Bulk RNA sequencing blends every cell in a tissue sample into one averaged profile. "Deconvolution" methods try to reverse this. They estimate what fraction of the sample came from each cell type by expressing the bulk profile as a weighted mix of reference profiles taken from single cells. The cell types biologists care about are often defined functionally, though, not by RNA. Immunologists gate T cells by surface proteins such as CD45RA. Neuroscientists split inhibitory interneurons into morpho-electric-transcriptomic (MET) types, which are defined jointly by shape, firing behavior and gene expression, and which wire into circuits in very different ways. RNA explains only about 40–60% of protein variation (A high-stringency blueprint of the human proteome). Morphology alone recovers fine interneuron MET types only about 59% of the time (Connectomics of predicted Sst transcriptomic types in mouse visual cortex). So for some functional distinctions, a bulk transcriptome may carry little signal at all. Current deconvolution tools report a fraction for every reference type regardless, with no warning when a number is effectively unidentifiable.
We propose to settle this before any bulk data are touched. Take a single-cell reference in which each cell has both RNA and a functional label (protein for immune cells, morpho-electric features for interneurons). Cluster it many times under resampling, alternating between an RNA-only view and a functional-only view. Record how often each pair of functional classes ends up in the same cluster. This cross-modal consensus tells us which functional distinctions are reproducibly visible from RNA. We then deconvolve only at that resolution, merging the distinctions that are not visible, and down-weight reference cells whose RNA and functional identities disagree. The claim is testable: the cross-modal consensus score should predict where deconvolution fails, and it should do so better than the obvious alternative of measuring how similar the RNA signatures are.
Core Claim
Much of the error in estimating fine-grained functional fractions from bulk RNA comes from the reference, not the unmixing algorithm. It has two sources. First, functional classes that are not stably separable in RNA space produce nearly identical signature columns, and the unmixing then trades weight between them arbitrarily. Second, reference cells whose RNA identity contradicts their functional label contaminate the signatures. A cross-modal consensus matrix measures both quantities directly. Using it to set the reference resolution and to weight reference cells should give functional-fraction estimates that are more accurate and honestly calibrated than estimates from finest-resolution RNA references or from protein-gated references.
The immune setting is the testbed, because paired RNA-and-protein atlases give exact ground truth. Interneurons are the application where the stakes are highest. Brain deconvolution today stops at a single "neurons" compartment. Whether it can go further, to parvalbumin (PV), somatostatin (SOM) and vasoactive intestinal peptide (VIP) subclasses or to Sst MET types, is an open question that this method is built to answer rather than assume.
Relation to Prior Work
Several papers motivate the gap. Deconvolution reveals cell-type-specific transcriptomic changes in the aging mouse brain ran CIBERSORTx on 141 mouse cortices. It resolved five coarse categories, with all neurons pooled, and never asked whether finer interneuron classes were identifiable; we take that question on directly. The spatially informed mFISHseq assay resolves biomarker discordance and predicts treatment response in breast cancer combined three transcriptomic classifiers into a consensus vote and reclassified 30% of patients relative to protein staining. It removed the mixing problem physically, by microdissecting pure tumor tissue. We instead ask computationally which protein-defined distinctions survive mixing. High-dimensional single-cell proteomics analysis of esophageal squamous cell carcinoma reveals dynamic alterations of the tumor immune microenvironment after neoadjuvant therapy found that RNA-level profiling misread the functional immune state. That finding is the failure mode our resolvability map is meant to flag in advance.
Two papers supply methods. Adapted single-cell consensus clustering (adaSC3) resamples cells and genes across multiple distance measures, uses diffusion maps in place of principal component analysis to embed curved cell manifolds, and reports better Adjusted Rand Index than SC3 on three of five datasets. We reuse its resampling and embedding, but add a second axis of resampling over modality and aggregate at the class level, not the cell level. scChord maps single-cell RNA to protein distributions with a variational autoencoder followed by flow matching, and recovers bimodal markers such as CD4. It works cell to cell and does not unmix mixtures. It also reports that joint protein covariance degrades at 228 proteins. We use it only as an optional labeler for reference atlases that lack protein measurements, and we treat that covariance limitation as a constraint.
The circuit literature explains why the distinctions matter. The Bayesian sampling in a canonical recurrent circuit with a diversity of inhibitory interneurons argues that SOM cells supply a momentum term that PV cells alone cannot. The connectomics study above shows Sst MET-8 cells forming 0.54 synapses/µm versus 0.25 for other Sst types. We do not propose to infer circuit dynamics from bulk tissue. The point is narrower: if bulk data cannot resolve these classes, any downstream claim about PV/SOM ratios is unsupported, and practitioners need to know that.
Research Program
The central object is a class-level cross-modal consensus. In each of $B$ resamples $b$ we draw 80% of reference cells and 80% of features. We then cluster in one view $v_b$, which is either RNA (diffusion-map embedding as in adaSC3) or the functional modality (protein, or morpho-electric features). For functional classes $a$ and $c$ we define
$$R_{ac} = \frac{1}{|\mathcal{B}_{\text{RNA}}|}\sum_{b \in \mathcal{B}_{\text{RNA}}} \Pr_{i \in a,\, j \in c}\big[\text{cluster}_b(i) = \text{cluster}_b(j)\big],$$
where $\mathcal{B}_{\text{RNA}}$ is the set of RNA-view resamples and the probability is over randomly drawn cells of the two classes. A high $R_{ac}$ means RNA routinely confuses $a$ with $c$. Each resample's contribution comes from a class-by-cluster count table, so the cost is linear in the number of cells, not quadratic. This avoids the $N^2$ consensus matrix that makes classic consensus clustering impractical at atlas scale. For each cell $i$ we also compute an agreement score $q_i$: the fraction of RNA-view resamples in which $i$ lands in the cluster where most of its functional class lands. Functional-view resamples serve as a control. They confirm that the functional labels themselves are stable, so that a high $R_{ac}$ cannot be blamed on noisy gating.
