Composition-Aware Reference Gene Selection

Measuring how much a gene is expressed usually means dividing by a "reference gene", an internal yardstick assumed to stay constant across the samples being compared. Decades of reference-gene studies show that the yardstick often moves. What they rarely ask is why. In a bulk tissue sample, RNA from many cell types is pooled. A gene can therefore look unstable simply because the mix of cells changed, even if its expression inside every cell type is perfectly flat. Worse, two genes made by the same cell type keep a constant ratio to each other. The most widely used stability test rewards exactly that pattern, so it can certify a pair of references that in fact tracks the abundance of one cell population.

We propose to score reference genes, and pairs of references, using single-cell atlases. The score separates two sources of instability: change inside a cell type, and change in the mix of cell types. Because a single-cell atlas splits cells by type, condition, tissue, sex and donor, most of these small subgroups contain very few cells. The score therefore borrows statistical strength across neighbouring subgroups instead of trusting each one in isolation. The output is a ranked panel of references with an explicit statement of which composition shifts it tolerates, plus a diagnostic that flags existing bulk-validated references that are really cell-abundance proxies.

Core Claim

Reference-gene stability belongs to the combination of cell type and condition, not to the tissue. The bulk-level tools now in standard use conflate the two, and this produces predictable false positives and false negatives. geNorm computes a gene's average pairwise variation, the M-value, and uses the pool-size criterion $V_n/V_{n+1}$ to decide how many references to average. NormFinder partitions variance within and between condition groups. BestKeeper uses the standard deviation of raw quantification-cycle values. The reference-gene literature documents that their rankings conflict (Amorphophallus, Li et al.). It also documents that a panel validated in one context fails in another: 18S produced a normalization error of 426 on CYP6-1 across aphid development (Myzus persicae case study), and EF1α was the worst candidate under abiotic stress in Reaumuria soongorica (Xia et al.). These papers motivate the proposal, but all of them work on bulk extracts, such as whole crushed aphids or plant organs. None can say whether the failure is regulatory or compositional.

The mechanism is simple enough to state exactly. Let $\pi_{sk}$ be the fraction of sample $s$'s RNA contributed by cell type $k$. Let $\mu_{gk}(c)$ be the mean expression of gene $g$ in cell type $k$ under condition $c$. The bulk log-ratio of genes $g$ and $h$ is then

$$ \log \frac{B_{gs}}{B_{hs}} = \log \frac{\sum_k \pi_{sk}\,\mu_{gk}(c_s)}{\sum_k \pi_{sk}\,\mu_{hk}(c_s)} . $$

This ratio is invariant to composition only if $\mu_{gk}/\mu_{hk}$ is the same for every cell type $k$. It is invariant to condition only if each $\mu_{gk}(c)$ is flat in $c$.

geNorm checks neither property directly. Take two genes expressed only in cell type $k$. Their ratio is constant, so geNorm scores the pair as ideal. Yet a normalization factor built from them is proportional to $\pi_{sk}$, so every target gene gets divided by the abundance of cell type $k$. This is the co-regulation trap flagged by the Amorphophallus study, appearing in compositional form, where no pathway-diversity rule for choosing candidates can catch it.

Research Program

The method has three pieces.

The first is a decomposition. From a single-cell atlas we estimate $\mu_{gk}(c)$ for every candidate gene. For each gene and each pair of genes we compute two variance components of the log expression or log-ratio. One is the variance across conditions within each cell type. The other is the variance across cell types, weighted by how much composition actually varies in the target setting. The composition spread is taken either from the atlas itself or from deconvolution of the user's bulk data.

The second is shrinkage across sparse subgroups. The within-type component must be estimated in each cell of the cell type × condition × tissue × sex table, and many of those cells hold a handful of cells from one or two donors. Estimating each one independently is what the intersectional-fairness literature shows fails. Paes et al. prove that verifying a property across many binary attributes becomes information-theoretically impossible. Ji et al. show that hierarchical borrowing cuts subgroup-metric error by a factor of 3 to 5 at ten labelled examples. We reuse the hierarchical idea, not their Beta-calibration model. We fit a hierarchical model on donor-level pseudobulk log-fold-changes, with random effects for cell type, condition and their interaction, and we report posterior intervals on each stability component. From DRAF we borrow the practice of placing explicit constraints only on subgroups above a population threshold, while the rest are handled through the marginals. Here, subgroups below a donor-count threshold contribute only through the shrunken parent effects. Molina and Loiseau show that marginal quantities bound intersectional ones when attributes are nearly independent. This constrains the design: when cell type and condition are strongly dependent, as when a condition creates a new cell state, marginal borrowing is unsafe. In those cases we flag the subgroup rather than smooth over it.

The third is selection. We replace the heuristic $V_n/V_{n+1} \le 0.15$ threshold with a posterior predictive criterion. A reference set is acceptable if its predicted normalization-factor drift stays within a tolerance, with a stated probability, over a declared range of composition and condition shifts. A set can therefore be certified "robust to beta-cell loss up to 50%" rather than simply "stable".

The work is analysis plus a small method. The deliverables are the scoring procedure, a catalogue of composition-robust reference pairs for the tissues in the benchmark atlases, and an audit of classic references (ACTB, GAPDH, HPRT1, EF1α-type genes) that reports which composition shifts break them.

