives the community a precise vocabulary and target for temporal subgroup discovery, and it is the contribution most likely to outlast the specific implementation.

  2. A genuinely coupled differentiable optimization of subgroup and window. The gradient path from temporal discrepancy through subgroup membership to thresholds, directions, and feature gates—and simultaneously through the soft temporal membership to window boundaries—means the window is learned from the discrepancy induced by the current subgroup rather than selected after the fact. This is consequential because it turns temporal localization into part of the discovery objective, which is the paper's central methodological claim and the main reason the ablation shows gains over static and globally temporal variants.

Critical weaknesses
  1. Narrow related work and no external temporal baselines. The paper positions itself only within subgroup discovery, exceptional model mining, and differentiable rule learning, and does not discuss or rule out time-series clustering, change-point detection/segmentation, shapelet/motif mining, or longitudinal subgroup discovery. The ablation compares only variants of the authors' own objective (Static, Global Temporal, Window, Behavioral, TDSD). This is consequential because the central claim—joint subgroup and temporal-window learning—is never evaluated against existing temporal discovery paradigms, so the paper does not establish that its soft-window formulation is necessary or preferable to simpler segmentation-plus-subgroup approaches.

  2. The real-data experiment does not support a "discovery" claim. On MIMIC-IV, TDSD returns a broad single-variable rule (lactate ≥ 2.10, 6,753 records), while baselines return a much narrower rule covering 53 records with a far larger raw discrepancy. The authors correctly note these are different populations and not a common causal estimand, but this means the clinical experiment only shows that different objectives yield different outputs—not that TDSD finds a better or more actionable subgroup. Combined with the modest hard-rule recovery in synthetic Experiment 1 (F1 0.447, recall 0.318), the empirical evidence does not convincingly demonstrate the practical value of the proposed discovery framework.

Questions for authors
  1. External temporal baselines (clarification). The ablation compares only internal variants of your own objective. Could you report results against at least one external temporal discovery approach—for example, a change-point/segmentation method followed by subgroup search, or a shapelet/motif-based baseline—on the synthetic window-recovery and behavior-recovery tasks? If not, could you explain why such a comparison is not meaningful? This materially affects my assessment of whether the soft-window formulation is necessary rather than merely convenient.

  2. Comparative evaluation in MIMIC-IV (clarification). TDSD and the baselines select different populations, so the reported discrepancies are not a common estimand. Is there a comparison—e.g., held-out temporal fit, calibration, or a pre-specified evaluation criterion applied to both discovered subgroups—that could indicate which discovery is more useful, rather than only that they differ? This affects whether I can read the clinical experiment as evidence for the method.

  3. Soft-to-hard extraction (clarification). Synthetic Experiment 1 shows F1 0.447 and recall 0.318 after thresholding, and the paper notes that thresholding can change support and alter the trajectory. Have you tried a more principled extraction procedure (e.g., optimizing a hard-rule surrogate, or reporting the soft-subgroup trajectory alongside the hard rule)? This affects how I weigh the gap between the continuous objective and the symbolic output.

  4. Disconnected exceptional periods (clarification). The current parameterization uses a single soft window. How much would the main conclusions change under a multi-window extension, and do any of the synthetic or MIMIC-IV patterns exhibit disconnected exceptional periods that the current method would misrepresent? This affects the scope of the "when" claim.

  5. Treatment-time alignment and confounding (clarification for the clinical claim). The paper correctly frames MIMIC-IV as observational. Could you clarify how treatment timing is aligned to the 0–24h MAP trajectory, and whether any adjustment for time-varying confounding or immortal-time bias was attempted? This affects how much weight I place on the clinical experiment as motivation.

  6. Relation to temporal segmentation/clustering (suggestion for framing, not a required experiment). For future work, a discussion of when joint soft-window learning is preferable to segment-then-discover pipelines would help readers situate the contribution. I note this as a framing suggestion rather than a request for additional experiments.

