When a hospital has an outbreak and only a few rapid tests or isolation beds per day, two kinds of signal are available. The contact network says who would spread the infection furthest if infected. The laboratory panel, a few blood counts and vitals combined into a risk score, says who is probably infected now. Network immunization research uses only the first signal and assumes infection status is known exactly. Clinical diagnostics research uses only the second and ignores who the patient goes on to expose. This note argues that the decision quantity is the product of the two, discounted by how long the test result takes to come back. It also argues that each signal alone fails in the same way a single biomarker fails: it collapses a two-dimensional problem onto one axis.
The second claim concerns evaluation. A policy like this cannot be credibly judged by checking, after the fact, whether the people it flagged turned out positive. Clinicians test the people they already suspect, and an audit of a sepsis alert system showed that this produces benefits that do not exist. We therefore propose a testbed that reproduces this suspicion-driven confounding, judges policies only by randomized allocation, and requires every policy to transfer to a different contact network and a different patient population before any claim is made.
Core Claim
For node $i$ at time $t$ we define a priority score
$$s_i(t) = \hat p_i(t)\,\sum_j w_{ij}\,\big(1 - F_\tau(h_{ij})\big),$$
where $\hat p_i(t)$ is a locally recalibrated probability that $i$ is infected, computed from a multi-marker panel. $w_{ij}$ is the expected contact duration between $i$ and $j$ per unit time. $F_\tau$ is the cumulative distribution of lab turnaround time $\tau$, evaluated at the horizon $h_{ij}$ over which that exposure would occur. The last factor therefore counts only the exposures that can still be prevented once the result arrives.
The specific, falsifiable hypothesis concerns the low-budget regime. On real high-resolution contact data, A high-resolution human contact network for infectious disease transmission found two things. Targeted immunization was no better than random at 5% coverage and helped only from 20% upward. Contact duration predicted outbreak size far better than degree ($r^2 = 0.929$). We predict that the failure at 5% coverage is a detection failure, not a topology failure. With a few interventions, the bottleneck is finding who is infected, so multiplying by $\hat p_i$ should make small budgets useful where topology alone cannot. If the joint score does not beat both marginal rankings at 5–10% budgets, the hypothesis is wrong.
How This Relates to Prior Work
Three lines of network-control work supply the topological half and its limits.
- An Experimental Study on Network Immunization benchmarks Degree, NetShield (which maximizes the drop in the graph's leading eigenvalue) and DAVA. It finds that winners depend on graph type.
- Controlling Epidemic Spread Under Immunization Delay Constraints shows that a delay before intervention takes effect makes nearby hubs poor targets. It gives a greedy guarantee, but only on trees.
- Controlling Graph Dynamics with Reinforcement Learning and Graph Neural Networks (RLGN) learns testing and isolation under partial observation with graph neural networks, which are models that pass information along graph edges.
All three treat node state as a clean susceptible, infected or recovered label. The delay paper's delay concerns vaccine effect, not diagnosis. We replace the clean label with an uncertain multi-marker probability and make diagnostic turnaround the delay. The delay paper motivates our discount term. The tree-only guarantee constrains us: we make no approximation claim on the cycle-dense contact graphs we use.
The diagnostic half comes from work showing that combined routine markers beat single ones. On the triage dataset in Creating an automated trigger for sepsis clinical decision support at emergency department triage using machine learning, AUC was 0.67 with vitals alone and 0.86 with free text added. AUC, the area under the ROC curve, is the chance a model ranks a random positive above a random negative. In Identification of routine blood derived hematological and lipid indices in ILD through machine learning, a six-feature panel reached external AUC 0.849, against 0.793 for a single ratio. We reuse this style of cheap routine-lab model as the source of $\hat p_i$. We do not claim new diagnostic modeling.
Two papers constrain how we evaluate.
- Randomized Clinical Trials or Convenient Controls: TREWS or FALSE? audited the evidence for TREWS, a sepsis early-warning system. In that audit, purely random alerts showed an apparent mortality drop from 6.4% to 3.3% once the analysis conditioned on prompt lactate ordering. This motivates our insistence on randomized evaluation inside the testbed.
