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My primary concern is that the proposed framework combines several established statistical and machine-learning techniques without introducing a clearly identifiable new methodological contribution. The main components include transformer-based concept extraction, pooled logistic hazard models, VARX, negative-control calibration, multiple-testing corrections, and rule-based graph construction. Although their integration is meaningful from an application perspective, the manuscript does not convincingly establish what constitutes the fundamental methodological innovation. In summary, it remains unclear what new learning or inference principle is introduced beyond applying existing statistical safeguards to clinical KG construction.
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Several central components rely on linear or additive models, including VARX-based estimation of intervention responses and linear regression for beat-level physiological couplings. These assumptions appear restrictive given that physiological responses to clinical interventions are often nonlinear, state-dependent, and characterized by complex temporal dynamics. Drug concentration–effect relationships, in particular, may exhibit nonlinear dose responses, saturation effects, delayed responses, and substantial interactions with the patient's physiological state. While linear models may offer interpretability and computational advantages, the paper does not sufficiently justify why they are appropriate for the investigated relationships. More importantly, it remains unclear whether the reported robustness is a property of the proposed framework or partly a consequence of its restrictive modeling assumptions.
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The proposed framework contains numerous fixed thresholds and heuristic decisions, including physiological concept definitions, persistence tiers, minimum sample-size requirements, sign-consistency criteria, significance thresholds, lag windows, and graph-edge admission rules. Some thresholds are clinically motivated and reasonable. However, several algorithmic choices appear insufficiently justified. For example, why is a sign-consistency criterion of 75% considered appropriate? Why are five contributing cases sufficient for admitting a relationship? How sensitive are the resulting graphs to these and other design choices?
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The reported reduction in false relation instances is striking. For example, Table 2 reports approximately 0.06 false concept-level relations per graph for the proposed method, compared with approximately 12.4 for the correlational KG baseline under the transplant null. However, the comparison involves fundamentally different estimation procedures. The proposed approach pools information across patients, restricts candidate relations, applies negative-control calibration, and uses conservative population-level admission criteria before instantiating relations in individual graphs. In contrast, the correlational baseline estimates temporal relationships primarily at the individual-patient level. Consequently, the reported improvement may reflect differences in pooling, candidate selection, statistical power, multiple-testing procedures, and graph sparsity rather than an intrinsic advantage of the proposed graph-construction methodology. A more convincing evaluation would compare the methods under matched conditions, including identical candidate relation sets, comparable pooling strategies, equivalent calibration procedures, and controlled graph density. Without such comparisons, I find the magnitude of the reported improvement difficult to interpret.
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The experiments demonstrate that certain estimators identify relationships under artificially constructed null conditions. However, successfully avoiding false discoveries under negative controls is not equivalent to correctly identifying genuine physiological relationships. In particular, replacing intervention trajectories with those of other patients or redistributing intervention times changes aspects of the underlying temporal and treatment distributions. These procedures do not necessarily reproduce all relevant characteristics of the null hypothesis in a closed-loop physiological system. The random-time experiments also reveal important limitations: several estimators continue to admit false relations despite negative-control calibration. Furthermore, the concept-level experiments report false population-level admissions in a non-negligible proportion of null replicates, even though the average number of false relation instances per patient graph is small. A central missing component is a systematic evaluation using simulated closed-loop physiological systems with known ground-truth relationships. Such experiments should investigate varying feedback strengths, degrees of unobserved confounding, nonlinear response functions, sampling frequencies, and intervention policies. Crucially, the evaluation should consider both false-positive control and the ability to recover true relationships. Otherwise, highly conservative procedures may appear robust simply because they reject most candidate edges.
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Although the paper emphasizes patient knowledge graphs, most slow relations are estimated at the population level and subsequently instantiated within individual patients based on the occurrence of corresponding events. However, observing two temporally related events in an individual patient does not establish that the underlying population-level relationship is valid for that specific patient. The evidence pointers improve traceability but do not, by themselves, validate the physiological or causal interpretation of individual graph edges. This concern is reinforced by the authors' finding that none of the 11 slow intervention-response relationships demonstrates reliable patient-specific predictive improvement in the split-half experiments. Therefore, the resulting graphs appear to represent patient-specific observations annotated with population-level relationships rather than independently learned patient-specific physiological dependencies.
