Certified Pool Sizing: Bounding Missed Infections per Subgroup When Pooling Dilutes Weak Samples

Pooled testing mixes several people's samples into one test so that a lab can screen many people for the cost of a few tests. It has a physical weakness. Each added negative sample dilutes the virus from a positive one, so a person carrying little virus can drop below what the assay can detect and be reported negative. Machine-learning triage systems now decide who gets pooled, and they make this worse in a way that is easy to miss. They send people whom they judge unlikely to be infected into large pools. But being judged unlikely to be infected is not the same as being safe to dilute. Some groups that are rarely infected, such as people screened without symptoms, tend to carry less virus when they are infected. These are exactly the people whose infections a large pool erases. A system can report an acceptable average false-negative rate while missing a large share of infections in one identifiable group.

We propose a way to choose each person's pool size, from individual testing up to a large pool, that comes with a statistical guarantee. With high probability over the calibration data, the fraction of infections missed after pooling stays below a target in every predefined subgroup, and the pipeline uses as few tests as that guarantee allows. Two estimated pieces make the guarantee possible. The first is a curve giving the probability that a pool of size $k$ detects an infected person with a given viral load. This curve is wrapped in a simultaneous confidence band: an envelope that contains the whole true curve with stated probability, not just its value at chosen points. The second is a subgroup-level calibration step borrowed from conformal prediction. The point at which pooling stops paying off then falls out per subgroup, as a consequence of the policy, rather than being a single population-wide prevalence cutoff.

Core Claim

The quantity a pooled-testing pipeline should control is the post-pooling miss rate for each group. It depends on two things: how likely people in the group are to be infected, and how much virus the infected ones carry. Existing work controls one of these at a time. Smart pooling uses gradient-boosted risk scores on patient metadata to keep high-risk people out of pools. That raises the prevalence at which pooling stays efficient from about 30% to 50%. Its error control, however, is a single wet-lab false-negative bound of about 5.4% at pool size 10, with no breakdown by subgroup or by viral load.

Semi-quantitative group testing models dilution as a shift in the cycle threshold, written $Ct$: the number of amplification cycles before the virus is detected, where higher means less virus. The model is $Ct_{\text{group}} \approx Ct_{\text{individual}} + M\log_{10}(g)$ for group size $g$. The authors fit a parametric sigmoid for false negatives but give no uniform uncertainty around that curve and no subgroup guarantees. Density-Dependent Group Testing proves that the detection curve's shape near zero concentration decides whether pooling is worthwhile at all. It assumes that curve is known.

Conformal Triage for Medical Imaging AI Deployment is the closest method in spirit. It uses the Learn-then-Test procedure, which picks decision thresholds by running a sequence of statistical tests with controlled overall error, to certify predictive values for single CT scans. Its errors are observed directly. Ours depend on what a sample would have done in a pool size that was never run. Our claim is that a certificate on the full detection curve can be combined with group-conditional risk control to certify pool sizes that were never observed in calibration. We expect this to recover most of the throughput that conservative fixed pool sizes give up.

Research Program

Detection probability as a conditional CDF. We work with the effective post-pooling cycle threshold $u = Ct + M\log_{10}k$ and define the pooled detection probability as

$$s(u) = \mathbb{P}(Ct_{\text{pool}} \le L \mid u),$$

where $L$ is the assay's detection cutoff. This is a conditional cumulative distribution function evaluated at a fixed point. lpcde estimates exactly this kind of function, with three features that matter here. It adapts at the boundary of the data, which is the high-$Ct$ end where misses happen. It corrects smoothing bias so the intervals are not shifted. And it supplies uniform bands, not just pointwise ones. We use it to produce a lower band $\underline{s}(u)$ that lies below the true $s$ for all $u$ at once, with probability $1-\delta_1$. A multiplier-bootstrap version is a secondary estimator.

The single index $u$ ties every pool size to one curve. We test whether that tie holds, because it is the assumption that lets us extrapolate to pool sizes not used in calibration. We also relax it by letting $M$ vary with $k$.

