Losing Coordination Between Organ Systems as a Sparse Early Warning of Collapse

When a patient deteriorates toward septic shock or cardiac arrest, the usual early-warning model watches the levels of vital signs and labs: heart rate going up, blood pressure going down. Network physics suggests a different thing to watch. In systems made of several subsystems that depend on one another, such as coupled power and communication grids, collapse is often abrupt. The system loses the mutual support between its parts, and then fails all at once once enough links are gone, rather than degrading gradually. This proposal asks whether the same holds at the bedside. The question is whether a handful of features that measure how well physiological subsystems still move together can predict deterioration as well as much larger models, stay informative when ICU treatment hides the levels, and give clinicians an explanation of the form "the link between circulation and breathing has broken."

The opportunity matters because clinical prediction faces three linked problems. Sparse models built from vital-sign levels work on general wards but fail in the ICU, where vasopressors and ventilators hold the numbers in range. Feature sets chosen in one hospital break in another. And post-hoc explanations of large sequence models are distrusted, sometimes rightly. A small set of coupling features, whose relationship to risk can be checked against a specific prediction from interdependent-network theory, could address all three at once. If it fails, we learn something concrete about where network-collapse analogies stop applying to physiology.

Core Claim

We claim that cross-subsystem coupling statistics are a distinct and parsimonious signal of deterioration. They are rolling measures of whether, for example, heart rate and respiratory rate, or blood pressure and heart rate, still co-vary the way they do in a stable patient. Five things should follow if the claim is true. First, at a matched feature budget, a sparse model allowed to use coupling features should match or beat one restricted to level and variability features. Second, the advantage should be largest exactly where level-based models are known to fail: in patients receiving active hemodynamic support. Third, the advantage should transfer better across hospitals. Fourth, if coupling features are only allowed to enter the model when they clearly earn their place, they should still be selected.

Fifth, and most specific to the network-collapse lens: the relationship between outcome hazard and the fraction of decoupled subsystem links should be threshold-like rather than proportional. Below a critical fraction, losing a link should barely change risk. Beyond it, risk should jump. This is the clinical analogue of the discontinuous collapse of the mutually connected part of a network.

The theory motivating this is the interdependent percolation result. Buldyrev et al. prove that once two or more networks depend on each other node-for-node, the surviving mutually connected component collapses discontinuously at a critical damage level, even when each network alone degrades smoothly. Later work strengthens and qualifies this. Zhang, Arenas and Yağan show in a load-redistribution model that terminal breakdown stays abrupt and that intermediate coupling can be protective. Dong shows that the sharpness of collapse grows with coupling strength. Studies of dynamic interdependence in multilayer networks find explosive transitions and a characteristic plateau before breakdown in coupled oscillator and epidemic dynamics.

All of this work lives on synthetic graphs or engineered grids. None of it tests whether human multi-organ failure has this shape. We do not claim the body is a percolating graph. We borrow one falsifiable prediction, threshold-like hazard in the number of broken inter-subsystem links, and one design principle: monitor dependencies, not just components.

Research Program

The first piece is a coupling-feature library. We group routinely charted variables into subsystems: circulatory (heart rate, mean and systolic pressure), respiratory (respiratory rate, oxygen saturation), thermoregulatory (temperature), and, where labs are available, metabolic and renal (pH, lactate, blood urea nitrogen, creatinine). For each pair of subsystems we compute, over a trailing window of $w$ hours, a coupling index $c_{ij}(t)$. This is the rank correlation of the first differences of representative channels $i$ and $j$, plus a lagged variant to capture delayed responses. The reference distribution of each $c_{ij}$ comes from patients who remain stable. A link counts as "decoupled" at time $t$ when $c_{ij}(t)$ falls outside the central 90% of that reference. The mutual-support score is

$$s(t) = 1 - \frac{1}{|E|}\sum_{(i,j)\in E} \mathbf{1}\left[c_{ij}(t)\ \text{decoupled}\right],$$

where $E$ is the set of monitored subsystem pairs and $\mathbf{1}[\cdot]$ is the indicator function. The value $s(t)$ is the fraction of inter-subsystem links that are still intact.

