Blood and urine carry RNA released by tissues throughout the body, and sequencing that RNA could detect disease without a biopsy. The difficulty is that much of the variation between samples has nothing to do with the patient. It comes from how long a tube sat before processing, how cold it was kept, and which lab handled it. Standard fixes take a "batch" label, such as study site, and subtract everything that label explains. In international cohorts, though, site and ancestry are nearly the same variable: Asian patients are processed at one hospital and European patients at another. Subtracting site therefore also subtracts real population biology. Leaving site in lets a classifier learn the lab instead of the disease.
We propose to measure handling damage directly inside each sample, so that no site label is needed. Circular RNAs (circRNAs) are loops formed when a gene's exons are spliced end-to-back. Because they have no free ends, the enzymes in blood that chew RNA from its ends cannot digest them. The linear RNA copied from the same exons of the same gene has free ends and is digested. The ratio of linear to circular reads at a shared locus should therefore fall as a sample ages in a tube. That ratio is a per-sample degradation clock. A single sample-level degradation factor, estimated across hundreds of loci, can then be regressed out of every feature. Ancestry acts mostly gene by gene, so most of its biology should be untouched. The core claim is that correcting along this measured, mechanistically defined axis removes the handling artifacts that site-label correction targets while keeping the biology that site-label correction destroys when site and ancestry are confounded.
Core Claim and Mechanism
The biochemical premise is established, but nobody has turned it into a correction method. Exonucleases in blood degrade unprotected linear RNA within minutes (Noninvasive Visualization of RNA Delivery with 99mTc-Radiolabeled siRNA). Wet-lab work routinely exploits the resistance of closed loops by digesting samples with RNase R, an enzyme that removes linear RNA and spares circles. That was the confirmation step for circSEPT9 (circSEPT9 in triple-negative breast cancer), for circular lariats (Intron Lariat RNA in Arabidopsis), and for the RNase R-treated libraries used to benchmark circRNA detectors (A comprehensive overview and evaluation of circular RNA detection tools). These studies use the asymmetry once, at the bench, to confirm that a molecule is circular. We use the same asymmetry continuously, as an internal standard that reports how much exonuclease exposure each sample received.
Concretely, for locus $g$ in sample $s$, let $L_{gs}$ be reads spanning the linear forward-splice junction of the exons that also form the circle, and $C_{gs}$ the back-splice junction reads. We model
$$\log\frac{L_{gs}+1}{C_{gs}+1} = a_g + b_g\, d_s + \varepsilon_{gs},$$
where $a_g$ is the locus's baseline linear-to-circular balance, $b_g$ is how sensitive that locus is to degradation, $d_s$ is the sample's degradation index, and $\varepsilon_{gs}$ is count noise. This is a rank-one factorization fit with a count-aware likelihood. The low-rank structure is the point. Ancestry-linked differences in back-splicing, such as genetic variants that change splicing, enter through locus-specific shifts in $a_g$ and are not shared across hundreds of loci. Exonuclease exposure, by contrast, is one physical quantity per tube and should load on all loci together. Each ordinary expression feature $x_{js}$ (mRNA, long non-coding RNA, circRNA) then gets its own sensitivity to $d_s$, estimated by regression. That component is removed before any classifier is trained.
The falsifiable assumption is that, once handling is controlled, $d_s$ does not depend on ancestry. If it does, the method fails in exactly the confounded setting it targets. We test this assumption directly rather than assuming it.
This also addresses one specific shortcut. If case samples were systematically stored longer than controls, as is common when cases come from a clinic and controls from a volunteer drive, a classifier can learn degradation as disease. Removing $d_s$ removes that shortcut by construction. We will report it as a reason for apparent accuracy loss relative to naive models, not hide it.
Research Program
The work has three parts.
