Rebalancing the Wrong Minority: Re-Positive Tests and Imbalance Correction

Some patients who have recovered from COVID-19 and been discharged later test positive again by RT-PCR, a test that amplifies viral genetic material. These "re-positive" patients are a small minority (5.7% of 420 recovered patients in one Wuhan cohort) and look like an ordinary rare-event prediction target. Standard machine learning practice for rare targets is to correct for class imbalance: upweight, oversample, or synthesize the rare class so the model stops predicting "negative" for everyone. The clinical literature suggests this is the wrong move. Most re-positive events seem to be harmless leftover genetic fragments rather than live virus or true relapse. When the rare class is mostly benign, imbalance correction teaches the model to find harmless shedders more aggressively, while the few clinically important cases stay buried inside the positive label.

We propose to state this failure mode precisely, show that existing imbalance and noise-robust methods do not fix it, and test a simple remedy. The remedy splits the observed positive label into a benign component and a clinically meaningful component. It uses information that only becomes available after the event (the test's cycle threshold, antibody status, culture results when they exist, symptoms, and imaging) to estimate how much each positive belongs to each component. Imbalance correction is then applied only to the meaningful component. The general lesson reaches beyond COVID: many medical rare-event labels are triggered by a test or by an administrative event and mix benign and serious mechanisms. Hospital readmission is one example, since it mixes planned and emergency returns. We use that case as a public benchmark where the split is actually recorded.

Core Claim

When a minority label is the union of a benign mechanism and a target mechanism, and the benign mechanism can be predicted from the same pre-event features, imbalance correction on the observed label reduces detection of the target mechanism. Under a fixed alert budget, it can do worse than no correction at all. Noise-robust imbalance methods do not help, because benign positives are not hard or randomly flipped examples. They are easy, consistent, feature-predictable positives.

The re-positive literature provides an unusually clean natural case of this. Zhao et al. show that the length of the initial RNA-positive period strongly predicts recurrence: the odds ratio is 1.05 per day, and 3.09 for more than 28 days versus less than 14 days. Meanwhile, Tan et al. find that all five re-positive patients they cultured grew no virus. Those patients had a mean Ct of 34.7 (range 32.95–38.63; the cycle threshold is the number of amplification rounds needed to detect virus, so higher means less virus) and 100% carried neutralizing antibodies. Put these together and the strongest learnable signal for "re-positive" may be a signal for slow clearance of non-viable RNA. A classifier tuned to that signal would flag the wrong people.

How This Differs From Prior Work

The clinical studies motivate the problem but do not pose it as a learning problem. He et al. report re-positive rates under rehabilitation interventions. Yang et al. show that seven re-positive patients had no fever, no progression, lower CT lung scores (P=0.030), and short readmissions. Wang et al. find blunted T-cell and NK-cell activation and an ID1-high/IFITM10-low transcriptomic pattern in re-positive patients. All of these treat "re-positive" as a single outcome. They use logistic regression, generalized additive models, or group comparisons, and none asks what a predictor trained on that outcome would learn. Reservoir studies (Chen et al., Chan et al.) add further evidence that RNA detection outlasts live virus. We take the biological claim that positivity is a mixture as given and ask what it does to learning.

Two strands of imbalance work constrain the method. The first is cost-sensitive and segmentation losses, such as the balance loss of Xu et al. (66.8 vs 59.8 Dice on KiTS19 kidney tumor segmentation), and generative oversampling, such as Red-GAN. These assume the minority label is the target. The second is the noise-robust ensemble of Liu et al. (DuBE), which stays stable up to 50% label noise where plain hard-example mining collapses past 20%. Its soft hard-example mining, however, downweights examples the model finds hard. Benign shedders with long initial shedding are easy positives, so we predict this mechanism will keep them rather than filter them. That prediction is testable, and it marks the specific difference from DuBE.

