Children with long COVID rarely show up with one new problem. They arrive with fatigue, shortness of breath, chest pain, headaches, and sometimes something unexpected, such as blood in the urine. The largest pediatric electronic-health-record study tested each diagnosis category separately and found 304 that are statistically elevated after infection (Lorman et al.). A list of 304 overlapping signals cannot answer the questions clinicians and phenotype designers actually ask. How much of the extra illness after infection does each diagnosis account for? Which diagnoses are just echoes of each other? Which flag children that nothing else would catch?
We propose answering these questions with the Shapley value, the cooperative-game rule for splitting a group's total output fairly among its members. Here the "players" are diagnoses, and the "output" of any set of diagnoses is the excess fraction of infected children, compared with matched uninfected children, who acquire at least one new diagnosis from that set. The Shapley value then splits the total excess burden among diagnoses. A diagnosis that usually co-occurs with others gets only a share of each child's credit. A diagnosis that is often a child's only new problem keeps full credit. The shares add up exactly to the overall excess. For this particular game the computation is exact, has a closed form, and runs in linear time. We expect the resulting ranking to differ from per-diagnosis relative risk in predictable ways, and we test whether it produces better compact definitions of pediatric long COVID.
Core Claim
The obvious way to join these two literatures is to compute Shapley centrality on a SARS-CoV-2–host protein interaction network and rank genes for post-acute sequelae. That is a near-copy of the one existing bridge paper. Sun et al. combined Shapley values from case–control variant data with a STRING protein network to rank autism candidate genes, and it surfaced HLA genes that degree, betweenness and PageRank missed. That idea would also sit on data the file does not contain: there is no pediatric molecular cohort here, and gene rankings have no ground truth. We therefore move the game to the level where pediatric post-acute data actually exist, the bipartite graph linking children to their new post-infection diagnoses.
On that graph, the value of a set of diagnosis nodes is the number of child nodes it touches. This is exactly the group degree centrality that Tarkowski et al. place in their polynomial-time class. Our method differs from theirs in one respect: we take the difference of two such games, one for infected children and one for uninfected children.
Concretely, let $D_c$ be the set of new diagnoses (players) for child $c$ in the post-acute window. Let $P$ and $Q$ be the matched COVID-positive and COVID-negative groups, with sizes $n_P$ and $n_Q$. For any set $S$ of diagnoses, define $v(S)$ as the fraction of $P$ with at least one diagnosis in $S$, minus the same fraction in $Q$. Each child contributes a game worth 1 when $S$ intersects $D_c$. In a random ordering of players, a diagnosis $i$ is pivotal for that child exactly when it comes first among the child's diagnoses, which happens with probability $1/|D_c|$. The Shapley value is therefore
$$ \phi_i \;=\; \frac{1}{n_P}\sum_{c\in P,\; i\in D_c}\frac{1}{|D_c|}\;-\;\frac{1}{n_Q}\sum_{c\in Q,\; i\in D_c}\frac{1}{|D_c|}, $$
and the values sum to $v(N)$, the total excess burden.
This makes the redundancy correction completely transparent. Each child's unit of illness is split equally among that child's new diagnoses. The same derivation gives two variants. The Banzhaf index gives weight $2^{-(|D_c|-1)}$ instead of $1/|D_c|$, so it penalizes co-occurrence more steeply. The Owen value, the version of Shapley for players grouped into fixed blocks, uses organ systems as blocks. If a child's new diagnoses span $m$ systems and $k_j$ of them fall in system $j$, each of those diagnoses receives $1/(m k_j)$. The result is an organ-system decomposition of excess burden that respects the ICD hierarchy.
The claim is that these redundancy-corrected shares are a more useful summary of pediatric post-acute burden than independent per-cut tests. We will test this through stability across hospitals, through the quality of short phenotype rules built from the shares, and through era-to-era decomposition of how the burden shifted.