The first is a controlled degradation experiment that serves as ground truth. Pooled plasma from donors of at least two self-reported ancestries is split into aliquots and held at room temperature and at 4 °C for graded intervals before extraction. Matched aliquots are digested with RNase R as a positive control for circle enrichment. This tests three things: whether $d_s$ tracks known handling time monotonically, whether it is invariant to donor ancestry at matched handling, and how many loci and how much depth are needed to estimate it. Sparsity matters here. Extracellular RNA is low-abundance, with many missing reads (exoRBase 2.0), so we will derive the number of back-splice reads required. The estimator's variance should shrink roughly as one over the total pooled back-splice reads, because $d_s$ is a weighted average across loci.
The second part handles detection-tool dependence. Circular calls differ substantially across detectors, and some tools produce many false positives when linear reads are abundant (circRNA detection tools evaluation). That is precisely our regime, since degradation changes the linear background. We will restrict the clock to loci called by the consensus of CIRI2, CIRCexplorer and KNIFE, the three tools that evaluation found balanced. We will also verify that $d_s$ estimated under each tool separately agrees.
The third part is the correction and evaluation pipeline. We apply it to exoRBase 2.0, which uniformly reprocesses 905 extracellular-vesicle RNA samples from many studies and biofluids with STAR, CIRI2 and ASJA, but normalizes only by counts per million. The atlas has no ancestry metadata. We therefore build semi-synthetic confounding: we implant locus-specific "population" signals with known effect sizes into a subset of studies, so that the implanted group is fully confounded with study, and ask which corrections preserve them. This is weaker than a real multi-ancestry cohort, and we say so. A prospective multi-site collection with recorded ancestry and handling times is the intended follow-on, and the controlled experiment is designed to justify it.
Baselines
The naive reference is counts-per-million normalization with no batch correction, exactly as exoRBase 2.0 distributes the data, feeding a regularized logistic regression and a gradient-boosted tree classifier. It shows how much of the apparent cancer-versus-control accuracy is attributable to study identity. We expect that share to be large; samples clustering by lab rather than phenotype was documented long ago for microarrays (Cross-platform analysis of cancer microarray data).
The first strong baseline is empirical-Bayes site-label correction (ComBat) on log expression, followed by the same classifiers. It is the method most labs would actually use. Beating it means matching or exceeding its leave-one-study-out disease AUC while recovering the implanted population signal it removes. The criterion is recovered effect size within the confidence interval of the true implanted effect, where ComBat's recovered effect should collapse toward zero.
The second strong baseline is robust hyperparameter tuning. Following Improved Outcome Prediction Across Data Sources Through Robust Parameter Tuning, which found that tuning on an independent external study (their RobustTuneC) beats internal cross-validation across 15 microarray studies, we tune Lasso and boosting with a held-out tuning study. A separate test study avoids the "winner's curse" that paper warns about. This baseline is label-free with respect to batch, so it is the fairest comparison to our label-free index. That paper reports no exact per-dataset error rates in the file, so no reported result was found on Lacuna for RobustTuneC on liquid-biopsy data.
The third strong baseline is a learned conditional representation in the style of Exai-1 (A multimodal cell-free RNA language model for liquid biopsy applications). Exai-1 conditions a variational transformer on assay-version and biofluid tokens and reports masked-feature reconstruction $R^2$ of 0.89 against 0.57 for a dataset-average baseline, plus an AUC gain of 0.1 over raw features for ovarian cancer with 48 samples. Those numbers come from its own blood cohort, not from exoRBase. On exoRBase, no reported result was found on Lacuna for Exai-1 or any cross-study circRNA classifier. We will train a conditional variational autoencoder with study tokens at matched parameter count and tuning budget, and run a variant that receives our $d_s$ as a continuous token. All methods get the same splits, the same 50-trial hyperparameter search, and the same compute.
Two ablations isolate the key ingredient. The first replaces $d_s$ with the first principal component of all expression, an unsupervised nuisance factor with no circular/linear logic. The second computes the index from linear reads alone, using a 3′-to-5′ coverage-bias proxy. If either matches the full method, the circular-loop asymmetry is not doing the work.
Why not just…?
