Count-Level Uncertainty for Graded ctDNA Staging in Small Cohorts

Droplet digital PCR (ddPCR) splits a blood-derived DNA sample into about 20,000 tiny oil-wrapped droplets, amplifies each one, and counts how many light up. From that count, Poisson statistics give an absolute number of tumor DNA copies without any calibration curve. Clinical studies then routinely discard most of this information. They reduce each sample to "circulating tumor DNA (ctDNA) detected or not," or to "above or below the cohort median." For the highest-stakes calls, such as whether a patient has cleared tumor DNA after surgery or after eight weeks of therapy, the decision often rests on whether zero, one, or three droplets out of thousands fluoresced. A sample with zero positive droplets from a small DNA input is weak evidence of clearance. A sample with zero positives from a large input is strong evidence. Binary calls treat these two cases as identical.

We propose to model the raw droplet counts directly. A hierarchical Bayesian model would carry each sample's counting uncertainty forward into a graded, ordinal disease-burden stage. It would pool information across related mutations so that rare variants are not analysed in isolation. It would also abstain explicitly when the evidence cannot separate adjacent stages. The claim is narrow and testable. In small cohorts, and specifically in the low-count regime near the detection limit, keeping track of how much evidence each count represents should produce risk stages that are better calibrated and that transfer between cohorts better than binary calls, median splits, or plug-in continuous allele fractions. Elsewhere, we expect no gain.

Core Claim

Three bodies of evidence motivate the claim. First, continuous ddPCR abundance carries signal that the binary call destroys. In papillary thyroid cancer, Ni et al. found that BRAF V600E presence or absence was not associated with aggressive behaviour. Cellularity-adjusted ddPCR abundance, by contrast, was an independent predictor, and a gradient-boosted model fusing that abundance with clinical features reached an external AUC of 0.82. Second, the downstream literature still dichotomizes. Till et al. median-split KRAS ctDNA and scored clearance as detected versus undetected. The TriMeth gastric cohort of Iden et al. used binary methylation calls. The colorectal liver metastasis study (CRLM cohort) used binary postoperative status. Third, the clinically decisive time points are exactly where counts are sparse. Postoperative positivity was 15% in the gastric cohort, about 13 patients. Clearance in the pancreatic cohort is by definition a statement about counts near zero.

What would be new is the following chain. The model links each sample's binomial droplet likelihood to a latent tumor fraction. It links that latent fraction to an ordinal stage and a survival hazard. Every layer is fitted jointly, with partial pooling across mutation types and an abstention rule driven by the posterior. None of the cited studies propagates counting uncertainty into the prognostic model. Ni et al. come closest, but they feed a point estimate of abundance into XGBoost.

The Model

For sample $i$, let $k_i$ be the number of positive droplets for the mutant probe, $N_i$ the number of accepted droplets, $v$ the droplet volume, and $c_i$ the mutant concentration in copies per microlitre. The physics of partitioning gives

$$k_i \sim \mathrm{Binomial}\!\left(N_i,\; 1 - e^{-c_i v}\right),$$

which is the likelihood behind the standard estimate $\lambda = -\ln(1 - k/N)$. We write $c_i = f_i G_i$, where $G_i$ is the total genome-equivalent concentration from the wild-type or reference channel, itself modelled with its own count likelihood, and $f_i$ is the latent tumor fraction. Outcome enters through a proportional-hazards term,

$$h_i(t) = h_0(t)\exp\!\left(\beta_{m(i)} \log f_i + \gamma^\top x_i\right),$$

where $m(i)$ indexes the mutation (for example KRAS G12D versus G12V), $\beta_m$ is its prognostic slope, and $x_i$ are clinical covariates.

Two further pieces complete the model. The slopes $\beta_m$ share a hierarchical prior, so a small G12V subgroup borrows strength from G12D without being forced to equal it. The ordinal stages are defined on $\log f$: confidently cleared, below detection but uninformative, low burden, and high burden. Their boundaries are learned from outcome in one cohort and then frozen. A sample whose posterior over $f_i$ puts substantial mass in two stages is reported as "indeterminate, re-draw or increase input" rather than forced into a stage. This mirrors the abstention layer of DeepTag, where routing the most uncertain 10% of veterinary notes to humans raised accuracy on the rest. Here the uncertainty has a physical source, the droplet count, rather than coming from a learned confidence head.

For longitudinal data such as the day-7, 14, 21 and 60 draws of Lyskjær et al., $\log f_i(t)$ gets a per-patient random-walk prior. This lets a transient surge be distinguished from counting noise. That distinction matters: the surges in 7 of 24 patients were what predicted early failure ($p=0.01$).

Research Program

The work has three parts. The first is a simulation study grounded in the binomial partitioning model. It varies cfDNA input, droplet yield, true tumor fraction and cohort size from 15 to 130. It maps where counting uncertainty actually changes stage assignments, and where it is negligible. That second region, high-count samples, is where we predict no benefit.

The second part is a reanalysis of real cohorts at the droplet-count level. The data come from the PRINCE (N=129) and standard-of-care (N=85) pancreatic cohorts of Till et al., the 229-sample gastric cohort of Iden et al., the 439-sample liver-metastasis cohort, and the 24-patient FOLFIRI cohort. This requires per-well $k$, $N$ and input volumes from the original groups. These are routinely exported by ddPCR software but are not reported in the papers, so data-sharing agreements are a precondition and the main practical risk. The two pancreatic cohorts are the priority because they provide a natural cross-cohort transfer test.

