Is a bulk ceRNA edge real, or is it just stroma?

Many cancer papers claim that a long non-coding RNA (lncRNA) "sponges" a microRNA and so switches on a gene that drives tumor metabolism. A microRNA is a short RNA that silences target genes, and a sponge is another RNA that soaks up the microRNA and frees those targets. Most of these claims rest on one kind of evidence: the lncRNA and the target gene rise and fall together across a cohort of bulk tumor samples, which are ground-up tissue averaged over millions of cells. In a tumor like pancreatic cancer, where fibroblasts and immune cells often outnumber cancer cells, two transcripts that are both made mainly by cancer cells will correlate across patients simply because patients differ in how much of the sample is tumor. No microRNA is needed. This note proposes to measure how much of the published bulk evidence for this "competing endogenous RNA" (ceRNA) mechanism survives once tissue composition is removed, and to build a test that asks the right question: do the two transcripts co-vary within one cell type, beyond what composition explains, with the uncertainty of the unmixing step carried through to the final pathway conclusions.

The testbed is metabolic reprogramming in pancreatic ductal adenocarcinoma (PDAC). Here a real mechanism exists: the lncRNA SNHG12 sponges miR-199a-5p to stabilize HIF1α, the master switch for hypoxic glycolysis (Overexpression of SNHG12 regulates the viability and invasion of renal cell carcinoma cells through modulation of HIF1α). Here too, aggressive glycolytic tumor states have been separated from stroma by unmixing bulk data (Clinically impactful metabolic subtypes of pancreatic ductal adenocarcinoma (PDAC)). The work will build a benchmark and a test, then re-audit published networks. It is an audit-and-correction study, not a new predictor.

Core Claim

We claim that, in stroma-rich tumors, a large share of lncRNA–mRNA pairs reported by standard bulk ceRNA pipelines is explained by between-patient variation in cell-type proportions. We further claim that a compartment-resolved test with propagated uncertainty removes these artifacts while keeping planted true interactions. The part that is not already done is the combination of three things: a ground-truth benchmark in which composition-driven correlation and within-cell covariation can be switched on and off independently; a test defined on the cancer-cell compartment, not on the bulk sample; and a check on the downstream pathway analysis. That last check asks whether the "oncogenic" enrichments reported for bulk ceRNA targets, such as the TGF-β enrichment in Identification of a competing endogenous RNA network associated with prognosis of pancreatic adenocarcinoma, are fibroblast signatures leaking through.

The closest existing work does not do this. LnCeCell 2.0 catalogs 836,581 cell- and spot-specific ceRNA interactions from single-cell and spatial data, but it is a lookup resource. It does not test interactions in bulk clinical cohorts, and it never asks how often bulk calls are compositional. The PDAC metabolic-subtype study unmixed tumor from stroma with DeMixT, but it looked only at protein-coding metabolic genes and ignored non-coding regulators. The bulk ceRNA papers for pancreatic cancer and for osteosarcoma (Development and analysis of long non-coding RNA-associated competing endogenous RNA network for osteosarcoma metastasis) never unmix at all.

The Test

For sample $i$, the bulk level of gene $g$ is modeled as $y_{gi} = \sum_k \pi_{ik} x_{gik} + \epsilon_{gi}$. Here $\pi_{ik}$ is the fraction of cell type $k$ in the sample, $x_{gik}$ is that cell type's per-cell expression of $g$ in that sample, and $\epsilon_{gi}$ is measurement noise. A ceRNA claim is a claim about the malignant compartment $k = T$: across patients, the lncRNA's $x_{\ell iT}$ should predict the target mRNA's $x_{miT}$, and the effect should shrink when the shared microRNA is abundant. It is not a claim about $y_{\ell i}$ and $y_{mi}$.

We estimate sample-specific malignant-compartment expression with DeMixT, as in the PDAC subtype study. We also run a multi-cell-type version that regresses bulk expression on estimated proportions and their interaction with the candidate regulator.