4 comments

We thank the reviewer for recognizing the value of the who–when–how formulation and the coupled optimization of subgroup and temporal boundaries. We agree that the original experiments do not sufficiently establish the practical benefit of joint discovery over discrete alternatives. In response, we have conducted additional outcome-driven synthetic experiments with 20 independent paired seeds and two discrete search baselines.

Critical Weaknesses

W1. Narrow related work and lack of external temporal baselines

We agree. The original Table 2 is an internal objective ablation, not a comparison against established temporal discovery methods. We have added two independently implemented discrete search strategies: Beam-Exact, which performs beam search over interpretable conjunctions and exhaustively scans admissible temporal intervals for each candidate subgroup, and Static-then-Scan, which first selects a subgroup using its signed-average discrepancy magnitude and subsequently scans its trajectory. Both use coverage weighting, a minimum three-point window, and the same minimum per-arm support requirement for hard rules as the revised TDSD. These directly test whether coupling subgroup selection and localization is useful relative to a discrete joint search or a sequential pipeline. The results are reported in Q1 below.

We will also expand the related work to discuss change-point detection, time-series clustering, shapelet/motif discovery, and longitudinal subgroup identification (including Wei et al., 2020). These paradigms are relevant comparators, although they typically target temporal segmentation, trajectory similarity, recurring patterns, or longitudinal heterogeneity rather than the specific treatment–control discrepancy over a covariate-defined rule. We will clarify this distinction without claiming that these approaches cannot be adapted to our problem.

W2. Limited evidence of practical discovery value

We agree that the MIMIC-IV experiment does not establish that the discovered lactate rule is clinically preferable or actionable. The TDSD and baseline rules cover different populations; larger discrepancy alone is not evidence of greater usefulness, and larger support alone is not evidence of a better discovery. We will narrow the clinical claim to exploratory pattern generation and use independent validation as described in Q2.

Regarding synthetic recovery, we clarify that the original Experiment 1 used ground-truth membership labels in its BCE objective. Its F1 of 0.447 is therefore a supervised representation-recovery result, not a valid unsupervised discovery benchmark. Our new experiments instead train using only covariates, treatment, and observed outcomes, using planted labels exclusively for evaluation. Coverage-aware TDSD achieves mean held-out hard-rule F1 of 0.698 in the standard benchmark and 0.699 in the larger benchmark, compared with 0.601 and 0.516 for the corresponding coverage-free variant. This supports the revised method's ability to recover useful rules.

Questions for Authors

Q1. External temporal baselines

We agree that such comparisons are meaningful. We have completed the following outcome-driven comparison using 20 independent data seeds per temporal pattern, independent training/test realizations, and five patterns. The table reports held-out transient-window IoU, mean hard-rule F1 and trajectory metrics across the five patterns, and mean runtime per run.

MethodTransient IoU ↑F1 ↑Corr. ↑RMSE ↓Runtime (s) ↓
Beam-Exact0.3150.7280.9870.5280.506
Static-then-Scan0.3200.5900.8850.7450.506
Behavior objective0.3200.7450.9870.4111.606
TDSD, no coverage0.8750.6010.9810.4621.634
TDSD, coverage-aware0.7750.6980.9860.3221.657

The revised objective weights temporal quality by the square root of subgroup coverage and adds support/effective-sample-size penalties and a minimum window duration. Hard rules are selected on training data and evaluated on independent test data. On transient patterns, the paired IoU improvement of coverage-aware TDSD over Beam-Exact is 0.460 (95% CI [0.399, 0.522]) and over Static-then-Scan is 0.455 ([0.392, 0.519]). The corresponding paired F1 and correlation intervals include zero. These confidence intervals are unadjusted. Across the five patterns, the hard-rule failure rates are 2% for coverage-aware TDSD and 0% for both discrete baselines; correlation and RMSE are calculated on feasible runs only. In the larger benchmark, coverage-aware TDSD achieves transient IoU 0.742 versus 0.102 for both discrete baselines, and takes 4.12 s per run versus 17.84 s for Beam-Exact.