A certified miss rate per group. Let $\pi_G$ be the infection rate in group $G$, and let $P_G$ be the distribution of individual $Ct$ among infected members of $G$. These $Ct$ values are known from individual confirmatory tests. For a policy $k(x)$ that maps a person's covariates to a pool size, the miss rate in $G$ is

$$\text{FNR}_G(k) = \mathbb{E}_{Ct \sim P_G}\big[\,1 - s(Ct + M\log_{10}k(x))\,\big].$$

This treats the worst case of one positive per pool, so it is conservative when pools contain several positives. Replacing $s$ with $\underline{s}$ and estimating the expectation over calibration positives gives a quantity that upper-bounds the true miss rate on the band event.

Calibrating the policy. The policy assigns each person the largest pool size whose predicted miss contribution stays below a threshold $\lambda(x)$. That contribution is predicted risk times $1-\underline{s}$ at the person's predicted $Ct$. The threshold is a linear combination of group indicators, following the BatchGCP parameterization, which fits such combinations to give coverage in many overlapping groups at once.

We calibrate $\lambda$ on a grid using Learn-then-Test. Each group's certified miss rate is tested against the target $\varepsilon$, with a Bonferroni correction across groups and with the band failure probability $\delta_1$ included. The result is that, with probability at least $1-\delta_1-\delta_2$, every group satisfies its target. Among policies that pass, we choose the one with the fewest expected tests, using the Dorfman cost: $1/k$ per person for the pool, plus individual retests when a pool is positive.

A group whose certified policy collapses to $k=1$ has crossed its own pooling efficiency threshold. We report that point per group as a function of prevalence. It is the dilution-aware, subgroup-local counterpart of the population-level ceilings reported by Liu et al. (about 10%) and Ng et al. (about 17%).

Data selection: the hardest constraint. Under Dorfman testing, a negative pool is never broken apart. Its missed positives are therefore never seen, and naive estimates of $s$ are biased upward. The band can only be fit honestly on records where individual and pooled results both exist for the same sample, or on deliberate dilution series. We will audit the data sources for this before anything else. A biased $s$ would silently break the guarantee, and no amount of calibration downstream can repair it.

Baselines

The naive reference is a static, dilution-compensated pool size applied to everyone. We use $k=6$, as in the Shenzhen chlamydia screening study, which reported 96.7% sensitivity at that size. We also run classical Dorfman with the pool size that is optimal for the measured prevalence. These show what simple rigidity costs in tests and what it hides about subgroup misses.

The strongest existing triage method is Smart Pooling. We retrain its gradient-boosted risk model on the same training split and tune its routing cutoff $T$ on the same calibration split, with the same hyperparameter search budget as our risk model. Pooled survivors use its fixed pool size of 10. Its reported operating point is 0.36 expected tests per specimen at 5% prevalence, with an estimated false-negative upper bound of about 5.4% at pool size 10 (Smart pooling). We beat it if either of two things holds. Our method could match its tests per specimen within 0.03 while bringing every group's miss rate under $\varepsilon$ in cases where Smart Pooling's worst group exceeds $\varepsilon$. Or it could use fewer tests at equal worst-group miss rate.

The strongest dilution-modeling method is semi-quantitative group testing. It reports 24% fewer tests than standard pooling on the Israeli data and an optimal pool size of 15 at 2% prevalence (SQGT). We run it with its parametric sigmoid fitted on our calibration split. This comparison isolates what group conditioning and uniform bands add over a good dilution model alone.

Group-pessimal calibration takes the most conservative per-group threshold and applies it to everyone. Batch Multivalid Conformal Prediction showed that this choice inflates prediction sets. We expect it to push most people into individual testing.

Four ablations isolate the ingredients. The first replaces $\underline{s}$ with pointwise lower intervals. The second replaces the nonparametric band with a parametric-bootstrap band on the sigmoid. The third replaces group-conditional calibration with a single marginal threshold. The fourth drops the $Ct$ term so that triage ranks by infection risk alone. That last version is our pipeline with the viral-load ingredient removed, and it is the cleanest test of the core claim.