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More importantly, the practical benefits of this representation remain unclear. The paper provides limited evidence that the proposed knowledge graphs improve downstream predictive performance or generalization compared with models directly using the underlying physiological time series and intervention histories. The authors also acknowledge that typed relations improve held-out concept-onset prediction over a history-only baseline in only one of three codings. A convincing demonstration of downstream utility, such as prediction of physiological deterioration, intervention-response forecasting, or improved robustness to distribution shifts, would substantially strengthen the contribution.
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The distinction between clinician policy and physiological response is central to the paper. However, the proposed statistical models do not resolve the causal identification challenges arising from time-varying confounding and partially observed clinical decision processes. Relevant drivers of intervention decisions, including surgical stimulation, unrecorded medication administration, and other clinical events, may not be captured in the available data. Negative-control calibration can help detect spurious associations but does not generally eliminate bias from unobserved confounding or identify causal intervention effects. This is particularly relevant because the concept-level response relations fail the authors' prespecified pharmacological sign checks.
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The principal feedback-related experiments are conducted using VitalDB, a single-center surgical dataset. Although MIMIC-IV waveform data provide additional evaluation, the corresponding experiments do not externally validate the central intervention-response findings because the necessary action records are unavailable. Consequently, it remains uncertain whether the reported results generalize to other hospitals, clinical intervention policies, or patient populations.
Replying Reviewer JH1c
Thank you for the careful review. Both of your points led to new analyses, which we summarize here and will add to the revised paper.
On W1 and your question (does the conclusion hold on the highest-confidence relations?)
You are right that a sign fixed by respiratory physics is much stronger evidence than one taken from documented clinical practice. We split the 29 relations into three tiers using the sign source the paper already lists for each relation: physics (5 relations), pharmacology and physiology (14), and documented practice (10). Nothing was re-run; the table re-counts the existing calibrated calls within each tier.
(RT: false admissions under the random-time null. Ranks use the reliability-first rule we declared in advance.)
The conclusion holds on the physics tier, which is where we would most like it to be judged. The matched and interrupted-trend designs admit 4 of the 5 physics relations, all with the physical sign and with no random-time false admissions, and they rank first under both of our ranking rules. Cross-correlation and Granger, by contrast, admit set rate → EtCO₂ with the sign of the clinician's policy and end up at ranks 9–12. Two estimators need a caveat. The sequential-trial contrast gets the signs right but has two random-time false admissions. VAR-LiNGAM gets all five signs right, yet calls every one of its physics estimates significant on every transplant null, so its error control is poor even though its signs are correct.
Pharmacology looks similar: the three design-based estimators take the top ranks. In the practice tier no estimator stands out, and two policies (P08, P10) come out with the opposite sign for almost every estimator that admits them, which makes us think the practice label is the problem there rather than the estimators. We agree with your reading, and the revision will describe the policy tier as agreement with documented practice, outside the reliability claim.
On W2 (the 0.06 vs. 12 comparison)
Thank you for pressing on this. Table 2 compared our full pipeline with a per-patient correlational graph built under different procedures, and the baseline used a single null replicate. We have replaced it with a ladder that starts from the per-patient baseline and adds our ingredients one at a time. Every row uses the same candidate relations, the same 38 null replicates and the same metric.
Read from top to bottom, the gap closes in identifiable steps. Per-patient rules have no way to abstain when the whole graph is null, so they always return edges. Pooling alone makes the transplant count worse, because with three million rows the pooled tests pick up the case-phase structure that transplanted series share. The negative-control rule removes most of what remains, and adjusting for case phase removes the transplant excess altogether. Between that last ladder row and our construction there is a further 2–3× on the shift null, and those intervals overlap. This makes the claim sharper than Table 2 could: the improvement comes from how relations are constructed and admitted, and those ingredients would help any pooled statistic; it does not come from a new estimator. The revised paper will say this and will no longer set 12.4 against 0.06.