An important qualification is that exact scanning of mean absolute discrepancy can favor short peak intervals, whereas the soft relaxation and hard-rule extraction introduce different optimization biases. We therefore interpret the IoU improvement as evidence for the complete search procedure, not proof that soft windows are intrinsically necessary. Furthermore, the benchmark's reference interval is meaningful as a planted episode only for the transient pattern; we do not interpret IoU for monotonic or oscillatory patterns as true episode recovery.

Q2. Comparative evaluation in MIMIC-IV

We propose a common, pre-specified held-out evaluation criterion applicable to every discovered hard rule and window. We would discover the rules on patient-disjoint training data, freeze the rules and intervals, and estimate their signed discrepancy trajectories on independent validation data. For each rule, we would report coverage, treatment/control effective sample sizes, trajectory reproducibility (RMSE between discovery and validation estimates), and the same coverage-weighted validation quality:

Qval(S,W)=cval(S)1/2 1∣W∣∑t∈W∣Δ^S,val(t)∣.Q_{\mathrm{val}}(S,W)=c_{\mathrm{val}}(S)^{1/2}\,\frac{1}{|W|}\sum_{t\in W}|\widehat\Delta_{S,\mathrm{val}}(t)|.

Patient-level bootstrap intervals on the independent validation sample would quantify uncertainty. This criterion compares the utility of discovered patterns under a common objective; it does not turn their contrasts into a common causal estimand or establish clinical benefit. We will also report a support–magnitude trade-off so that conclusions do not depend solely on one coverage exponent.

The original clinical figures (Figs. 5b and 6) and numerical summaries require an additional audit: the plotting code uses stored optimization trajectories, while the tabulated metrics re-evaluate extracted hard rules. Absolute discrepancy explains why reported magnitudes can be positive despite negative trajectories, but does not explain the large magnitude mismatch. We will regenerate both from a single verified hard-rule mask and withdraw the existing post-selection p-value.

Q3. Soft-to-hard extraction

Yes. The new benchmark implements a more principled, outcome-driven extraction procedure. Instead of using a single fixed gate threshold, it periodically ranks features by their learned gates and evaluates the top-k hard conjunctions (k = 1, 2, 3) using their learned thresholds and directions. It discards rules with inadequate per-arm support and selects the feasible rule/window checkpoint maximizing the training quality. No planted labels or test outcomes are used for this selection.

This directly addresses the gap between continuous optimization and symbolic discovery. As reported above, the revised method obtains mean hard F1 of 0.698/0.699 across the two benchmarks, but the remaining failure rates and stronger beam-search F1 demonstrate that exact rule extraction is still challenging. These gains cannot be attributed to extraction alone because the coverage-aware objective and training protocol were also revised. We will report both soft and hard discrepancy trajectories, their support, and their discrepancy in quality on the same independent data.

Q4. Disconnected exceptional periods

We agree that one interval cannot represent several disjoint episodes. The oscillatory pattern in Fig. 3(b) is a clear synthetic example: the absolute discrepancy has several separated peaks, while the full signed trajectory records changes in direction. The single-window IoU in Fig. 4(c) should not be interpreted as recovery of all oscillatory episodes. In MIMIC-IV, the plotted TDSD curve also has several extrema, but the figure inconsistency and lack of validated episode boundaries prevent us from claiming disconnected clinical effects.

A natural extension is to define K soft windows and their differentiable union,

wunion(t)=1−∏k=1K[1−wk(t)],w_{\mathrm{union}}(t)=1-\prod_{k=1}^{K}[1-w_k(t)],

and substitute this into the coverage-aware temporal objective, with constraints on window duration/separation and a penalty on the number of active intervals. The full trajectory remains available for distinguishing sign changes. This preserves the who–when–how formulation while extending the scope of when to multiple episodes. A union-IoU evaluation against truly disconnected planted windows would be appropriate.

