Calibrated Timing of the NET Therapeutic Window

When a patient in septic shock tips from protective inflammation into destructive immunothrombosis, the clinical question is rarely whether but when — and the cost structure around that question is brutally asymmetric. Neutrophil extracellular traps (NETs) — web-like scaffolds of DNA and antimicrobial proteins that neutrophils release to snare microbes — are the pivot point. Early in infection they are an essential antimicrobial barrier; sustained, they weave platelets, tissue factor, and fibrin into microvascular clots that resist lysis and drive multi-organ failure (Yan et al.; Xin Gao et al.). A therapy that eradicates NETs too early strips the patient's antimicrobial defense and invites secondary infection; delivered too late, the thrombus is already irreversible (Yan et al.; Aklilu et al.). This is the "dual role" of NETs, and it defines a narrow therapeutic window whose timing must be predicted per patient.

Machine learning has an exactly matching unresolved problem. A risk model that outputs the population base rate is perfectly calibrated on average and clinically useless; a model that outputs tight, confident event times is sharp but, when wrong, catastrophically misleading. Post-hoc recalibration fixes the dishonesty by smearing predictions back toward the average, destroying the sharpness that made them actionable (Dheur & Ben Taieb; Feng & Tang). The two literatures have never been joined: no NET study evaluates calibration or sharpness (they report odds ratios and AUROC), and no calibration study has been tested on a decision problem where both error directions carry severe, physically distinct costs. This proposal builds that bridge.

Core Claim

I claim that forecasting the onset of thromboinflammatory decompensation — the moment a sepsis or ARDS patient crosses into NET-driven disseminated intravascular coagulation (DIC) — requires a model that is threshold-calibrated in time, not merely calibrated or sharp on average, and that the NET dual role supplies the exact cost structure under which this distinction becomes measurable and decisive. Concretely: clinicians act on rules of the form "start anticoagulation or NET-dissolving therapy if the predicted probability of decompensation within horizon $h$ exceeds threshold $k$." Sahoo et al. proved that average calibration leaves a reliability gap between the payoff a clinician expects from such a rule and the payoff they actually get, and that threshold calibration — calibration on every threshold-defined subgroup — is necessary and sufficient to close it. But their theory and experiments cover only static, binary predictions (hospital length-of-stay, wealth). Extending this to censored, time-to-event forecasts over hourly, non-i.i.d. patient trajectories is the open technical problem; the NET therapeutic window is the setting where solving it matters most, because both failure directions (treat too early, treat too late) are fatal.

Research Program

The decision problem. Let $S_\theta(t \mid x)$ be the model's predicted probability that a patient with hourly feature history $x$ has not yet decompensated by time $t$ (decompensation defined prospectively, e.g., by IST-style DIC scoring or a pre-specified vasopressor/coagulation composite). The clinical policy acts when predicted horizon-$h$ risk exceeds $k$. The payoff is

$$\mathcal{U} \;=\; -\, c_{\mathrm{late}}\,\pi_{\mathrm{FN}} \;-\; c_{\mathrm{early}}\,\pi_{\mathrm{FP}},$$

where $\pi_{\mathrm{FN}}$ and $\pi_{\mathrm{FP}}$ are the fractions of untreated decompensators and unnecessarily treated patients, $c_{\mathrm{late}}$ encodes irreversible microvascular thrombosis and organ necrosis, and $c_{\mathrm{early}}$ encodes loss of the antimicrobial NET barrier with secondary infection. The dual role of NETs is thus not decoration: it is the payoff matrix, and it is asymmetric in a way that operational benchmarks like length-of-stay are not. Because interventions in the ICU are graded (DNase dosing, anticoagulation intensity, apoptosis-promoting agents such as the CDK inhibitor AT7519 shown to reverse delayed neutrophil apoptosis in ARDS models (cb5b40225246676df17ca0e640445844)), I will evaluate a family of thresholds $(k, h)$ rather than a single cut.