Uncertainty from the unmixing step enters in two ways. The first follows the argument of Statistical inference for cell type deconvolution (MEAD), which shows that treating estimated proportions as known inflates false positives; we use sandwich-type variance for the proportion-driven terms. The second follows SCDC: we re-estimate with different single-cell references, so that the choice of reference atlas counts as a source of error. The microRNA dependence enters as an interaction term, in the same spirit as the conditional mutual information of JAMI, but applied to compartment-level estimates.

A final coarse plausibility filter uses single-cell counts from the 3CA atlas. It asks whether the lncRNA reaches a per-cell abundance in malignant cells that makes titration of the microRNA physically possible. This is the stoichiometric objection raised in the ceRNA literature, and it is almost always ignored.

Pathway analysis of the surviving targets uses a compartment-matched background, meaning only genes expressed in malignant PDAC cells, which avoids the background bias described in Assumptions about frequency-dependent architectures of complex traits bias measures of functional enrichment. Each gene is weighted by the confidence of its interaction and not admitted by a hard cutoff.

Research Program

The first component is the benchmark, which is the main deliverable. We build pseudobulk samples from 3CA PDAC single-cell data, with fibroblast, immune and malignant fractions sampled to match the purity range seen in TCGA PAAD.

In the null version, we shuffle each gene's values across cells within each cell type. This keeps every cell type's average profile but destroys any within-type covariation, so every bulk correlation that remains is compositional by construction.

In the planted version, we add a synthetic ceRNA effect inside malignant cells only. The effect is placed on chosen lncRNA–metabolic-gene pairs such as HIF1A, HK2, PDHK and glycogen-catabolism genes, at graded strengths, and it is modulated by a simulated microRNA level. A second variant plants the effect only in cells labeled as the M2 glycolytic state, because M1 and M2 states coexist in single tumors.

A third variant tests a known weakness of the unmixing methods. We deliberately remove a cell state from the reference to see how an incomplete atlas, which POPPY's authors flag as a limit (Cross-modal transfer learning for mapping bulk transcriptomes at cellular level), leaks into false edges. On these data, a method's false-positive rate under the null and its power under the planted version are known exactly.

The second component is the real-data audit. We rerun the published PDAC ceRNA pipeline on TCGA PAAD (178 samples) with GTEx normal pancreas, and the osteosarcoma pipeline on GSE39040 and GSE39055. We then record which published edges and which enrichment terms survive the compartment-resolved test.

The third component asks whether the metabolic biology changes. Specifically, do any lncRNA–microRNA–metabolic-gene axes survive and differ between the M1 and M2 malignant states? For any that do, the application is bulk cohorts with outcome data.

Baselines

The naive reference point is the standard bulk pipeline exactly as published in the PDAC ceRNA paper. That pipeline finds differential expression with edgeR, builds co-expression modules with WGCNA, filters candidate pairs through miRcode, starBase and miRDB, and runs GO and GSEA on the targets. It is the method whose conclusions are in question. We run it unmodified on the same pseudobulk and real cohorts, and its null false-positive rate on the benchmark is the quantity to beat. The file gives no reported false-positive rate for bulk ceRNA calls; no reported result was found on Lacuna for this. For context only, that paper reports a 14-mRNA classifier with time-dependent AUCs of 0.719, 0.806 and 0.794 at 1, 3 and 5 years on TCGA, and AUCs "consistently exceeding 0.60" on ICGC. Those AUCs measure prognosis, not whether the edges are real.

The strongest existing inference method is conditional mutual information via JAMI, which conditions lncRNA–mRNA dependence on the microRNA. It is the most principled bulk ceRNA test in the file, but it does not condition on composition. We run it on the same inputs, with permutation significance at the same false discovery rate target. Beating it means lower null false-positive rate at equal or higher planted-edge recall.

The most dangerous competitor is simple covariate adjustment. This means partial correlation, or a regression with an interaction term, computed on bulk expression while adjusting for estimated tumor purity and cell-type proportions. It gets the same proportion estimates and the same microRNA term as our method, so the only difference is that it works on bulk values and treats the estimated proportions as fixed. We regard the proposal as justified only if it beats this baseline in the regimes the theory predicts. Those regimes are low purity, per-cell expression that shifts with cell state (the M2-only planted version), and references with missing states.