Q5. Treatment-time alignment and confounding

The available cohort-extraction SQL uses a common landmark six hours after ICU admission for both groups, followed by 25 hourly MAP measurements over the subsequent 0–24 hours. The exposed group comprises patients initiating norepinephrine/noradrenaline by the landmark; controls have no recorded initiation during their ICU stay, and later initiators are excluded. The cohort retains the first adult ICU stay per patient with at least 30 hours of ICU stay. Thus, time zero is a common ICU landmark, not the actual moment of treatment initiation, and the counts refer to patients with one selected stay each.

The analysis code estimates baseline logistic propensity scores and uses clipped, stabilized inverse-probability weights. This is an attempt to adjust for measured covariates, not time-varying confounding. The original extraction also allows some laboratory measurements after the landmark, and the 24-hour SOFA feature may use post-exposure information. Conditioning on sufficient follow-up and excluding later initiators using future information introduces selection concerns; the landmark alone does not eliminate immortal-time or other time-related biases. Consequently, the present analysis cannot identify a causal response to norepinephrine initiation.

For revision, we will clarify the actual time axis in the figures, audit pre-landmark measurements and missingness, and avoid causal language. A stronger causal study would define eligibility and treatment strategies at a common time zero, handle subsequent initiation and censoring explicitly, and use appropriate longitudinal adjustment (e.g., marginal structural models) when time-varying confounding is present.

Q6. Relation to temporal segmentation and clustering

Thank you for this suggestion. We agree that segment-then-discover is preferable when temporal boundaries are shared across populations, when a fixed subgroup has an inexpensive exact scan, or when the scientific question concerns a global change point. Clustering and motif discovery are useful for identifying recurrent trajectory shapes, particularly when covariate-defined logical descriptions are not required.

Joint subgroup/window optimization is motivated by subgroup-dependent timing: a discrepancy localized in a small population may disappear in a global trajectory, so a globally selected segment can exclude the relevant episode before subgroup search begins. TDSD allows the candidate subgroup to influence the temporal localization and vice versa. The new comparison with Static-then-Scan provides evidence for this coupling on the transient synthetic setting, while Beam-Exact shows that coupling does not require a differentiable window. We will explain these complementary use cases and frame TDSD as one useful search strategy rather than a replacement for temporal segmentation or clustering.

Closing

We appreciate the reviewer's constructive suggestions. The new outcome-driven, multi-seed comparisons provide stronger evidence for the localization capabilities of TDSD while exposing remaining trade-offs in rule recovery and support. We will revise the manuscript to report these results transparently, broaden the related work, and restrict the clinical and multi-window claims to what is supported by the current evidence.

Reviewer_RULfOpenReview ↗

raise score

Thank you for the detailed response. W1 is substantially resolved by the two independently implemented discrete baselines; the paired transient IoU gain of 0.460 (95% CI [0.399, 0.522]) convincingly supports the coupled search procedure, though Beam-Exact's higher hard-rule F1 (0.728/0.745 vs 0.698) narrows the case for the differentiable window, and the revised "one useful search strategy" positioning is appropriate. Q3 is resolved via the outcome-driven top-k extraction and the clarification that the original Experiment 1 was supervised representation recovery. W2 is partially addressed: the claim is properly narrowed to exploratory pattern generation, a pre-specified held-out criterion is proposed, and the authors commendably disclose the figure/metric inconsistency and withdraw the post-selection p-value, though the clinical validation remains a commitment I will check in revision. Q4 is honestly scoped rather than solved, and Q5 is resolved through transparent disclosure of the landmark time axis and baseline-only IPW. With the two most load-bearing concerns addressed and the remaining reservations non-blocking, I raise my rating from 2 to 3 (weak accept).

Reviewer_j5yLOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

The proposed method, TDSD, addresses longitudinal subgroup discovery as a unified problem consisting of interpretable identification, temporal localization of discrepancy and characterisation of its evolution (termed as who-when-how problem). The proposed solution consists of soft predicate representation, feature selection gates, differentiable logical conjunction, temporal quality measure, and joint optimisation of two objectives with Adam for window and behaviour qualities. The experimental analysis focuses on 4 synthetic setup ablations (synthetic subgroup, window, trajectory recovery, and quality measure ablation) and 1 experiment on real world data (MIMIC-IV ICU treatment response discovery) with vasopressors as treatment and MAP as outcome.