The model and training objective. The forecaster is a recurrent network over the hourly MIMIC-Extract feature grid, parameterized as in Avati et al. to output a flexible time-to-event distribution (I will use their Survival-CRPS — a proper scoring rule that penalizes both miscalibration and dispersion under censoring — as the base loss, and their 120-year upper bound trick to prevent probability mass leaking into impossible times). On top of this I add an in-training threshold-calibration penalty: for each clinically fixed $(k, h)$ pair, an isotonic-regularized term that penalizes the empirical calibration error on the subgroup of patients whose predicted risk falls in a neighborhood of $k$. This borrows the subgroup construction of Sahoo et al. but moves it from a post-hoc binary wrapper into the survival objective, because Dheur & Ben Taieb showed that post-hoc fixes buy calibration by inflating interval width, and Marx et al. showed in-training calibration penalties preserve sharpness.

The biological features. MIMIC-III does not assay NET markers directly — a real limitation, since MPO-DNA and Cit-H3 are the mechanistically decisive biomarkers and are measurable as early as Day 1 of septic shock, ahead of organ-failure scores (Yan et al.). I will use the available pathway proxies from the MIMIC-Extract grid (Wang et al.): neutrophil and neutrophil-to-lymphocyte trajectories, platelet count dynamics (the platelet–neutrophil relay is the obligate NETosis trigger (Shuai Liu et al.)), lactate, D-dimer, fibrinogen, and SOFA components. The feature-block ablation (below) tests whether these dynamic thromboinflammatory features improve threshold-level calibration specifically, beyond what static demographics provide.

Theory component. I will work out what threshold calibration means when the outcome is censored and the features are time-varying. Sahoo et al.'s necessity/sufficiency proof assumes static predictions and no censoring; the censoring mechanism in ICU data is informative (discharge, withdrawal of care), which Chapfuwa et al. identified as a primary failure mode of their Survival Function Matching. The target is a finite-sample reliability-gap bound under censoring at fixed horizon $h$, with the censoring assumption stated explicitly and tested.

Proposed Experiments

The primary dataset is MIMIC-III, using the MIMIC-Extract pipeline (Wang et al.) to build hourly trajectories for a sepsis cohort; Avati et al. used the same database (51,000 admissions, 70.1% right-censoring) and Sahoo et al. used it for threshold-calibration experiments on length-of-stay, so cohort construction and evaluation precedent exist. The outcome is time from sepsis onset to DIC/decompensation composite; class imbalance is expected, so I will report AUPRC alongside everything else, noting that on this database even strong intervention models can show AUPRC below 0.50 despite AUROC of 0.90–0.94 (Wang et al.). There is no reported result found on Lacuna for calibrated DIC-onset forecasting on MIMIC-III, so this evaluation is new ground.

Metrics: calibration slope (ideal 1.0) at the global and at each threshold-defined subgroup level; sharpness as Mean Coefficient of Variation of the predicted event-time distribution (Avati et al.); reliability gap at each fixed $(k, h)$ (Sahoo et al.); and the dual-cost payoff $\mathcal{U}$ under several $(c_{\mathrm{late}}, c_{\mathrm{early}})$ ratios, following Feng & Tang's point that average-calibration metrics like ECE do not track decision utility — their sharpness-preserving objective is a binary-classification tool, and adapting its spirit to censored event times is part of the contribution. A censoring-robustness check reruns the sweep under administratively truncated follow-up to probe the failure mode Chapfuwa et al. documented on SEER's mass censoring at 80 months.

A small feasibility study grounds the biology: the acute ischemic stroke cohort of Xin Gao et al. (45 patients, 45 controls, MPO-DNA and H3Cit measured) is far too small for model training, but it can test whether adding NET-marker trajectories to a calibrated forecaster shifts threshold-level calibration in the predicted direction. I will be explicit that this arm is hypothesis-generating, not confirmatory.

Baselines

The naive reference point is an uncalibrated deep survival model trained with standard maximum-likelihood log-loss on the same hourly features, architecture, and tuning budget. This is the "do nothing" option, and the corpus predicts its failure precisely: under 70%+ censoring, log-loss training produces lazy, smeared distributions — on the STARR EHR database, Avati et al. report Mean Coefficient of Variation of 18.42 for MLE versus 0.301 for Survival-CRPS, with the MLE model spreading probability across implausible time horizons. No reported MIMIC-III DIC-onset number exists for this baseline, so the comparison numbers will be produced by this project under matched conditions.