Why not just…?

Why not just run Learn-then-Test on observed false negatives per group, with no dilution curve? Where calibration data contain the exact pool size being certified, along with resolved individual outcomes, this is a legitimate competitor and may match us. We will run it in that setting and report it honestly. It cannot certify pool sizes absent from calibration, though, and those are the large, efficient pools the policy wants to use. It also inherits the problem that misses in negative pools go unobserved. The decisive comparison is a held-out pool size: we calibrate both methods without $k=12$ or $k=15$ and evaluate realized subgroup miss rates at those sizes.

Why not just fit the parametric sigmoid and plug it in? This is the most serious threat. If the $Ct$-shift sigmoid is well specified, a parametric band will be narrower than a nonparametric one and equally valid. Our argument for the nonparametric band is robustness near the detection limit. That is where curve shape decides whether pooling is viable at all, according to Density-Dependent Group Testing. It is also where a sigmoid fitted across all $Ct$ values may bend the wrong way. The parametric-band ablation settles this question. If the sigmoid band attains nominal subgroup coverage on real paired data at lower test cost, we will adopt it as the default and keep the nonparametric band as a misspecification check.

Why not just recalibrate Smart Pooling's probabilities per group, or use one conformal threshold per group? Per-group recalibration fixes errors in predicted infection risk but still ignores viral load. A group with well-calibrated infection risk and low loads is still over-diluted. Separate per-group thresholds also fail for overlapping groups and thin out small groups, which is the problem of conditioning on too much. The risk-only ablation tests the first point. The comparison of BatchGCP-style thresholds against separate per-group thresholds, on intersecting groups, tests the second.

Proposed Experiments

Main experiment. No dataset in the file is known to pair rich patient covariates with individual and pooled $Ct$ values. The main experiment is therefore semi-synthetic, and we say so plainly.

Covariates and infection labels come from the Bogotá patient cohort (2,068 samples with symptoms, travel history and comorbidities) and the test-center cohort (7,162 samples with location and timing). These are the Smart pooling data. Individual $Ct$ values for infected people are drawn from the empirical viral-load distribution of the 133,816-test Israeli dataset (SQGT). The detection curve is fit on Israeli records where pooled and individual results are paired.

We inject covariate-dependent load shifts, for example by making asymptomatic infected people carry higher $Ct$, and the size of the shift is the main stress variable. Prevalence is swept across 2%, 5%, 10%, 25% and 50%, extending the 10,000-person simulation design of the SQGT paper. Groups are symptom status, age bands, clinic location and their intersections.

Metrics. We report expected tests per specimen, the worst-group post-pooling miss rate, and the fraction of 200 random calibration and test resplits on which any group exceeds $\varepsilon$. That last number should stay at or below $\delta_1+\delta_2$. We also adapt the ERT diagnostic, which trains a classifier to predict when an uncertainty method fails, using a missed-infection indicator as the target. A LightGBM classifier tries to predict misses from covariates, which checks for violations in groups we did not specify.

Decisive checks. Three outcomes would decide the claims.

  1. On the Israeli paired records, the single-index curve fit at small $k$ should predict detection at held-out large $k$ inside the band. If it does not, the extrapolation claim fails.
  2. Under injected load shifts, the risk-only ablation should violate the worst-group target while the full method holds it. If both hold it, the viral-load term adds nothing.
  3. The full method should use fewer tests per specimen than the fixed-$k=6$ and group-pessimal baselines at equal worst-group miss rate. If it does not, the certificate is too conservative to be worth its complexity.

On the clean Dorfman synthetic benchmark of Density-Dependent Group Testing ($n=5{,}000$), we also check that when the true curve is $\rho^\alpha$ with $\alpha \ge 1$, the certified policy chooses individual testing everywhere. That is the regime where the theory says pooling cannot help.