Critical strengths
  • The problem motivation and the who, when, how formulation are meaningful and advances the conventional subgroup discovery problem. The extension of scalar score to reporting a tuple of (S,W,ΔS(t))(S, W, \Delta_S(t)) is interesting for clinical and longitudinal data.
  • The explanation of the differentiability of the method and the gradient flow from Δ(t)\Delta(t) back to the rule parameters is clear and easy to follow.
  • The evaluation analyses three failure modes of wrong individuals, wrong period, and wrong shape, which is useful distinctly using a separate metric for each.
Critical weaknesses

Methodology:

  • The coverage term is missing in the definition of the quality measure (QTDSDQ_{TDSD}) which makes it favour small subgroups. This is seen in Fig 2 (bottom), subgroup support decays to zero within about 100 epochs, while the temporal quality rises in the same time. Experiment 2 then further reports hard F1 or Jaccard to be 0. Standard subgroup discovery qualities generally weight the effect due to coverage (WRAcc or na⋅Δn^a \cdot \Delta).
  • The differentiability of the method is not yet convincing. 435 windows with T≤30T \leq 30, can be enumerated exactly. Furthermore, beam search is cheap with 6-10 covariates. A test on scaling regime would help justify gradient based search.

Experiments:

  • The experiments are not rigorous. Specifically, the variance is not reported as most of synthetic results appear to be from a single run.
  • The F1 and correlation gains in table 2 may not be statistically significant. Hence, further evaluation across seeds is needed to determine statistical significance.
  • No baselines reported in Exp 1-3 and only variants of the proposed objective are used as baselines in Exp 4. In the abstract, authors state “improves over increasingly time-aware alternatives”, which are mostly ablations and not compared to any existing works, hence, the claim needs further evidence. Some examples of relevant baselines are, Xu et al. 2024 (could be run on window-averaged outcomes), SD/EMM (e.g. pysubgroup) with a time-aware quality and an exhaustive window scan, causal trees (Athey & Imbens, 2016) on per-time or window averaged effects, longitudinal subgroup identification (Wei et al, 2020), a two stage baseline: static SD followed by an exhaustive window search (it directly tests whether joint optimisation benefits in any way). Inconsistency in results. Sec 4.6 reports TDSD discrepancies of 0.947 (overall) and 0.576 (window), but Figs. 5b and 6 show roughly −25 to −35 mmHg. The baselines’ +16.0 is positive, while their curve in Fig. 6 is negative.
  • The p-value of 0.0459 reported in Section 4.6 seems invalid. It is only legitimate if the permutation would rerun the entire discovery because the rule and window are selected on the same data.
  • The real world data evaluation is limited. It can be further extended to a semi-synthetic setup by keeping real MIMIC-iV or eICU covariates along with their time grid and plant S∗S^* and τ(t)\tau(t) to measure recovery under realistic correlation and missingness.
  • Better validation of results: The authors can either temporally split data or discover on MIMIC-IV and validate the rule and window on eICU.

Writing:

  • Inconsistent citation style: parenthetical citations use \citet throughout.
  • Irrelevant citations: Several citations don’t support their claims. COVID mental health (Daly et al., 2022), Video Captioning (Wu et al., 2018) and pedestrian trajectories (She et al., 2022) are cited for longitudinal discovery whereas network fairness (Du et al., 2020) is cited for precision medicine.

Overall, the paper is carefully written and the who-when-how problem formulation is interesting. Certain experiment results and observations make them less convincing. Specifically, the support collapse, shrinking window and hard F1=0 in Exp 2. No comparison with existing SD or heterogeneous-effect methods and the results on real data are inconsistent/invalid.

