Density-Gated Transmission Rates for Epidemic Forecasting

Crowding speeds up disease spread. The evidence for this is consistent across settings. Population density was the dominant driver of district-level COVID-19 surges in Bangladesh, while literacy rates showed no association (Sharif et al.). Density was among the top three predictors of case volume across Hong Kong planning units (Hong Kong SHAP study). It was the strongest socio-demographic predictor of viral load in English wastewater (wastewater geostatistics). Yet the neural forecasters that now lead regional epidemic benchmarks never see density. When they do receive it, it arrives as one more number appended to each region's feature vector. That number then has to compete with long case-count histories for the network's attention. The multimodal medical-imaging literature has shown that this setup lets the high-dimensional stream swamp the low-dimensional table.

We propose to put density in the one place where epidemiology says it acts: as a multiplier on the transmission rate inside a compartmental model that a graph neural network (a network that passes information between neighbouring regions on a map) learns to drive. A small monotone network maps each region's static crowding table to a gain on its infection rate. The case-count stream is only allowed to set the time-varying part of that rate. The payoff is twofold. The first is a forecaster that should transfer to regions it was never trained on, because the density effect is shared rather than memorised region by region. The second is a measured, uncertainty-quantified answer to an old epidemiological question: how steeply does transmission scale with density for influenza versus COVID-19?

Core Claim

The claim is structural, not architectural. For low-dimensional static covariates whose causal role is known, the right fusion operation is placement inside the mechanism, not a better attention block. We write each region $i$'s transmission rate as

$$\beta_i(t) = \beta_0(t)\, g_\phi(x_i)\, m_i(t),$$

where $\beta_0(t)$ is a shared seasonal baseline, $x_i$ is region $i$'s static crowding table (population density, household size, share of service-sector workers, low-income share), $g_\phi$ is a monotone network shared across all regions, and $m_i(t)$ is a bounded residual inferred from the region's recent case history by the graph network.

This rate enters a susceptible–infected–recovered (SIR) residual penalty. That penalty works the same way as in HeatGNN, which learns per-region SIR parameters from case series alone and penalises departures from the standard SIR equations.

Because $x_i$ reaches the output only through $g_\phi$, the network cannot drown it out, and it also cannot ignore it. Because $g_\phi$ is shared, it can be read out as a density–transmission curve. That curve has a log-log slope, the elasticity $\alpha = \partial \log \beta / \partial \log \rho$ with $\rho$ the population density. An elasticity of 0 corresponds to classical frequency-dependent mixing and 1 to pure mass action.

We predict three things. The gain over density-blind forecasters will be small when a region is seen during training and large when it is held out. The learned curve will be sub-linear and pathogen-specific. And the curve will survive a check against a reporting-independent signal (wastewater).

Research Program

The work has three parts.

The first part is a controlled simulation in which the answer is known. We generate metapopulation epidemics on the real region graphs of the benchmarks below, planting known density curves: power law, saturating, and a threshold shape that mimics the "hothouse" amplification reported for informal settlements. We then ask whether $g_\phi$ recovers the planted curve. We also plant a confounder: the detection rate rises with density, as it plausibly does when cities test more. Without this confounder the recovery test would be too easy. Following the undocumented-versus-documented split in SUDR, we add a density-dependent reporting fraction as a second shared monotone function and test whether the two can be separated. We expect separation only when regions differ enough in their epidemic timing, and we will report where it fails.

The second part is real-data forecasting. Density and crowding tables are joined to the regional benchmarks. These tables are external census data at the benchmark's unit, which we will have to assemble; the file does not supply them.

The third part is a reporting-independent check. We fit the same gated structure to the England wastewater series. The argument is that viral concentration in sewage does not depend on who gets tested. So if the density gain is real transmission rather than a testing artefact, the curve fitted on sewage should resemble the one fitted on cases.

The design choices are constrained by prior negative results. Aggregate Google mobility streams did not improve forecasts across 49 US states and 28 EU countries (mobility and GCN study). For that reason we deliberately do not add mobility in the main model. Mobility enters only as an optional input to the residual $m_i(t)$, in an ablation. The staged fusion evidence from TFormer and TabMixer motivates keeping the table on a separate path. Those papers delay or mix tabular metadata specifically so that image streams do not wash it out. Our proposal differs in replacing learned mixing with a mechanistically placed gate.