This construction extends the per-channel divergence monitoring of the Jensen–Shannon sepsis detector, which compares each patient's recent distribution of each variable to a recovering cohort and sums the results. That method is interpretable but by design ignores cross-variable structure, which is exactly what we measure. Our reference-cohort calibration reuses its idea.

The second piece is reluctant sparse selection. Following the reluctant additive model of Maronge, Huling and Chen, we start from a sparse linear model on level and variability features. We then let coupling features and a small number of smooth nonlinear terms enter only if they reduce held-out error after a heavier penalty. RAITR uses this idea, nonlinear terms "earning their way in," for static treatment rules on genomic data. We reuse its method, apply it to a different kind of candidate (dependency features rather than nonlinear transforms), and use it in a time-series risk setting. The reluctance doubles as a built-in test. If coupling carries nothing beyond levels, the procedure will not select it, and we will report that.

The final models are capped at a clinician-scale budget of $k \in \{5, 8, 12\}$ inputs. The cap of 12 mirrors the vitals-plus-demographics set of Ueno et al..

The third piece is a test of the collapse shape. Using $s(t)$ as a single covariate in a discrete-time hazard model, we compare three ways of letting hazard depend on $s$. One is proportional, linear in $1-s$. One is smooth and convex, a spline. One is a step at an estimated critical value $s_c$. We compare them by held-out likelihood and by a bootstrap test on the step size.

We also look for the pre-collapse plateau that network theory predicts: a period in which $s(t)$ sits near a critical value before a rapid drop. We do this with change-point fits on individual trajectories, using the same likelihood-ratio logic that quickest-detection methods for grid cascades apply to line-failure streams. That work restricts monitoring to the neighbors of components that have already failed. The analogue here is to watch links adjacent to subsystems that have already decoupled.

The fourth piece is the explanation itself. Because the model is sparse and additive, the explanation is the model. A risk score decomposes into named terms such as "circulatory–respiratory link broken for 3 hours" or "pH below threshold." There is no post-hoc approximation to distrust, which responds to the clinician skepticism documented by Upshaw et al.. PaX showed that standard LIME on sepsis sequence models credits demographics simply because they appear first in the input. We will use PaX on a deep comparator to check whether it independently rediscovers the same subsystem interactions that the sparse model selects.

The role of the cascading-failure literature should be stated plainly. Ghosh et al. fit linear causal graphs to grid outages and assume no hidden confounders. In the ICU, treatment is a massive hidden confounder, so we deliberately do not claim causal or interventional explanations. Our explanations are predictive and structural. The "escape time" idea of Yu et al. sets a constraint on evaluation rather than supplying a method: we report how many hours of warning each model gives, not only how well it ranks patients.

Baselines

The naive reference is a level-only sparse model: logistic regression with an L1 penalty (LASSO) on current values and trailing means of the same variable pool, capped at the same $k$. This is the honest "do nothing new" comparator. It embodies the redundancy argument of Ueno et al., who found that adding 34 labs to 12 vitals and demographics moved cardiac-arrest AUC only from 0.862 to 0.872. Note that this is on their Kameda cohort, which we do not reuse, so that number frames the question rather than serving as a target.

The strongest sparse competitor is the same LASSO given per-channel rolling variance and lag-one autocorrelation in addition to levels. These are the standard univariate signatures of approaching instability. Beating it shows that cross-channel structure adds something beyond within-channel instability. It gets the same windows, the same $k$, and the same nested cross-validation budget for its penalty.

The strongest unconstrained method is a temporal convolutional network on all 40 PhysioNet variables. Liao et al. report AUROC 0.924 for it on PhysioNet 2019, against 0.75 for their best non-deep model, a Random Forest. We will retrain it under our patient splits and prediction horizon, because their protocol may differ from ours. We also include a gradient-boosted tree model on all summary features. For the challenge's own metric, Reyna et al. report winning utility scores of 0.33–0.36, with a drop on the hidden hospital. We will report utility alongside AUROC.