The strongest competitor is Countdown Regression, the Survival-CRPS model of Avati et al., trained on identical features and given the same compute and hyperparameter search budget as my model. It is the strongest because it already solves the average calibration–sharpness problem on exactly this kind of data (calibration slopes near 1.0, CoV 0.301 on STARR) while leaving open precisely what I target: no decision thresholds, no censoring-aware subgroup guarantees, no biological dynamics. Chapfuwa et al.'s Survival Function Matching — which matches predicted survival curves to a differentiable Kaplan-Meier estimate — runs as the second strong baseline under the same budget, since it is the main alternative in-training calibration approach and reports near-ideal calibration slopes with low CoV across clinical cohorts (no exact numeric error is reported for their EHR cohort on Lacuna). A third baseline is post-hoc recalibration: the best Survival-CRPS model wrapped in Conformalized Quantile Regression, which Dheur & Ben Taieb linked theoretically to quantile recalibration. Beating the strongest baselines means: strictly smaller reliability gap at pre-registered $(k, h)$ thresholds, calibration slope within 0.05 of 1.0 at the subgroup level where baselines miss it, CoV no worse than Countdown Regression's, and higher realized dual-cost payoff $\mathcal{U}$ across at least three cost ratios. Two ablations isolate the ingredients: the full model with the thromboinflammatory feature block replaced by static demographics (isolating the biology), and the full model with the threshold-calibration penalty moved to post-hoc (isolating the training-time calibration).

Why not just…?

Why not just train a standard network with MLE or pinball loss? The corpus rules this out with numbers. Log-loss training under heavy censoring yields the lazy, high-variance behavior quantified above (CoV 18.42 vs 0.301, Avati et al.), and pinball loss falls into the calibration trap of aggressively narrowing intervals below their promised coverage (Chung et al.). In this proposal, that failure mode is not hypothetical: the reliability-gap evaluation at fixed thresholds is exactly the experiment that would expose it, and the MLE baseline is included so the failure is measured rather than asserted.

Why not just apply post-hoc recalibration to a strong model? This is the most credible alternative and I will treat it as such. Three independent results in the corpus show it falls short here: post-hoc methods achieve coverage by widening intervals (Dheur & Ben Taieb); temperature scaling demonstrably lowers downstream decision payoff (Feng & Tang); and post-hoc "distribution calibration" overfits the calibration split, yielding larger reliability gaps on test data than threshold calibration (Sahoo et al.). Still, the conformal-wrapped Countdown baseline is run at equal budget, and if it matches the in-training method on threshold reliability gap and retains CoV, that result would itself be publishable and would refute the proposal's core claim — the comparison is designed to settle it.

Why not just optimize AUROC or the C-index, since clinicians mainly need risk ranking? Ranking is insufficient when the decision is when and whether to intervene with a therapy that carries both-directional risk. Cox-style models rank well but produce unreliable absolute event times and poor calibration slopes (Chapfuwa et al.); and high AUROC can coexist with AUPRC below 0.50 under the class imbalance typical of ICU event onset, meaning most flagged patients are false alarms (Wang et al.). For a threshold policy, a ranker with no honest absolute probability cannot tell a clinician whether the patient above threshold $k$ has a 55% or a 95% chance of decompensating within 24 hours — and the treatment decision differs.

Why not just use classical biomarkers and severity scores? They arrive too late and carry no timing. NET-complex markers predict DIC and 28-day mortality independently as early as Day 1 of septic shock, ahead of organ-failure scores (Yan et al.); classical markers reflect damage already done. And a static score, however early, answers a different question from a calibrated survival forecast over the next 48 hours. The feature-block ablation directly tests how much the thromboinflammatory proxies add over demographics alone — if the gain is negligible, that will be reported as such, and the project's decision-theoretic contribution stands independently.

Decisive Checks

Three results decide the proposal. First, at matched budget, the threshold-calibrated survival model must show a smaller threshold-level reliability gap than Survival-CRPS, SFM, and their conformal-wrapped variants on pre-registered $(k, h)$ pairs, without worse CoV — this is the central empirical claim. Second, the ablation must show the thromboinflammatory feature block improves threshold-level calibration specifically (not just discrimination), tying the biology to the decision geometry. Third, the dual-cost payoff sweep must show the advantage holds across cost ratios rather than at one convenient point, because the clinical reality is that the early-cost/late-cost balance differs between patients and centers (Aklilu et al.). A final honest limitation: treatment changes the trajectory (the performative setting that Sahoo et al. explicitly exclude), so all payoff figures are observational-policy estimates; off-policy evaluation of the learned thresholds is the natural second phase.