Longitudinal EHR models for post-discharge events are the natural backbone to compare against: CURENet and MuST (AUC 85.81% on MIMIC-IV readmission). Both train on the coarse label. Nothing in the file indicates they separate benign from serious mechanisms.

Research Program

Let $x$ be features available before the event (initial shedding duration, comorbidities, monocyte counts, discharge labs and notes). Let $z$ be mechanism evidence observed only at or after the event: retest Ct, serology, culture, symptoms, CT change, and for readmission, admission type. We assume the observed positive arises from a benign component $b$ or a target component $r$, so that

$$p(y=1 \mid x) = \pi_b(x) + \pi_r(x),$$

where $\pi_b$ and $\pi_r$ are the probabilities of each mechanism given $x$.

A small mechanism model $g(z)$ outputs, for each positive $i$, a responsibility $q_i \in [0,1]$: its estimated probability of belonging to $r$. Culture-confirmed cases anchor the model, and Ct and serology serve as soft priors where no culture was done. The deployable predictor $f(x)$ is then trained on

$$\mathcal{L} = -\sum_i \Big[ w\, q_i \log f(x_i) + (1-q_i)\log\big(1-f(x_i)\big) \Big],$$

where negatives have $q_i=0$ and $w$ is the imbalance weight. The imbalance weight applies only to responsibility mass on the target mechanism. Benign positives count as negatives for the target. This is learning with privileged information (features used in training but not at prediction time), here the $z$ features, combined with mechanism-specific reweighting. It deliberately uses one weight and no multi-stage schedule, avoiding the hyperparameter fragility the file notes for unified losses.

Three things will be built. The first is a public benchmark from MIMIC-IV in which the observed label is any 30-day readmission and the target is emergency readmission. The benign mechanism, elective returns, is recorded through admission type, so ground truth exists. The second is a re-positive simulator calibrated only to reported quantities: a 5.7% overall rate, the shedding-duration odds ratios and hypertension and monocyte interactions from Zhao et al., the Ct range from Tan et al., and 0% culture growth in the benign component. We vary the target fraction of positives from 0% to 50% and how predictable the benign mechanism is from $x$. The third is an analysis on real re-positive data. We will request the registries from Zhao et al. and He et al. and use the public PBMC transcriptomics (GSE166253) only as a feasibility check on whether immune features shift $q$. The numbers there (10 re-positive vs 6 convalescent sequenced) are far too small for model claims.

We state plainly that no public re-positive dataset with viability labels appears in the file. The real-data arm therefore depends on access or on a small prospective substudy with culture on a sample of re-positives.

Baselines

The naive reference is an unweighted gradient-boosted classifier (or logistic regression) trained on the observed label with no imbalance correction, using its alert threshold tuned on validation data. Many "imbalance problems" disappear once the threshold is chosen well, so the proposal has to beat this.

The clinical-statistics baseline is the multivariable logistic regression with spline terms on shedding duration specified by Zhao et al., refit on the same features. Its reported effect sizes (odds ratio 3.09 for more than 28 days) are associations rather than predictive metrics. The file reports no AUROC or recall for re-positive prediction, so there is no reported predictive result on Lacuna for this task.

The standard imbalance baselines are weighted cross-entropy, focal loss, random oversampling, and SMOTE, all on the observed label.

The strongest imbalance competitor is DuBE, the noise-robust ensemble. Its reported result is a 15.22% average improvement over eight ensemble baselines on UCI benchmarks, with stability up to 50% label noise. It is the strongest competitor because it is the one method that explicitly claims robustness to contaminated minority labels.

The strongest sequence model is MuST, which reports AUC 85.81% and accuracy 92.37% on all-cause MIMIC-IV readmission (78.32% AUC EHR-only). On the MIMIC benchmark we reimplement its EHR branch as a shared backbone and swap only the training objective. If the full multimodal pipeline is not reproducible, we report our reproduced all-cause AUC next to theirs.