Research Program
The first step is to reconstruct the cohort design of Lorman et al. in RECOVER PEDSnet. That design has 1,309 cases coded U09.9 or B94.8, 6,545 COVID-positive and 6,545 COVID-negative propensity-matched controls, and an 18-month pre-infection washout so that only new diagnoses count. Access requires the standard RECOVER data-use process. Players are a partition of the ICD-10 tree into non-overlapping branches. We will start with the significant TreeScan cuts, with any nested cuts resolved to their deepest non-overlapping level, and check sensitivity to the cut level.
The second step computes Shapley, Banzhaf, Owen and leave-one-out shares. Leave-one-out credits a diagnosis only for children in whom it is the sole new code. By Skibski's result, removal-based ("vitality") scores belong to the same game-theoretic family (Vitality Indices are Equivalent to Induced Game-Theoretic Centralities), so leave-one-out is the natural extreme of the spectrum. Because every estimator is a sum over children, we get site-clustered bootstrap intervals essentially for free.
The third step tests whether the shares are useful, as described under Proposed Experiments.
The fourth step tests a pre-registered substantive prediction. Broad symptom codes in the R00–R99 branch (dyspnea, chest pain, fatigue), which dominated the TreeScan signal, should lose share under Shapley because they co-occur heavily. Isolated signals such as hematuria and nutritional deficiencies should retain share. The variant-era shift toward urinary manifestations and migraine reported by Lorman should appear as a reallocation of a fixed-sum budget.
A secondary, small-scale application uses the PEDSnet MIS-C cohort (Rao et al.). Its eight organ-involvement variables allow exact enumeration of all 256 sets. We will attribute ICU admission risk to organ systems and compare this with Rao's three latent classes. The specific question is whether Shapley shares explain the drop in the severe class from 52.3% pre-Delta to 39.6% under Omicron as loss of a few organ systems or as diffuse change.
Baselines
The naive reference is the singleton excess, $v(\{i\})$: each diagnosis's own excess incidence among infected versus uninfected children, with no adjustment for overlap. Every per-diagnosis risk table implicitly reports this. Our method must disagree with it where co-occurrence is high, and the disagreement must pay off downstream; otherwise the game adds nothing.
The strongest existing method is the TreeScan analysis of Lorman et al., which ranks hierarchical cuts by a scan log-likelihood ratio with multiple-testing control. Lorman reports 304 significant cuts in the case versus COVID-negative comparison. We found no reported result on Lacuna for any phenotype-capture, predictive or cross-site stability metric for TreeScan rankings. We will therefore rerun TreeScan on the identical matched cohort, players and post-acute window, and rank by its statistic.
The strongest machine-learning competitor is a classifier of infected versus uninfected status from the binary diagnosis matrix, with attributions taken from its coefficients or from per-feature Shapley explanations. The classifier will be an L1-penalized logistic regression and a gradient-boosted tree model. Both are tuned by site-grouped cross-validation, with the same tuning budget used to choose our only free choice, the ICD cut level.
For selecting compact phenotype rules, the strongest competitor is greedy maximization of $v(S)$ itself: repeatedly add the diagnosis that most increases excess coverage. Two ablations isolate the key ingredient, credit sharing among co-occurring diagnoses. Leave-one-out removes sharing entirely by crediting only unique children. Banzhaf changes the sharing rule while keeping everything else fixed.
Beating a baseline has three meanings, all evaluated with site-grouped bootstrap intervals. The first is higher leave-one-site-out rank stability. The second is that, at a matched rule size, the rule built from our ranking captures more excess burden or has higher positive predictive value for coded cases. The third is that the predicted direction of reranking holds on held-out sites.
Why not just…?
Why not just rank diagnoses by TreeScan or by relative risk? These scores treat each diagnosis independently, so ten correlated symptom codes all rank high even though they flag the same children. The 304-cut output in Lorman et al. shows the problem: the strongest signals were concentrated in one broad symptom branch. This criticism only matters if the reranking changes downstream rules. If phenotype rules built from TreeScan order match ours at equal size, we will report that the redundancy correction is cosmetic.
