Every indoor venue that reopened during a respiratory epidemic faced two decisions at once: who to let in, and where to put them. The two decisions are made by completely separate literatures. Ventilation studies show that where an infectious person sits relative to air supply ducts, exhaust vents, and seat columns changes everyone else's risk enormously — in a 100-seat theater, moving seats sideways cuts infection probability by 84.9–92.3%, while the same separation front-to-back, aligned with the airflow vortex, cuts it by only 36.3–74.0% (Is it Safe to Reopen Theaters During the COVID-19 Pandemic?). Screening studies, meanwhile, show that a door test's meaning depends on how common the infection is: positive predictive value — the fraction of flagged people who are actually infected — collapses as prevalence falls, so the same test that is useful in a surge mostly quarantines healthy people in a lull (Is “no test is better than a bad test”? Impact of diagnostic uncertainty in mass testing on the spread of COVID-19). No study joins the two. Seat-allocation models place infectors deterministically at fixed coordinates; screening models treat the room as a black box.
This proposal builds a joint policy. The core observation is that seat risk is two-sided: a seat has a risk of receiving contaminated air (the usual per-seat "safe seat" measure) and a separately quantified risk of emitting into other seats, which depends on proximity to return vents — an infected passenger beside a return vent had 60% of exhaled droplets removed within 20 seconds, while the same passenger deeper in the cabin tripled that removal time (Numerical Simulation of Droplet Dispersion and Passenger Infection Risk Assessment in a Subway Carriage). Because emission-side risk varies so strongly by seat, the cost of a screening false negative depends on where that undetected person is seated — and the cost of a false positive (a barred healthy patron) depends on prevalence. Seat allocation is therefore the natural lever for absorbing diagnostic uncertainty, and the optimal lever changes with prevalence.
Core Claim
Let each patron $i$ carry a posterior probability of infectiousness $p_i = P(D_i = 1 \mid t_i, \phi)$, computed by Bayes' rule from their screen result $t_i$, the test's sensitivity and specificity, and the community prevalence $\phi$. Let $T[s, s']$ be the probability that a source seated in seat $s$ infects a susceptible in seat $s'$ over one event, read off a precomputed computational-fluid-dynamics (CFD) airflow solution. Then the operator's problem is to choose an assignment $\sigma$ of patrons to seats, plus a bar-or-admit decision, minimizing
$$ \mathbb{E}[\text{infections}] \;=\; \sum_i p_i \sum_{j \neq i} T[\sigma(i), \sigma(j)] - \lambda \cdot (\text{barred patrons}), $$
where $\lambda$ prices the utility cost of refusing entry. The claim is threefold. First, the interaction term is first-order: because $T$ is highly anisotropic, policies that treat screening as deterministic (as Liang et al. must, since they assume 100%-certain infectors) leave a measurable gap against policies that use $p_i$, and that gap grows exactly when screening is least reliable. Second, the optimal policy switches regimes with $\phi$: at low prevalence, barring flagged patrons is mostly utility loss (their flags are mostly false alarms), and seating them in high-removal, low-emission seats dominates refusing them; at high prevalence, hard gating plus dilution-maximal placement of residual-risk patrons dominates. Third, since $\phi$ is never known exactly, the allocation should be driven by a concentration-bound-certified upper confidence interval on $\phi$, not a point estimate.
Research Program
The first component is a reusable transmission-matrix surrogate. Steady-state RANS CFD with the $k$-$\epsilon$ turbulence closure, exactly as Liang et al. use for the 100-seat theater (15.4 m × 8.0 m × 6.1 m) with their dilution-ratio-modified Wells-Riley model, is run once per ventilation configuration, and the resulting $100 \times 100$ matrix $T$ is then reused by every downstream policy. This amortization is the answer to the computational burden that Yang et al. hit with 223 parametric runs: policy search happens on the matrix, not in the solver. Validation is against published numbers — the surrogate must reproduce the reported lateral-versus-longitudinal reduction asymmetry and the staggered-seating reduction of 7.4–68.3% in maximum infection probability (Liang et al.). A second matrix is built for the subway carriage of Wu et al., where the exhaust-proximity contrast (D1 versus D2) and the dose thresholds for a 0.05 infection risk — roughly 2 trapped droplets at 100 µm, 12 at 50 µm, 1400 at 10 µm — give direct checks on the emission-side column of $T$.