References:

  • Xu, S., Walter, N. P., Kalofolias, J., & Vreeken, J. (2024). Learning exceptional subgroups by end-to-end maximizing KL-divergence. In ICML 2024, PMLR 235, 55267–55285.
  • Wei, Y., Liu, L., Su, X., Zhao, L., & Jiang, H. (2020). Precision medicine: Subgroup identification in longitudinal trajectories. Statistical Methods in Medical Research, 29(9), 2603–2616.
  • Athey, S., & Imbens, G. (2016). Recursive partitioning for heterogeneous causal effects. Proceedings of the National Academy of Sciences, 113(27), 7353–7360.
Questions for authors
  • In the joint optimisation, the authors are actually optimising the window and behaviour quality objectives separately. Could the authors clarify which subgroup is reported when these two objectives disagree? The behaviour objective only returns Δ^(t)\hat{\Delta}(t), it does not identify or classify behaviours.
  • Could the authors clarify what the index time refers to for controls, whether ‘records' refers to patients or stays, how vasopressor exposure is defined or how missing MAP values are handled?
  • Fig 1b plots binary cross entropy (BCE) but BCE does not seem to be part of the method. Were ground truth membership labels used in Exp 1 training?
2 comments

Thank you for recognizing the relevance of the who–when–how formulation and for identifying important methodological and empirical limitations. We address each concern below.

Methodology

W1. Coverage, support collapse and shrinking windows. We agree. Eq. (2) measures discrepancy magnitude without rewarding coverage. Although Sec. 3.8 discusses support constraints, the Experiment 2 implementation only uses a weak penalty, 0.2(Sˉ−0.15)20.2(\bar S-0.15)^2, which does not enforce feasibility. We propose the coverage-weighted objective

Qcov(S,W)=c(S)γ∑twW(t)∣ΔS(t)∣∑twW(t)+ϵ,c(S)=N−1∑iS(Xi).Q_{\mathrm{cov}}(S,W)=c(S)^\gamma\frac{\sum_t w_W(t)|\Delta_S(t)|}{\sum_t w_W(t)+\epsilon},\qquad c(S)=N^{-1}\sum_i S(X_i).

We will enforce minimum support separately in both treatment arms, monitor effective sample sizes, and require a minimum window duration. We will also remove the shrinking-window penalty in the primary comparison and test coverage exponents and minimum durations in sensitivity analyses. Coverage weighting alone cannot prevent window collapse: a mean absolute discrepancy is maximized by a peak when singleton windows are allowed. We will therefore distinguish peak localization from recovery of an entire exceptional episode and test a duration-weighted alternative. Hard conjunctions will be evaluated directly on independent data; infeasible rules will be counted as failures rather than silently discarded. We will revise the claim about Experiment 2 accordingly.

W2. Differentiability and scalability. We agree that differentiability is not itself evidence of computational superiority. With 30 time points, there are 435 intervals containing at least two points (465 including singletons). For a fixed subgroup, prefix sums make exact window scanning inexpensive. The potential benefit of TDSD concerns joint search over feature selection, thresholds, directions and windows. We will compare gradient search with beam search plus exact window scanning and a two-stage static search, varying dimensionality, temporal resolution and rule depth. We will report wall-clock time, candidate evaluations, recovery and held-out quality under matched constraints. We do not claim that gradient search is necessarily faster at the current scale.

Experiments

W3. Variance and statistical significance. We agree. Experiments 1–3 use fixed seeds. Experiment 4 uses five optimization restarts on a fixed training/test realization for each pattern, not five independent dataset replications. We will repeat all methods on at least 20 paired independent data seeds, report mean, standard deviation and paired confidence intervals, and adjust confirmatory comparisons for multiplicity. The small F1 and correlation gains in Table 2 (0.442 versus 0.435 and 0.865 versus 0.835) are descriptive, not established statistically significant improvements. We will also report failure rates and hard-rule support.

W4. External baselines. We agree that Table 2 is primarily an ablation. We will add a coverage-aware beam SD/EMM search with exhaustive temporal scanning, static SD followed by exact window search, and a treatment-interaction tree baseline. We will additionally evaluate adaptations of Xu et al. (2024), Athey and Imbens (2016), and Wei et al. (2020), distinguishing adaptations from faithful implementations. All methods will use the same data splits, admissible rule sizes, support constraints and temporal evaluation.

