Do Sick Children Accumulate New Diagnoses Faster? Rate Equations for Pediatric Long COVID

After a SARS-CoV-2 infection, some children pick up new diagnoses over the following months: fatigue, chest pain, migraine, gastrointestinal problems, flares of conditions they already had. Today this burden is summarized with single ratios, such as "infected children with chronic conditions use 21% more healthcare," or with static clusters of co-occurring codes. Those summaries cannot answer the questions that matter for prognosis. Is the excess burden driven by children gaining new conditions faster, or by conditions failing to resolve? Is the excess spread evenly, or concentrated among children who were already carrying several diagnoses? And does a child's pre-infection condition burden keep shaping their trajectory, or does its influence fade?

We propose to answer these questions with rate equations borrowed from network physics. In that literature, nodes are sorted into "buckets" by how many links they have, and differential equations track how nodes move between buckets as links are added and removed. Here, each child is a node in a growing child–diagnosis network. The child's "degree" is the number of distinct conditions active at a given time. Pre-existing chronic conditions form the starting graph, which that literature calls the substrate. Infection perturbs the rules that add and remove links. Fitting these equations to pediatric electronic health records yields two interpretable curves. The first gives how fast a child with $k$ active conditions acquires another. The second gives how fast each existing condition resolves as a function of $k$. Comparing these curves between infected and uninfected children breaks the single utilization ratio into acquisition, persistence, and dependence on prior burden.

Core Claim

Post-acute burden in children has a measurable shape, not only a size. We claim that a small parametric birth–death rate equation over condition counts can do three things. It can recover whether infection steepens accumulation among already-burdened children, which is the clinical analogue of preferential attachment, where well-connected nodes gain links faster. It can recover whether infection lengthens condition persistence specifically at high burden, the analogue of preferential survival. And it can recover how quickly the imprint of the pre-infection substrate decays. We also claim that the model forecasts the 12–18 month distribution of condition counts from early follow-up at least as well as flexible alternatives, while staying interpretable.

Write $N_k(t)$ for the expected number of children with exactly $k$ active conditions at time $t$ since cohort entry. Write $\lambda(k)$ for the rate at which such a child gains a new condition, and $\mu(k)$ for the per-condition resolution rate. The population then evolves as

$$\frac{dN_k}{dt} = \lambda(k-1)N_{k-1} - \lambda(k)N_k + (k+1)\mu(k+1)N_{k+1} - k\,\mu(k)N_k ,$$

with the kernels parameterized as $\lambda(k)=\lambda_0(1+k)^{\theta}$ and $\mu(k)=\mu_0(1+k)^{-\alpha}$. The exponent $\theta$ measures accumulation: $\theta=0$ means burden-independent acquisition and $\theta=1$ means linear preferential attachment. The exponent $\alpha$ measures preferential persistence: $\alpha>0$ means conditions in heavily burdened children resolve more slowly. Infection is allowed to change $\lambda_0$, $\mu_0$, $\theta$ and $\alpha$ over piecewise windows of post-infection time. The initial condition $N_k(0)$ is each child's pre-infection condition count.

Why This Connection, and What Is New

The method comes from rate-equation work on growing networks. Fotouhi and Rabbat put arbitrary starting graphs directly into the master equations (Growing a Network on a Given Substrate). They showed that the substrate's memory dominates early on and decays over time, and that uniform versus linear attachment produce exponential versus power-law limits. Kong and Roychowdhury modeled heavy node turnover with a deletion kernel $D(k)\propto k^{-\alpha}$, in which hubs survive preferentially, and showed that this kernel controls the stationary degree exponent (Preferential survival in models of complex ad hoc networks). Both were developed on synthetic graphs or web crawls. We reuse their kernel structure and substrate formulation, but our "deletion" removes links (conditions resolving) rather than nodes. Our parameters also change with time since infection, which the file identifies as a largely unsolved regime for exact solutions. For nonlinear kernels and time-varying rates we solve numerically and do not claim closed forms. Closed forms are used only as checks at $\theta\in\{0,1\}$.

The motivation comes from pediatric work showing that burden in children is entangled with prior chronic disease. Lorman et al. ran an agnostic tree-based scan over the ICD-10 hierarchy in RECOVER PEDSnet. They found 304 enriched clusters, signals that adult checklists miss, and 55.8% of pediatric cases carrying a pre-existing chronic condition (Understanding pediatric long COVID using a tree-based scan statistic approach). Pajor et al. found overall post-acute utilization rate ratio (URR) 1.21 and inpatient URR 2.03 among children with chronic conditions (Healthcare utilization following SARS-CoV-2 infection in children and adolescents with chronic conditions). The T1D study fit piecewise HbA1c slopes and a Cox model whose hazard ratio was not significant (Impact of SARS-CoV-2 Infection on Disease Trajectory in Youth with T1D). None of these separates acquisition from persistence, and none asks whether the effect depends on the burden a child already carries.

The closest dynamic model is latent transition analysis in the adult ORCHESTRA cohort (Latent Transition Analysis for Longitudinal Studies of Post-Acute Infection Syndromes). It is a hidden Markov model over seven latent symptom states measured every six months. It differs from our proposal in three ways. Its states are latent categories, not observed counts with a structured kernel. Its time is discrete and coarse. Its population is adult. Static adult phenotyping constrains the design rather than supplying it. Poisson factor analysis subphenotypes (Data-driven identification of post-acute SARS-CoV-2 infection subphenotypes) and propensity-weighted screening of 137 diagnostic categories (Data-driven analysis to understand long COVID using electronic health records) both collapse a 30–180 day window into one snapshot. That is exactly the information our model needs to keep.