The second component is the posterior model. Realistic (sensitivity, specificity) operating points come from the two acoustic-screening systems benchmarked on the DiCOVA 2021 cough-audio dataset: UFRC (ResNet-50 transfer learning, cost-sensitive focal loss, deep ensembles) reaches an AUC-ROC of 85.43%, and PANACEA (Teager-Energy cepstral features with gradient-boosted trees) reaches 76.31%. Sweeping ROC thresholds gives a family of (Se, Sp) pairs; combining with $\phi$ gives $p_i$ for every patron state. UFRC's ensemble-uncertainty tiering is directly reusable here: it lifts accuracy from 86% on high-uncertainty calls to 91% on low-uncertainty ones, so patrons arrive in three posterior tiers (screened negative, uncertain, screened positive) rather than two, and the allocator can place the uncertain tier rather than only gating it.
The third component is the allocation policy itself. With $T$ precomputed, the objective is quadratic in the assignment but cheap to evaluate (100 seats), so greedy insertion with local swaps, plus zone quotas derived from the emission-side column, suffices; no learning-based controller is needed and none should be trusted here. The policy's option set at each tier is {bar, seat anywhere, seat only in high-removal zones}, and the deliverable is a switching map over the $(\phi, \text{Sp})$ plane showing which option set is optimal — including the counterintuitive region where seating flagged patrons near exhausts beats barring them.
The fourth component adapts the certification machinery of ShiftBench, which shows that weighted conformal prediction false-certifies positive predictive value in 65–81% of boundary trials while a Maurer–Pontil empirical-Bernstein bound with Holm's step-down correction issues zero false certifications across 19,600 trials. We borrow the bound, not the setting: our "cohort" is a prevalence interval estimated from a finite surveillance sample, and our certified quantity is per-zone expected exposure rather than classifier PPV. This is a different mathematical object than their covariate shift (the prior $\phi$ moves, not the feature distribution), which is precisely why their machinery has never touched a physical domain — all 38 of their datasets are molecular, tabular, or text.
Baselines
The naive reference point is uniform seating at full capacity with no screening, under the theater's unfiltered-return-air configuration; Liang et al. report that infection probability stays below 0.1% only when masks and ventilation are in place, but no reported result found on Lacuna for the absolute unmitigated infection probability in that model, so we compute it ourselves from the validated surrogate and report it as the reference. The strongest existing competitor is the deterministic airflow-aware allocation of Liang et al. — staggered rows, maximal lateral distancing, which they report reduces maximum infection probability by 7.4–68.3% — combined with the door screen used as a hard gate at the UFRC operating point; this is the best any current method can do, since it is the only published policy that uses the airflow field at all. It will be run on the identical $T$ matrix, the identical classifier thresholds, and an identical tuning budget (grid search over distancing radius and gate threshold, matched to our policy's search over zone quotas and tier rules). Beating it means sitting strictly above it on the capacity-versus-expected-infections Pareto frontier at three or more prevalence levels, with the crossover prevalence located. Two further baselines isolate contributions: a screening-only policy (hard gate, random seating) and an occupancy-cap policy in the spirit of the compartmental model of Is “no test is better than a bad test”?, which caps headcount in a well-mixed room and so cannot see seat anisotropy at all. Finally, the key ablation runs our own allocator with posteriors collapsed to zeros and ones ($p_i \in \{0,1\}$), which removes exactly the Bayesian ingredient and leaves the geometry, the search, and the compute untouched; if the full posterior model does not beat this ablation, the core claim is wrong.
Why not just…?
Why not just improve the test's specificity? This is the real threat, and we treat it as such. Large-scale pancreatic cancer detection via non-contrast CT and deep learning shows near-perfect specificity is attainable in some domains — 99.9% specificity at 92.9% sensitivity across 20,530 consecutive patients, roughly one false positive per 1,000 tests — and at that specificity the posterior-weighting machinery adds little. But acute respiratory screening is nowhere near: the best cough-audio system sits at 85.43% AUC (UFRC), and the SIRQ analysis shows mass testing with specificity below roughly 0.98 is actively harmful (Is “no test is better than a bad test”?). Our experiments will settle the boundary honestly: we will map the (Se, Sp, $\phi$) region in which posterior-aware seating beats deterministic seating, and if that region excludes every operating point a realistic screen can reach, the conclusion is itself the finding.