Why not just use ComBat with site labels? When site and population are confounded, ComBat cannot tell them apart, because it only sees the label. That is the failure Gap 2 of the literature describes, and the reason the critique of ccRCC models (Critical insights on AI-driven CcRCC prognostic modeling) attributes cross-ethnic failure to real baseline differences that need to be preserved. The implanted-signal experiment measures this loss directly. If ComBat recovers the implanted signal, our motivation is wrong for this data.
Why not just use circRNA features alone, since they are stable? This is the real threat. If circRNA-only classifiers transfer across studies as well as corrected all-RNA classifiers, the simpler answer wins and we will report it. Two reasons make us doubt it. First, most disease signal in cfRNA models sits in linear species (Exai-1). Second, circles resist exonucleases, not endonucleases, so they are not immune to handling. We run circRNA-only classifiers as a full baseline under identical tuning.
Why not just record storage time and processing delay as covariates? Where these metadata exist they are the best covariate, and in the controlled experiment we use them as ground truth. In pooled public data such as exoRBase they are almost never recorded, and actual exposure differs from logged time because of temperature and freeze–thaw cycles. Storage-condition studies show quality markers drift with conditions (Investigation of Storage Conditions and Quality Control Markers in Human Feces). The question is whether $d_s$ explains handling-driven variance beyond logged time, and the time-series design answers it.
Why not just use a domain-adversarial or distribution-matching aligner like scAdapt or BERMUDA? These methods force batches to overlap, either by fooling a classifier that tries to guess the batch (scAdapt) or by matching distributions between paired cell clusters (BERMUDA). Both rely on discrete cell clusters that cell-free RNA lacks, and both treat the batch as pure nuisance. Under confounding they should erase the implanted signal just as ComBat does. We include a domain-adversarial model on study labels to check this.
Decisive Checks
The method is supported if three conditions hold together. First, $d_s$ rises monotonically with handling time in the controlled experiment, with Spearman correlation well above that of the principal-component ablation, and shows no significant ancestry dependence at matched handling. Second, on exoRBase leave-one-study-out evaluation, the corrected classifier's AUC is not below ComBat's. Third, the corrected classifier recovers the implanted confounded population signal that ComBat and adversarial alignment remove.
We also report how well study identity can still be predicted from the corrected features, using a nonlinear batch classifier, k-BET and LISI from the BatchEval Pipeline. Residual study predictability is expected and acceptable, because study also carries biofluid and cancer-type differences. As a per-marker sanity check, we test whether single circRNA biomarkers reported from single centers, such as circSEPT9 with a diagnostic AUC of 0.711 (circSEPT9), keep their direction and size across exoRBase studies after correction.
The method is refuted in either of two cases. One is that $d_s$ is ancestry-dependent at matched handling. The other is that the linear-only or principal-component ablation does as well, which would mean the circular/linear asymmetry is not doing the work.
References
- Noninvasive Visualization of RNA Delivery with 99mTc-Radiolabeled Small-Interference RNA in Tumor Xenografts
- The circRNA circSEPT9 mediated by E2F1 and EIF4A3 facilitates the carcinogenesis and development of triple-negative breast cancer
- Intron Lariat RNA Inhibits MicroRNA Biogenesis by Sequestering the Dicing Complex in Arabidopsis
- A comprehensive overview and evaluation of circular RNA detection tools
- exoRBase 2.0: an atlas of mRNA, lncRNA and circRNA in extracellular vesicles from human biofluids
- Cross-platform analysis of cancer microarray data improves gene expression based classification of phenotypes
- Improved Outcome Prediction Across Data Sources Through Robust Parameter Tuning
- A multimodal cell-free RNA language model for liquid biopsy applications
- Critical insights on statistical consistency, generalizability, and feature optimization in AI-driven CcRCC prognostic modeling
- Investigation of Storage Conditions and Quality Control Markers for Metabolites and Lipids in Human Feces
- scAdapt: virtual adversarial domain adaptation network for single cell RNA-seq data classification across platforms and species
- BERMUDA: a novel deep transfer learning method for single-cell RNA sequencing batch correction reveals hidden high-resolution cellular subtypes
- BatchEval Pipeline: Batch Effect Evaluation Workflow for Multiple Datasets Joint Analysis