The third part is a small-cohort stress test. We repeatedly subsample the larger cohorts to N=25 and N=50 to emulate the studies that dominate this literature. One example is the 25-patient biliary trial of Monge et al., whose arms of 6 to 17 patients produced uninformative intervals. We then measure how often each method's stage boundaries and hazard ratios replicate in the held-out remainder.

We deliberately leave out droplet-image analysis. I2ddPCR classifies individual droplets at 99.05% accuracy, but only on nine seahorse-gene samples. Its contribution is upstream of ours. If a per-droplet misclassification rate is available, it can enter as a false-positive rate in the binomial likelihood, but the proposal does not depend on it.

Baselines

The naive reference point is the clinical standard: a binary detected/undetected call using each study's own positivity rule, entered into a Cox model with the same covariates. This is what Iden et al. and the liver-metastasis study report. In those settings it yields large effects, a postoperative RFS hazard ratio of 6.22 in the gastric cohort and a recurrence hazard ratio of 4.0 in the liver cohort. Any graded scheme must at least match these within the same data. The second simple baseline is the median split of Till et al. In PRINCE it separated median OS of 6.4 versus 18.1 months for G12D (log-rank $p=0.0010$). Week-8 G12D clearance separated 19.0 versus 7.6 months ($p=0.0002$). We would re-derive the median in a training cohort and apply it unchanged to the other cohort, since the median's dependence on the cohort is the weakness we are testing.

The strongest existing method is continuous abundance fed into a flexible learner, following Ni et al.'s fusion model, which reached an external AUC of 0.82 on the thyroid task. We run two versions on identical splits, covariates and tuning budget: XGBoost and a penalized Cox model on $\log(\hat f + \epsilon)$, with $\epsilon$ tuned by nested cross-validation. The second is the most dangerous competitor, because it is cheap and already continuous.

The key ablation keeps our full hierarchical and ordinal structure but replaces the count likelihood with the plug-in point estimate $\hat f_i$. Any gain that survives this ablation is attributable to modelling counting uncertainty. A gain that disappears means the benefit came from pooling or ordinal structure alone. A second ablation removes pooling across mutations, which isolates the G12V question.

Beating the baselines means two things. Cross-cohort calibration of stage-specific survival improves, measured by integrated calibration error of predicted versus observed one-year survival when trained on PRINCE and tested on the standard-of-care cohort. Discrimination is not worse, measured by Harrell's C-index. There is no reported C-index or calibration result found on Lacuna for any of these ddPCR cohorts, so all baseline numbers on these metrics will be produced by us under the shared protocol.

Why not just…?

Why not just enter log allele fraction as a continuous covariate? This is the real threat. For samples with dozens of positive droplets, the point estimate is precise and our model should reduce to it. The argument depends on the low-count stratum, where $\log(\hat f+\epsilon)$ is dominated by an arbitrary $\epsilon$ and every zero-count sample is treated as equally cleared. The plug-in ablation tests this directly. We will report results separately for samples with $k \le 3$ and $k > 3$. If the plug-in model matches ours in the low-count stratum, the proposal's central claim fails, and we will say so.

Why not just use a published cutoff, such as Ni et al.'s 0.167 abundance threshold? A fixed cutoff is transferable in a way a median is not. However, it is still a point decision on a noisy estimate, and it encodes no notion of insufficient evidence. In Ni et al. the cutoff is also tied to cellularity-adjusted tissue abundance in thyroid, not plasma. The comparison will apply the cutoff learned in one pancreatic cohort to the other and count the samples whose posterior straddles it. Those are the patients for whom a hard cutoff is a coin flip.

Why not just move to broad sequencing panels? Panels address the single-marker blind spot that Lyskjær et al. documented, where an unmonitored subclone expanded while the tracked mutation cleared. Our method does not fix that. But fragment-level models such as FLDL trained on 4,394 samples, which is not the regime of most ddPCR studies. Lyskjær et al. also note that targeted sequencing coverage was too low for confident low-frequency calls. The two approaches are complementary. Multi-probe ddPCR fits naturally into our pooled-slope structure, and clonal escape remains an acknowledged limitation.

Why not just abstain using a learned confidence score? One could train a classifier and defer its least confident cases, as DeepTag does. With 24 to 130 patients, learned confidence estimates are themselves unstable. The ddPCR count gives a physically derived uncertainty for free. We will compare deferral by posterior stage-overlap against deferral by the predictive-probability margin of the plug-in XGBoost model, at matched deferral rates of 10% and 20%.

Decisive Checks

The first check is cross-cohort transfer between the two pancreatic cohorts. We freeze stage boundaries learned on PRINCE and evaluate calibration, C-index, and stage-wise survival separation on the standard-of-care cohort. This is a stronger version of the replication Till et al. reported qualitatively.

The second check is the G12V question. If pooling yields a posterior for $\beta_{\mathrm{G12V}}$ concentrated near zero with an interval excluding the G12D slope, the variant difference is biological. If the interval is wide and overlaps, the reported null ($p=0.7101$) was plausibly underpowering. Either answer is informative.

The third check is the subsampling experiment. At N=25 and N=50, across 500 resamples, we measure the variance of stage boundaries and the rate at which each method's hazard ratio sign and significance replicate in the held-out remainder. The proposal succeeds if the count-level model is both more stable and better calibrated, and if the gain concentrates where the simulation predicts: low input, low counts, and the clearance time points. If gains appear uniformly across count levels, we would suspect leakage from the pooling or ordinal structure rather than from measurement modelling. The plug-in ablation is there to catch exactly that.