Why not just seat everyone as if they might be infected? That policy is the deterministic baseline with maximal distancing: safe under any leak, but it buys safety only by emptying the room. Our comparison reports the capacity-at-equal-risk point for both policies; if worst-case distancing matches our policy's risk at, say, 70% of the capacity, the simple rule wins and we will say so. The expectation, grounded in the staggered-seating gain of 7.4–68.3% (Liang et al.), is that at moderate prevalence the posterior tiers let the room run fuller at equal risk because only the small uncertain tier needs dilution-maximal seats.
Why not just plug Bayes' rule into the existing seat map? The static plug-in is the obvious combination and we deliberately go past it for three reasons: it assumes $\phi$ is known exactly (surveillance gives an interval); it evaluates seats one patron at a time, ignoring that patron $i$'s risk depends on who is seated around them, which is the combinatorial structure our allocator handles; and it has no bar-or-seat decision, so it cannot discover the low-prevalence regime where seating flagged patrons in high-removal zones dominates barring them — an option no cited study considers. Our ablation with collapsed posteriors is exactly the plug-in shorn of these pieces, so the experiment separates the ingredients rather than arguing around them.
Why not just extend the compartmental epidemic model with a venue? The SIRQ framework of Is “no test is better than a bad test”? already couples test error to transmission, but it is zero-dimensional: everyone contacts everyone uniformly. A venue added as one well-mixed compartment cannot see that identical headcount differs by up to a factor of two in risk depending on seat orientation, because the lateral-versus-longitudinal asymmetry (84.9–92.3% versus 36.3–74.0% reductions, Liang et al.) is invisible to it. We include this as the occupancy-cap baseline; in fact our prevalence input could be driven by exactly such a compartmental model, which is a marriage rather than a rivalry.
Proposed Experiments
Experiment one validates the surrogate: the theater matrix must reproduce the published reduction ranges and the subway matrix the exhaust-proximity removal contrast before any policy claim is made. Experiment two is the main sweep: prevalence from 0.1% to 10%, classifier operating points drawn from the UFRC and PANACEA ROCs, all five policies run per cell, reporting expected infections per event, worst-seat probability against the 0.1% safety threshold, admitted-patron count, and falsely barred count. The decisive readouts are the Pareto dominance over the deterministic baseline, the location of the policy-switching crossovers, and the size of the gap to the collapsed-posterior ablation — the direct measurement of the screening–airflow interaction term. Scenario stress uses the couplings Wu et al. quantify: density from 2 to 4 persons/m² raises droplet trapping on bodies from under 20% to over 50%, and 35% relative humidity roughly doubles trapping versus 70%, so rush-hour and dry-winter cells test the policy where emission-side risk is most amplified. Experiment three tests certification: prevalence is estimated from a simulated surveillance sample of size $k$, the Maurer–Pontil empirical-Bernstein upper bound (per ShiftBench) feeds the allocator, and $\phi$ then drifts; the certified allocations must hold their per-zone exposure bounds while plug-in allocations with point estimates violate them at a measurable rate. A final transfer test runs the same policy structure, unchanged, on the warehouse geometry of Yang et al., where low-speed ceiling fans make breathing-zone concentrations worse than fans off — a regime in which the emission-side seats move and only a matrix-driven policy can find them.
References
- Is it Safe to Reopen Theaters During the COVID-19 Pandemic?
- Is “no test is better than a bad test”? Impact of diagnostic uncertainty in mass testing on the spread of COVID-19
- Numerical Simulation of Droplet Dispersion and Passenger Infection Risk Assessment in a Subway Carriage
- Comparing airborne infectious aerosol exposures in sparsely occupied large spaces utilizing large-diameter ceiling fans
- UFRC: A Unified Framework for Reliable COVID-19 Detection on Crowdsourced Cough Audio
- PANACEA Cough Sound-Based Diagnosis of COVID-19 for the DiCOVA 2021 Challenge
- ShiftBench: A Benchmark for Per-Cohort Certify-or-Abstain Decisions on Positive Predictive Value Under Covariate Shift
- Large-scale pancreatic cancer detection via non-contrast CT and deep learning