Baselines

The naive reference point is normalization by a single canonical housekeeping gene (ACTB or GAPDH), together with library-size normalization for sequencing data. The literature already shows this can fail badly, for example the twofold artefact from HPRT1 in porcine oocytes (Haug et al.). It anchors the scale of any improvement.

The strongest existing practice is the bulk multi-algorithm consensus. geNorm, NormFinder, BestKeeper and the comparative ΔCt method are run on bulk (or pseudobulk) samples, and their ranks are combined by geometric mean in the RefFinder style (Multi Algorithm Consensus and Pairwise Variation Analysis), with pool size chosen by $V_n/V_{n+1}$. This is the procedure every cited reference-gene paper uses, so it is the competitor practitioners would actually choose. It gets the same candidate genes, the same samples, and NormFinder receives the true condition-group labels. The benchmark numbers these papers report are stability values from their own organisms, such as the 0.149 NormFinder value for ACTB+PFKP in Haug et al. Those are not comparable to our tasks. No reported result was found on Lacuna for consensus reference selection on single-cell-derived pseudobulk benchmarks, so we will establish that number ourselves.

The strongest method-level competitor is deconvolve-then-adjust. We estimate cell fractions with RNA-Sieve or MEAD, then regress the estimated fractions out of the bulk-selected references and targets. RNA-Sieve reports 6.9% mean L1 error in Smart-Seq2/10x cross-protocol deconvolution, against 8.6% for the next best method. That figure bounds how well composition can be removed after the fact. Deconvolve-then-adjust uses the same single-cell reference we use.

Two ablations isolate our ingredients. The first uses the decomposition without shrinkage, estimating each subgroup independently. The second keeps shrinkage but drops the composition term, so it is equivalent to a within-cell-type-only geNorm.

Beating the baselines means two things. The error in recovered log2 fold changes of held-out target genes must be significantly lower than both the consensus baseline and deconvolve-then-adjust, using paired tests across simulation replicates and tissues. The false-stable-pair rate, defined below, must also be lower.

Why not just…?

Why not just use NormFinder with condition groups, since it already separates within- and between-group variance? NormFinder's groups are the experimental conditions, while composition varies both between and within them, for example donor-to-donor differences in beta-cell fraction. A pair of genes specific to the same cell type has low variance in both components, so NormFinder has no term that penalizes it. The composition-shift simulations below measure this directly: consensus rankings including NormFinder should select same-cell-type pairs at a rate that grows with composition variance.

Why not just deconvolve the bulk data and skip reference genes altogether? For transcriptome-wide sequencing this is a real threat, and deconvolve-then-adjust is a full baseline for that reason. It does not help an RT-qPCR panel, where only a dozen genes are measured and there is nothing to deconvolve. Choosing references beforehand from an atlas is exactly what those experiments need. Deconvolution also inherits its own failure modes: MEAD states its inference breaks with missing or over-partitioned cell types, and every deconvolution method treats reference profiles as condition-invariant (SCDC included). If deconvolve-then-adjust matches our method on the sequencing tasks, we will report that our contribution is limited to the targeted-assay setting.

Why not just use rank or pairwise-reversal methods that avoid normalization? Less is more argues that within-sample gene-pair orderings sidestep library-size artefacts. They do not sidestep composition. A reversal between a T-cell gene and an epithelial gene flips when the tissue mix flips, and the equation above applies to ordering as much as to ratios. We will test whether gene-pair classifiers built from pairs our method flags as composition-sensitive lose accuracy under simulated composition shift.

Why not just estimate stability separately in each cell type × condition subgroup? That is the no-shrinkage ablation. The fairness results of Paes et al. and Ji et al. predict high variance in sparse subgroups. We expect it to over-reject genes in rare cell types, and the ablation measures by how much.

Proposed Experiments

The first experiment uses pseudobulk simulation with known ground truth. From Tabula Muris Senis (used by RNA-Sieve) we build pseudobulk samples across age, sex and tissue. We control composition shifts and include or exclude true within-type expression changes. The truth for each target gene is its within-cell-type fold change. The metrics are the absolute error of the recovered log2 fold change after normalization, and the false-stable-pair rate. That rate is the fraction of certified reference sets whose normalization factor correlates with some $\pi_k$ above a threshold. We repeat the simulation with a Smart-Seq2 reference and 10x pseudobulk, and the reverse, to add the cross-platform scaling distortion documented by RNA-Sieve and MEAD.

The second experiment uses a natural composition shift in real bulk data. In the 77-donor pancreatic islet cohort used by SCDC, beta-cell proportion falls with HbA1c (p = 0.0019 in SCDC). Xin et al. and Segerstolpe et al. single-cell data serve as the atlas. The decisive check is this: reference sets chosen by bulk consensus should show normalization factors that correlate with estimated beta fraction, and should create spurious HbA1c associations for control targets whose within-beta-cell expression is flat in the single-cell data. Sets chosen by our method should not. We also test the reverse error, in which genes rejected by bulk consensus prove flat within every cell type.

The third experiment is a low-mixture sanity check. On the MDA-MB-468/MCF-7/fibroblast mixtures from SCDC, with 6:3:1 ground truth, the predicted bulk pairwise ratios from the equation above should match the observed ratios. This checks that the linear mixing model holds for the candidate genes before we rely on it.

The proposal fails if bulk consensus and our method pick references whose normalization factors have indistinguishable composition correlation in the islet cohort. It also fails if deconvolve-then-adjust closes the whole gap on the simulated sequencing tasks. The second outcome would narrow the claim to targeted-assay design, and we would state that plainly.