- All models are local documents the Epic Sepsis Model's AUC falling from an advertised 0.73–0.83 to 0.60–0.64 in independent hospital evaluations. This motivates recalibrating $\hat p_i$ locally.
The external-transfer gap reported in A Clinically Practical and Interpretable Deep Model for ICU Mortality Prediction with External Validation. (eICU 0.912 to MIMIC-III 0.855) gives a concrete precedent for the patient-population shift we impose.
Finally, Measures to prevent nosocomial transmissions of COVID-19 based on interpersonal contact data simulates fixed staff-rotation policies on a hospital contact network. It does not choose individuals adaptively from diagnostic data. We use its network, if obtainable, as a hospital-like transfer target.
Research Program
The real-data prerequisite is a hospital where both contact logs and routine labs are recorded for the same people. The file contains no such dataset. We therefore build a semi-synthetic testbed whose two halves are each empirical. That limitation sets the scope of every claim below: the results are evidence about mechanisms, not evidence of clinical efficacy.
Contact layer. Contact structure comes from empirical networks. The primary network is the 788-person sensor network from the high-resolution contact paper, which records over 760,000 interactions and supplies duration weights. The hospital transfer target is the Hebei General Hospital contact network, if the data can be obtained; the file does not indicate public release. Otherwise we use synthetic modular ward networks parameterized to match that paper's reported outbreak scale. A stochastic transmission model with an exposed stage, plus asymptomatic transmission, runs on these networks.
Marker layer. Each simulated person's observable profile is drawn from real patients. When person $i$ is tested, the testbed samples a lab-and-vitals vector from the pool of real eICU or MIMIC-III patients matching $i$'s true state: infected, or not infected. The result is returned after a turnaround drawn from $F_\tau$. The infection labels are not specified in the file, so this is a design choice: we would define them with an infection-diagnosis code, analogous to how the ED triage paper derived its sepsis outcome from discharge codes. The risk model behind $\hat p_i$ is trained on one database and deployed in simulation using profiles from the other. This reproduces the documented transfer gap.
Clinician layer. Simulated clinicians order tests preferentially on symptomatic people and on high-contact staff. This reproduces the "processes of care" pathway identified in the TREWS audit, the causal route by which existing clinician suspicion drives both test ordering and outcome.
Policies and budgets. Each policy chooses up to $k$ people per day to test and isolate if positive, with $k$ set at 2–20% of the population.
What we measure. - Infections averted relative to no intervention. - Peak simultaneous infections. - Tests consumed. - A second evaluation, run in parallel, that mimics a retrospective audit: the positive rate among flagged people, and outcome differences between people who were and were not promptly tested. We report how far the ranking of policies under this audit disagrees with the ranking under randomized allocation, using Kendall's rank correlation between the two orderings.
Transfer conditions. Every policy is tuned in a source condition (school network, eICU-trained risk model) and frozen. It is then run in target conditions (hospital-like network, MIMIC-III marker pool), both with and without a short "silent mode" local recalibration of $\hat p_i$, following the recurrent local validation lifecycle proposed in All models are local. Silent mode means the model scores patients but no decisions are made from its output. Recalibration uses the first $n$ simulated days of tested results.
Baselines
Random allocation. Choosing $k$ people uniformly at random is the naive reference. The contact-network paper reports it as indistinguishable from targeting at 5% coverage, so beating it at that budget is the minimum bar.
Pure topology. Within this family, the strongest simple competitor is duration-weighted strength targeting. The sensor-network evidence ($r^2 = 0.929$ for strength versus outbreak size) makes it stronger than raw degree. We also run degree targeting and NetShield as implemented in An Experimental Study on Network Immunization. We also run the delay-aware greedy method of Controlling Epidemic Spread Under Immunization Delay Constraints, applied heuristically off-tree.
Pure risk. "Test the sickest" ranks people by $\hat p_i$ alone. We run it with the full multi-marker model and with a single-marker model built from vitals only. The single-marker version mirrors the 0.67 versus 0.86 AUC contrast in the ED triage paper, and isolates whether multiple markers matter once topology is in the score.