The key ablations, all evaluated with our loss on the same backbone, are three: replace soft $q_i$ with a hard rule (Ct below 30 or culture-positive counts as target, everything else benign); set all $q_i=1$, which recovers ordinary reweighting; and give the mechanism model random $z$.

All methods use the same splits and feature sets. Each gets an equal hyperparameter search budget (the same number of trials over its own weight, focal, or sampling parameters) chosen on target-mechanism validation performance. That choice deliberately favors the baselines, since in practice they would be tuned on the observed label.

Beating a baseline means higher recall of the target mechanism at a fixed alert budget (top 5% of patients flagged) and better calibration for the target. The improvement must exceed the 95% bootstrap interval across five seeds, and the proposal must also beat the hard-rule relabeling.

Why not just…?

Why not just relabel with a Ct cutoff and then use any standard imbalance method? This is the real threat, and it is included as an ablation. The evidence against relying on it is that Tan et al.'s non-viable cases span Ct 32.95–38.63 around a commonly cited infectivity cutoff near 30. Many settings also lack Ct, serology, or culture for every positive, and a hard rule cannot use partial evidence. If hard relabeling matches the soft responsibilities in both the simulator and the readmission benchmark, we will report that the contribution is the diagnosis (label mechanism matters more than imbalance method) together with the relabeling rule, and drop the mechanism model.

Why not just use Zhao et al.'s logistic regression? For predicting the observed re-positive label it may be as good as anything, given cohorts of a few hundred. Our claim is not that it predicts re-positivity poorly. The claim is that it predicts the wrong thing well. The simulator experiment where the benign mechanism is driven by shedding duration will show whether its top-ranked patients are mostly benign. Logistic regression is also a valid backbone for our loss, and we will report it in that role.

Why not just use a noise-robust imbalance method like DuBE? DuBE's robustness is shown for injected noise on UCI benchmarks, and its soft hard-example mining targets examples with high error. Benign shedders are low-error positives, so we predict DuBE will keep them. If DuBE closes the gap in the experiment that sweeps how predictable the benign mechanism is, the hypothesis is wrong, and we will say so.

Why not just skip imbalance correction and tune the threshold? This becomes plausible when the target is a reasonable fraction of positives. We expect the gap to grow as the target share shrinks toward Tan et al.'s 0 of 5. The target-share sweep is designed to locate where, if anywhere, correction of any kind starts to matter.

Proposed Experiments

The decisive check comes first and runs on the MIMIC-IV readmission benchmark. We train every method on all-cause readmission and evaluate on emergency readmission, asking whether weighted cross-entropy, focal loss, SMOTE, and DuBE reduce emergency-readmission recall at a 5% alert budget relative to the uncorrected model. We also ask whether mechanism-aware training reverses that loss. Metrics are target recall at the fixed budget, target AUPRC (area under the precision-recall curve), the fraction of alerts that are benign, and the calibration error for the target.

The second experiment sweeps the simulator over target share and benign predictability. The prediction is a crossover: standard correction helps when the target dominates positives and hurts when benign positives are frequent and predictable from $x$. The position of the crossover against the reported cohort parameters indicates where real re-positive data likely sits.

The third experiment, conditional on registry access, repeats the comparison on real re-positive cohorts. It uses whatever mechanism evidence exists (Ct, serology, symptoms, CT) to form $q$, and reports which features the deployable model relies on with and without mechanism-aware training. The specific falsifiable expectation is that initial shedding duration loses importance and markers of impaired immune activation gain it once benign mass is removed from the target. Wang et al.'s findings point to activation markers, the IMPACC subtype work (IMPACC) points to slow-clearance endotypes, and shedding duration is what Zhao et al. identify. A null result here, with the model unchanged after relabeling, would argue that on real data the benign and target mechanisms are not separable from pre-event features, and that would itself be worth reporting to anyone building rare-event alerts from test-triggered labels.