Why not just fit a classifier and use SHAP or LASSO coefficients? This is a real threat, since both also discount redundant features. Their attributions, however, explain a fitted model's log-odds. They depend on regularization and model class, they can split credit arbitrarily between perfectly collinear codes, and they do not sum to anything clinically interpretable. Our shares are model-free, exact, and sum to excess children per thousand. The experiments settle the question directly by comparing cross-site stability and rule quality. If the boosted-tree SHAP ranking is equally stable and yields equally good rules, the honest conclusion is that our contribution reduces to a closed-form, auditable equivalent.
Why not just select phenotype diagnoses by greedy maximum coverage? For the pure selection task, greedy optimization of $v(S)$ may be as good as or better than ranking by Shapley, because it optimizes the target directly. We do not claim otherwise. Shapley's role is attribution: a single order-independent allocation that is stable to which diagnoses happen to be chosen first. We will report greedy as the selection upper reference and judge our method mainly on attribution stability and on era-decomposition.
Why not just apply Shapley centrality to a SARS-CoV-2–host interactome, the obvious bridge? Sun et al. already established that template for pediatric gene prioritization. Gulbahce et al. showed that viral targets sit near disease genes. Neither direction provides pediatric post-acute molecular data or a validation target in this file. A gene ranking without an outcome to check it against would be untestable here, whereas EHR attributions can be checked across nine hospitals.
Proposed Experiments
The first experiment tests stability. For each method we compute its diagnosis ranking on eight hospitals and correlate it with the ranking on the held-out ninth. A useful attribution should replicate across sites despite differences in coding practice.
The second experiment builds compact rules. For each rule size from 3 to 25 diagnoses, the rule is "any new diagnosis in the top-$k$." We report the fraction of total excess burden captured on held-out sites. We also report positive predictive value and sensitivity for U09.9/B94.8-coded cases against COVID-positive and COVID-negative controls. The codes are an imperfect silver label, since the file notes coding lag and contaminated controls, so we will also chart-review a stratified sample of rule-positive, uncoded children if feasible.
The third experiment is the pre-registered reranking test. Shapley share relative to singleton excess should fall with average co-occurrence count. Broad R00–R99 symptom codes should drop and isolated codes should hold.
The fourth experiment is era decomposition. Because shares sum to the total excess, the pre-Omicron versus Omicron change in total burden decomposes exactly into per-diagnosis and, through the Owen value, per-organ-system contributions. We test whether that decomposition reproduces the metabolic-to-urinary shift Lorman described, and whether it is more stable under bootstrap than differences in per-cut statistics.
For external replication with a different comparator, we will recompute the game in the five-country cohort of 55,270 children with COVID-19 and 1,952,693 with influenza (international network cohort), replacing $Q$ with influenza-positive children. This separates SARS-CoV-2–specific shares from generic post-viral ones. The file gives no outcome figures for this cohort, so all of this would be new measurement.
The decisive check is the comparison of the Shapley ranking against the singleton-excess and boosted-tree SHAP rankings on held-out sites. If it is neither more stable nor better at matched rule size than either one, the approach should be abandoned as offering no advantage beyond interpretability.
References
- Understanding pediatric long COVID using a tree-based scan statistic approach: An EHR-based cohort study from the RECOVER Program
- Game theoretic centrality: a novel approach to prioritize disease candidate genes by combining biological networks with the Shapley value
- Efficient Computation of Semivalues for Game-Theoretic Network Centrality
- Vitality Indices are Equivalent to Induced Game-Theoretic Centralities
- Spectrum of severity of multisystem inflammatory syndrome in children: an EHR-based cohort study from the RECOVER program
- Viral Perturbations of Host Networks Reflect Disease Etiology
- Baseline characteristics, management, and outcomes of 55,270 children and adolescents diagnosed with COVID-19 and 1,952,693 with influenza in France, Germany, Spain, South Korea and the United States: an international network cohort study