Strongest existing method: RLGN. We use RLGN from Controlling Graph Dynamics with Reinforcement Learning and Graph Neural Networks, given the marker-derived $\hat p_i$ as an extra node feature so that it can in principle learn the product itself. That paper reports RLGN keeping 51% of a 50,000-node population healthy versus 21% for its best supervised baseline, and 60% containment on a three-community graph where supervised learning achieved 0%. There is no reported result found on Lacuna for RLGN, or any of these policies, with noisy biomarker inputs or on the sensor contact network.
Fair comparison. All policies share the same simulator seeds, budgets, turnaround distribution and source-condition tuning budget, matched in simulator rollouts. RLGN receives the same number of rollouts for training as the other methods receive for hyperparameter search.
Ablations. Three ablations isolate the key ingredients: removing the turnaround discount, replacing multi-marker $\hat p_i$ with the single-marker version, and skipping local recalibration.
What counts as winning. The joint score must avert more infections than both the strength-only and risk-only rankings at the 5% and 10% budgets. The improvement must exceed seed-to-seed variability across at least 200 simulated outbreaks per condition. It must also hold in the transfer condition after recalibration.
Why not just…?
Why not just isolate the people with the longest total contact time? This is the most credible simple alternative, and it is a baseline. The evidence against it as a full answer is the same paper that recommends it: at 5% coverage, targeting gave no gain over random. That is exactly the operating regime of scarce tests. The proposal's experiment either shows strength-only staying near random at low budgets while the joint score separates from it, or it does not. If it does not, the hypothesis is refuted.
Why not just test the sickest-looking patients? Risk-only ranking finds infected people but ignores whether they will expose anyone before their result returns. Isolated, low-contact patients may score high and avert little. The proposal's comparison with risk-only, broken down by node strength, tests this directly. If the infected people in the network turn out to be almost all high-contact staff, the two signals are correlated and the joint score adds little. We would report that as a finding about hospital topology, not hide it.
Why not just hand the marker scores to RLGN and let it learn the policy? This is a real threat, because a learned policy could discover the product, and more. We include exactly this variant. If it matches or beats the closed-form score in the source condition, the interpretable score is justified only if it transfers better without retraining. We test this by measuring the drop of each policy between source and target. Either way, the evaluation-protocol results do not depend on which policy wins.
Why not just run a real cluster-randomized trial on wards? That is the end goal, and the TREWS audit shows nothing weaker is convincing about patient outcomes. A trial is expensive, though, and must commit to a small number of arms in advance. The testbed's purpose is to pick those arms, estimate effect sizes for power calculations, and show in advance which non-randomized analyses would mislead. The resulting design would allocate policies across wards in a stepped-wedge rollout, in which wards switch to the new policy at randomized times, with silent-mode recalibration at each site.
Decisive Checks
Check 1: the low-budget hypothesis. Does the joint score beat both strength-only and risk-only rankings at 5% budget on the sensor network? A null result here ends the method claim.
Check 2: the confounding reproduction. Inside the testbed, does the retrospective-style audit show a spurious benefit for random allocation, as the TREWS audit's coin-flip protocol did? Does it rank policies differently from randomized evaluation? If the audit shows no spurious benefit, our clinician model is too weak and must be strengthened before other results are trusted.
Check 3: transfer and recalibration. When the eICU-trained risk model and source-tuned policies move to the MIMIC-III marker pool and the hospital-like network, how much of the averted-infection advantage survives? How much of the loss does a few days of local recalibration recover? A large unrecovered loss would show that network-guided surveillance inherits the "all models are local" problem in its topological component as well as its diagnostic one. Each site would then have to measure its own contact network before deployment.
References
- A high-resolution human contact network for infectious disease transmission
- An Experimental Study on Network Immunization
- Controlling Epidemic Spread Under Immunization Delay Constraints
- Controlling Graph Dynamics with Reinforcement Learning and Graph Neural Networks
- Creating an automated trigger for sepsis clinical decision support at emergency department triage using machine learning
- Identification of routine blood derived hematological and lipid indices in ILD through machine learning; a retrospective case-control study
- Randomized Clinical Trials or Convenient Controls: TREWS or FALSE?
- All models are local: time to replace external validation with recurrent local validation
- A Clinically Practical and Interpretable Deep Model for ICU Mortality Prediction with External Validation.
- Measures to prevent nosocomial transmissions of COVID-19 based on interpersonal contact data