Three ablations isolate the key ingredients. The first uses plug-in proportions with no uncertainty propagation, which tests MEAD's argument inside this setting. The second uses a single reference, not the SCDC-style set, which tests how much reference choice matters. The third removes the stoichiometric filter. For the unmixing step itself, the best figure reported in the file is SCDC's Pearson correlation of 0.991 with ground truth on a controlled 6:3:1 cell-line mixture. That is an upper bound on unmixing quality under ideal conditions, not a ceRNA result.

Why not just…?

Why not just adjust for tumor purity? This is the real threat, and the experiments are designed to settle it. If per-cell expression were constant within cell types, adjusting bulk data for proportions would remove most compositional correlation, and our method would add little. The prediction is that it fails in two situations: when the metabolic state of the malignant cells itself varies with composition, as with hypoxic, stroma-dense regions and coexisting M1/M2 states, and when proportions are estimated with error, which is MEAD's point. The planted-state and missing-reference benchmark variants measure exactly this. If adjustment matches our method across these variants, the contribution becomes the audit plus the recommendation to adjust, and we would report it that way.

Why not just look up the interactions in LnCeCell 2.0? A catalog of single-cell ceRNA scores cannot say whether an interaction is active in a given patient cohort, and it cannot be linked to trial outcomes that exist only as bulk data. There is a second limit. Standard single-cell RNA sequencing captures microRNAs poorly, and co-variation measured in sparse single-cell data carries its own dropout confounding. We use LnCeCell 2.0 as a source of candidate pairs and as an independent check on which edges agree across resolutions, not as ground truth.

Why not just run single-cell sequencing on patients? The file's evidence argues against making this the whole answer. Clinical cohorts such as COMPASS, TCGA and ICGC are bulk and archival and cannot be re-sequenced. Dissociation also biases which cells are captured, as noted in the SCDC paper. Single-cell data are still essential here, as the reference and as the benchmark substrate.

Why not trust HIF1α and MYC alone to explain the metabolic genes? Transcription factors may indeed explain most of the variance. The SNHG12 result shows that HIF1α abundance itself can be gated by a sponge. Our interaction model includes HIF1A and MYC target scores as covariates, so a ceRNA edge is counted only if it adds signal beyond transcriptional control.

Proposed Experiments

The first decisive check is calibration on the null benchmark. At a 5% nominal false discovery rate, the compartment-resolved test should hold close to nominal error across purity levels, while the naive pipeline and JAMI should show false positives that grow as purity falls. The same curve for purity-adjusted partial correlation tells us whether the extra machinery is needed.

The second check is power on the planted benchmark, including M2-restricted effects. Precision-recall curves should show our method recovering planted edges that composition adjustment misses. This check fails if the curves overlap.

The third check is the real-data audit on TCGA PAAD and the osteosarcoma sets. We report the fraction of published edges that survive and whether the published TGF-β and PI3K/AKT enrichments persist under a compartment-matched background. The prediction is that the TGF-β enrichment weakens sharply once fibroblast content is removed. The SNHG12–miR-199a-5p–HIF1A axis is the biologically validated positive control: if the test discards it in PDAC malignant cells, that is either an informative tissue difference or a power failure, and the planted benchmark at matching effect size tells us which.

The final check applies surviving malignant-cell axes to outcome cohorts. It asks whether they add information beyond the M1/M2 metabolic subtype, which already separates outcomes: in the subtype paper, CPTAC survival was worse for M2 (p=0.008), and in COMPASS 48% of M2 versus 20.4% of M1 patients progressed on first-line therapy. We test for added signal with nested Cox models on CPTAC and ICGC. We would include COMPASS only if lncRNA expression can be quantified from its bulk data, which the file does not establish. A null result here is acceptable. The primary contribution is the calibrated separation of real ceRNA edges from compositional ones, not a new prognostic score.