Research Program

The data are RECOVER PEDSnet records under the OMOP common data model, with the same exposure definitions, controls, and 18-month washout used by Lorman et al. The infected group consists of children with documented infection. There are two control groups: COVID-negative children, and positive children without a PASC code. These controls matter because the file flags under-coding of the PASC code U09.9 and the resulting bias toward null effects.

A "condition" is a diagnosis category at a fixed level of the ICD-10 tree. It counts as active if it was coded within a trailing activity window. Ninety days is the primary choice, with 60 and 180 days as sensitivity checks, because the window is a real degree of freedom that can manufacture persistence. The pre-infection count over the washout period defines each child's substrate.

The most serious threat is that infected children simply visit more often, and more visits produce more codes. We handle this with an observation layer: a condition is recorded only if an encounter occurs, so visit rates enter the likelihood separately from true acquisition. We also fit the same model to negative-control code families, injuries and routine well-child codes, where infection should not change the kernels.

Estimation works at the child level. Each child's count follows a birth–death Markov chain, and panel observations at irregular encounter times give an interval-censored likelihood computed with matrix exponentials. Covariates such as age, variant era, acute severity, and the chronic-condition flags from Pajor et al. enter as multiplicative effects on $\lambda_0$ and $\mu_0$. The kernel exponents are estimated per group. Before using real data, we simulate cohorts from known kernels, with realistic visit sparsity and coding dropout, to check that $\theta$ and $\alpha$ are identifiable at PEDSnet-like sample sizes and follow-up lengths.

Baselines

The naive reference point assumes infection does nothing. We fit the rate equation to each child's pre-infection period and to COVID-negative controls, then propagate it forward. If infected children's 12–18 month count distributions are no worse predicted by this than by any infection-aware model, there is nothing to decompose.

The first strong competitor is the regression approach the field already uses. This means negative-binomial generalized estimating equations on condition counts and visit counts, in the style of Pajor et al. (overall URR 1.21, 95% CI 1.18–1.24; inpatient URR 2.03) and the piecewise-slope models of the T1D study. It is strong because it is simple, robust, and already accepted clinically. We fit it to the same cohorts, windows, and covariates. We report both its rate ratio, which should reproduce the published 1.21 order of magnitude on the chronic-condition subset as a sanity check, and its forecast of count distributions.

The second and most serious competitor is a nonparametric continuous-time multistate model. It uses the same counts and the same observation layer, but gives each bucket its own free gain and loss rate. It nests our model, so it is the fair test of whether the power-law kernels are a useful constraint or only a convenient story. The two get the same data, the same likelihood machinery, and the same regularization search budget.

The third competitor is latent transition analysis following the ORCHESTRA design, refit to pediatric data at the finest epoch the data support.

For the forecasting task, we found no reported result on Lacuna for pediatric condition-count trajectories. The nearest published predictive number is a median AUROC of 0.76 for logistic regression predicting adult U09.9 diagnosis in N3C (Predictive models of long COVID). We cite it only as context, because the task differs.

Beating the competitors means the following. We need held-out log-likelihood per child-month at least equal to the nonparametric multistate model, with tighter intervals at high counts ($k\ge 4$), where data are sparse. We need better calibration than the regression baseline for the probability of entering the high-burden buckets by month 12. We need lower error than every baseline on the forecast count distribution at 12 and 18 months from fits on the first six months, measured with a Wasserstein distance and tail mass.

The ablations isolate each ingredient: fixing $\theta=0$, fixing $\alpha=0$, dropping the substrate initial condition, and dropping the observation layer.

Why not just…?

Why not just report utilization or condition-count rate ratios with regression, as RECOVER already does? A rate ratio of 1.21 can arise from faster acquisition, slower resolution, or both. It can arise from a uniform shift or from a concentrated surge in already-burdened children. Each implies different follow-up care. The regression baseline is fit to the same data, so the experiment shows directly whether the kernels contain information it misses. If the infection effect turns out to be a pure scale change ($\theta$ and $\alpha$ identical across groups), the regression summary is adequate, and we will say so.

Why not just fit a fully nonparametric multistate model? This is the real threat, because it is more flexible and contains our model as a special case. If it matches us everywhere, including at sparse high counts, then our contribution shrinks to the estimated exponents as a descriptive result. That would still be a finding, but a smaller one. The decisive comparison is extrapolation: forecasting 18-month distributions and high-burden buckets from short follow-up, where a two-exponent kernel should borrow strength and free per-bucket rates should be unstable.

Why not just use latent transition analysis, which has already been applied to post-COVID condition? The ORCHESTRA model is built on six-month epochs and latent categories whose meaning shifts with how the model is specified. Pediatric records are dense, irregular encounter streams in which the pre-infection substrate is observed directly. We run the latent model as a baseline. If it forecasts better, that indicates that symptom type matters more than symptom count. We would then extend our buckets to counts within organ systems rather than defend a single count.

Decisive Checks

Four results would settle whether the idea is worth pursuing. The first is substrate memory. In the growth-only setting of Fotouhi and Rabbat, the influence of the starting graph decays. We will test whether the gap in trajectories between children with zero and with two or more pre-existing conditions shrinks at the rate the fitted kernels predict. A gap that persists beyond that rate would point to unmodeled per-child heterogeneity, which would itself be a reportable result. The second check is that negative-control code families show no infection-driven change in $\theta$ or $\alpha$. If they do, the visit-driven detection artifact has not been removed. The third check is whether the pre-Omicron and Omicron eras, which Lorman et al. found enrich different clusters, differ in kernel shape or only in scale. The fourth is subgroup replication in the chronic-condition cohort of Pajor et al. and the T1D cohort, to test whether the inpatient surge corresponds to a measurably steeper accumulation exponent among children who entered infection already carrying multiple diagnoses.