Baselines

The naive reference is a per-region autoregressive model fitted to case counts alone. It shows how much any spatial or mechanistic structure buys.

The strongest existing forecasters are EpiGNN and HeatGNN. EpiGNN encodes local transmission risk from graph degree and learns region-to-region connections. It reports 5.6% lower RMSE than the best baselines on seasonal influenza and 13.4% lower on COVID-19. HeatGNN reports the lowest RMSE and highest Pearson correlation on US-States and US-Regions influenza, but I found no absolute error values reported on Lacuna for HeatGNN or EpiGNN. We will therefore rerun both from their released configurations on identical splits (EpiGNN's 50/20/30 temporal split), with the same hyperparameter search budget and seeds as our model. Beating them means lower RMSE at 1–12 week horizons on the held-out-region protocol described below, with a paired test across regions and seeds significant at 0.05. That significance bar matters because the mobility study's GCN gains of 1.20–2.85% MAE did not reach it.

The key ablation keeps the HeatGNN-plus-gate architecture identical but gives the same crowding table to the model in one of three alternative ways. The first is concatenation to node features. The second is conditioning that rescales and shifts internal activations from the table (FiLM-style). The third is an iterative bottleneck in which a shared latent array queries each input stream, as in HEALNet. HEALNet reports a 4.5% gain over existing fusion strategies on the TCGA cancer cohorts. This ablation isolates placement from information content, because every variant sees exactly the same numbers.

A final mechanistic baseline is a metapopulation SIR model whose transmission rate is a fitted parametric power law in density, estimated by Bayesian inference in the spirit of SUDR.

Why not just…?

Why not just add density as a node feature to HeatGNN or EpiGNN? This is the concatenation arm of the ablation, so it will be measured directly rather than argued. Our honest expectation is that it ties the gated model on regions seen during training. A per-region learned transmission rate can absorb any static regional factor, density included. The difference should appear only on held-out regions, where a concatenated feature has no guarantee of acting monotonically or multiplicatively. If concatenation also matches on held-out regions, the placement claim is false and we will report it that way.

Why not just fit a mechanistic model with a power-law density term? This is the real threat. If the learned curve $g_\phi$ turns out to be a straight line on log-log axes, a two-parameter power law captures the science. In that case the neural component is justified only by the residual $m_i(t)$ and forecasting accuracy. The parametric baseline tests exactly this. The synthetic threshold and saturation curves tell us whether the flexible curve earns anything when the truth is not a power law. Nobody currently knows which case holds on real data, and that is part of what the study will find out.

Why not just use XGBoost on crowding tables plus lagged cases? Tree models reached $R^2$ of 0.830 across Hong Kong units but struggled on large-outbreak clusters, which are exactly the dense estates where amplification matters (Hong Kong SHAP study). They also produce no transmission dynamics for multi-week horizons. We include a gradient-boosted model with lagged cases as a tabular baseline under the same held-out protocol.

Proposed Experiments

The primary benchmarks are Japan-Prefectures influenza (47 prefectures, 2012–2019), US-States influenza (49 states), and Australia and EU COVID-19 series. They are used as in EpiGNN and HeatGNN.

We choose Japan as the headline test for a specific reason. Its prefectures range from Tokyo to sparse rural regions, which gives the widest density contrast, and density is the source of identifying variation for $g_\phi$. Metrics are RMSE, MAE and Pearson correlation at 1, 3, 7 and 12 weeks.

We run each benchmark under two protocols. The standard protocol uses a temporal split with all regions in training. The decisive protocol holds out a fifth of the regions, stratified by density, trains on the rest, and forecasts the held-out regions from their early-season cases alone. We expect the gated model's advantage to be near zero under the first protocol and clearly positive under the second. That pattern would support the claim; uniform gains or uniform ties would refute it.

Secondary checks run at two scales. At the fine scale we fit the gated model to Hong Kong's 215 planning units to test whether the density curve steepens at fine spatial resolution, as the informal-settlement literature suggests. At the national scale we fit it to the 303-site England wastewater series. There we compare the fitted elasticity against the case-based fit, and compare predictive-interval coverage against the 94.1% that the R-INLA geostatistical model reports in 10-fold cross-validation.

Two outcomes would falsify the approach. The first is recovering the planted density curve only when the reporting confounder is switched off. The second is a sewage-based elasticity that disagrees with the case-based one.