We do not expect a 12-input model to match the network's in-distribution AUROC. Beating the baseline means one of three things. The sparse coupling model comes within 0.02 AUROC of the network in distribution. Or it loses less than the network does when trained on Hospital A and tested on Hospital B. Or it outperforms the network in the treated-patient stratum.

The key ablation removes the coupling features from our own pipeline while keeping reluctant selection, the nonlinear terms and the budget fixed. A second ablation replaces each coupling index with a version built after shuffling one channel in time within each patient. This keeps both channels' marginal behavior and destroys only their co-movement. If performance survives the shuffle, the gain was never about coupling.

Why not just…?

Why not just train a sequence model on raw vitals and let it learn the coupling? This is the real threat. A temporal network sees all channels jointly and can in principle learn any co-movement pattern. Its reported AUROC of 0.924 (Liao et al.) is high. We do not argue that it misses coupling. We argue that it hides it in a form clinicians cannot audit, and that its advantage may shrink across hospitals. Reyna et al. report a performance drop on the held-out hospital for challenge entries, and Zhang et al. show minimal feature sets shifting across populations. The cross-hospital and treated-stratum experiments settle this. If the network keeps its lead there too, our contribution narrows to interpretability at a known accuracy cost, and we will say so.

Why not just add pairwise interaction terms to a LASSO or gradient-boosted trees? Products of current levels capture "both abnormal at once," not "no longer moving together." A patient on pressors can have normal heart rate and pressure whose fluctuations have stopped tracking each other. Gradient-boosted trees given all channel summaries form a strong version of this alternative, and we run them. The shuffled-coupling ablation is the clean discriminator. Interaction models see identical inputs before and after shuffling, while our coupling features do not.

Why not just use per-channel early-warning statistics such as rising variance and autocorrelation? These are cheaper and well motivated by the general physics of tipping points. They are our strongest sparse baseline for exactly that reason. The marginal-divergence detector of the Jensen–Shannon study is the closest published relative, and it sums channels independently. If variance and autocorrelation match coupling features at equal $k$, the network-of-networks framing adds nothing operational, and the proposal fails its central test.

Why not just use SOFA-style bedside scores? They are parsimonious and transparent, but they score organ levels against fixed cut-offs. PaX found that 4 of the top 10 sepsis predictors lie outside SOFA. We include a SOFA-component logistic model as an additional reference point.

Proposed Experiments and Decisive Checks

The primary dataset is the PhysioNet/CinC 2019 sepsis challenge data: about 40,000 ICU stays from two public hospital systems, with hourly vitals and sparse labs. We train on one hospital and test on the other in both directions. Its hourly sampling makes coupling estimates noisy, so we use windows of 8–12 hours and report how estimate variance changes with window length.

Two further datasets address specific gaps. The minute-level vitals in MC-MED, used by Kim et al., let us check whether coupling signal sharpens with denser sampling, as it should if it is real. MIMIC-IV records vasopressor and ventilation exposure, which lets us stratify every comparison by active support. That stratification tests the ICU-masking failure described by Ueno et al., whose level-based model dropped to AUC around 0.58–0.64 in ICU patients. No reported result was found on Lacuna for a comparable deterioration benchmark on MIMIC-IV, so all MIMIC-IV numbers will be baselines we produce ourselves.

Metrics are AUROC, area under the precision–recall curve, challenge utility, median lead time before onset, and false alarms per patient-day. The last matters because rare-event models like Ueno's have a positive predictive value near 4%.

Four results are decisive. First, at $k=12$, coupling features must be selected by the reluctant procedure and must improve held-out precision–recall over the variance-and-autocorrelation LASSO on both hospital transfer directions. Second, the improvement must be larger in vasopressor-exposed patients than in unexposed ones. Third, the shuffled-coupling ablation must remove the gain. Fourth, the step hazard model in $s(t)$ must beat the proportional model by held-out likelihood with a bootstrap-stable $s_c$ that replicates across hospitals.

If the first three hold and the fourth fails, we have a useful sparse, interpretable model but no evidence for first-order collapse in physiology, and we will report it that way. If the first fails, coupling is redundant with levels at this sampling rate. That would extend Ueno's redundancy finding to a new feature family, which is itself a clear negative result.

References

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