W5. MIMIC-IV numerical inconsistency. Thank you for identifying this. The original evaluation code computes overall magnitude as the mean absolute discrepancy, so the positive 16.003 is not a signed treatment effect. However, this distinction cannot explain the large mismatch between the TDSD curve and the reported 0.947/0.576. The code generates the numerical summary by re-evaluating the extracted hard rule, whereas plotting uses the stored optimization-result trajectory. We will regenerate both from a single verified hard-rule mask, aligned patient ordering, weighting scheme and time grid, and report signed and absolute summaries separately.

W6. Post-selection inference. We agree. The current permutation test fixes the discovered subgroup, permutes treatment within it and retains the original IPW weights; it neither repeats discovery nor accounts for observational treatment assignment. Thus, 0.0459 is not a valid confirmatory post-selection p-value. We will remove it and the corresponding significance claim. Our primary validation will freeze the rule and window on discovery data and estimate the contrast with patient-level uncertainty on independent validation data. For randomized synthetic data, we will also rerun the complete discovery pipeline for every permutation. Unrestricted treatment permutation is not justified for observational MIMIC-IV; any conditional randomization procedure requires an appropriate assignment model and assumptions.

W7. Semi-synthetic and external validation. We agree. We will retain real MIMIC-IV covariates, time grids and observation masks while generating randomized treatment and planting known subgroup-specific trajectories. This will test recovery under realistic covariate dependence and missingness. For clinical validation, we will use a patient-disjoint holdout, preferably a temporal split based on valid calendar-era information, and evaluate the frozen rule/window without rediscovery. eICU validation is a valuable extension subject to access and harmonization of MAP, treatment and covariates.

Questions for Authors

Q1. Which subgroup is reported when the objectives disagree? Sec. 3.8 defines two separate optimization modes. Window discovery jointly optimizes subgroup and window and returns (S^W,W^,Δ^SW)(\hat S_W,\hat W,\hat\Delta_{S_W}). Behavior discovery optimizes a different subgroup and returns (S^B,Δ^SB)(\hat S_B,\hat\Delta_{S_B}). These subgroups need not coincide. We will explicitly label the mode used in each experiment. The RMS behavior objective measures magnitude, not behavior class; the retained trajectory permits descriptive characterization, but the current method does not automatically classify transient, delayed or oscillatory patterns.

Q2. Clinical index time, records, exposure and missing MAP. The available extraction SQL defines a common landmark six hours after ICU admission for both arms, retaining the first adult ICU stay per patient with at least 30 hours of ICU stay. Exposure is early norepinephrine/noradrenaline initiation by that landmark; controls have no recorded initiation during the stay, and later initiators are excluded. This is not alignment to actual treatment initiation. The analysis groups by subject ID, so the reported counts represent patients with one selected stay each, not hourly rows. The SQL selects the nearest valid MAP within half an hour of each hourly grid point; the analysis interpolates within observed ranges, excludes trajectories with fewer than two distinct measurements, and fills remaining missing values with time-specific medians. We will verify the final extraction against these scripts and report missingness and exclusions. Importantly, the available SQL allows some laboratory values after the landmark, and the result file uses sofa_24hours; we will audit measurement timing and restrict baseline variables to information available before the landmark (before exposure if making causal claims).

Q3. BCE and ground-truth labels in Experiment 1. Yes. The original Experiment 1 code explicitly trains with BCE against the planted membership labels. This is a supervised representation-recovery sanity check, this experiment intentionally uses supervised subgroup recovery because we want to verify that the differentiable rule-learning component itself works correctly..

Closing

We appreciate these constructive suggestions. Our intended contribution is interpretable joint population and temporal localization, with a complementary trajectory-discovery mode. We will narrow the current claims and prioritize feasible hard-rule recovery, independent repeated experiments, external baselines and valid clinical validation.

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

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