We merge classes agglomeratively on $R$ until every remaining pair falls below a threshold, which gives a resolvability tree. Signatures are built from $q$-weighted cell means at each tree node. Unmixing uses non-negative least squares, and uncertainty comes from bootstrapping over reference resamples. The output is a fraction for each identifiable node, with an interval. The threshold is chosen on held-out donors only.
Baselines
The naive reference point is to predict each sample's fractions as the reference cohort's average composition. Any method that cannot beat it on held-out donors is reporting no sample-specific information.
The strongest existing method is CIBERSORTx-style ν-support vector regression run at the finest RNA cluster resolution, as in the aging-cortex study. Fine-resolution estimates are then summed up the tree post hoc, so it is scored at exactly the same nodes as our method. It is the strongest competitor because it is the field default and the post hoc summing lets it fully use fine structure. For PBMC pseudobulk there is no reported result found on Lacuna for CIBERSORTx or any deconvolution method on GSE164378. The nearest reported figure is the approximately 90% validation accuracy of CIBERSORTx against scRNA-seq in the aging-cortex paper, which is a coarse five-class setting and not directly comparable. We will run this baseline ourselves on identical pseudobulk and reference donors, with a matched hyperparameter search over the regularization setting ν and the choice of signature genes.
The third baseline is a protein-gated reference: signatures computed per protein-defined class, using all cells, without merging or weighting. Four ablations isolate our ingredients. Merging on signature cosine similarity instead of $R$ tests whether consensus adds anything beyond collinearity. RNA-only adaSC3 consensus without the modality axis tests whether the cross-modal part matters. Removing the $q$-weighting tests whether down-weighting discordant cells matters. Replacing diffusion maps with principal component analysis tests the embedding choice.
Beating the strongest baseline means two things on held-out donors: lower root-mean-square error of functional fractions at the nodes both methods report, and bootstrap intervals whose empirical coverage is near nominal. For the resolvability claim specifically, success means $R_{ac}$ predicts per-pair unmixing confusion with higher rank correlation than signature cosine similarity does.
Why not just…?
Why not just deconvolve at the finest RNA resolution and sum up afterwards? This is the most serious threat. At coarse nodes, summed fine estimates may be close to optimal, because weight traded between near-duplicate columns cancels out in the sum. If so, our merging adds nothing at the coarse level, and the contribution shrinks to calibrated intervals plus the map of which nodes can be reported at all. The post hoc-summed CIBERSORTx baseline settles this directly. We will report that outcome if it occurs, and we expect the gains to concentrate at intermediate nodes where fine errors do not cancel.
Why not just build the reference from protein-gated labels? This fixes the definition of the target but not the fact that some protein classes, such as CD45RA-high versus CD45RA-low within a lineage, may differ only slightly in RNA. The collinearity remains and nothing warns the user. The protein-gated baseline and the unweighted ablation measure how much of our gain comes from merging and how much from weighting. If both add nothing, the honest conclusion is that functional relabeling is sufficient.
Why not just merge classes whose signatures are highly correlated? Signature similarity is computed from class means. It ignores within-class spread and discordant cells, and both of these drive unmixing variance. This ablation is the key test of the proposal: if cosine merging predicts confusion as well as $R$, the consensus machinery is unnecessary and we will say so.
Why not translate bulk RNA into protein with scChord and deconvolve in protein space? scChord is trained on single cells. Applying it to a mixture violates its training distribution, and its reported degradation in joint protein covariance at 228 proteins undermines any mixture-level protein reconstruction. We use it only to label protein-free reference cells, and we check that the resulting $R$ matrix matches the one computed from measured protein on the same donors.
Proposed Experiments
The primary benchmark is GSE164378, more than 161,000 PBMCs with 228 surface proteins. We gate cells into protein-defined classes, split donors into reference and test sets, and build pseudobulks with known protein-defined fractions drawn from Dirichlet mixtures. We also include a second pseudobulk set that deliberately under-samples one lineage, to probe robustness to composition shift. GSE100866 (about 8,600 cord blood cells, 13 proteins) is a small replication with a different tissue. The first decisive check is pairwise: for every class pair, does $R_{ac}$ rank the pair's measured unmixing confusion better than signature cosine similarity? The second is end to end: fraction error and interval coverage against the baselines above. The third tests the protein-free route. We relabel reference cells with scChord-imputed protein, recompute $R$, and measure how much the resolvability tree changes.
The interneuron arm uses the 477-cell VISp Patch-seq dataset. Here the functional view is its morpho-electric features and the labels are MET types. Two limitations apply: 477 cells is small, and Patch-seq RNA is noisy. We therefore report the resolvability tree over PV, SOM, VIP and Sst MET types with bootstrap intervals on $R$, and evaluate unmixing only on small held-out-cell mixtures. The question is whether distinctions that matter for wiring, such as MET-8 versus MET-4, are RNA-resolvable at all. We then apply the resulting tree to the 141-mouse aging cortex bulk cohort. Without ground truth, the checks are internal. Interneuron-node estimates must be stable across reference resamples, must not exceed the neuronal fraction that coarse deconvolution assigns, and should show age trends only at nodes the tree deems resolvable. A negative result would be informative in its own right: MET-level distinctions invisible in bulk RNA would mean that any circuit-level claim about SOM/PV composition requires protein or spatial measurement, not deconvolution.
References
- A high-stringency blueprint of the human proteome
- Connectomics of predicted Sst transcriptomic types in mouse visual cortex
- Deconvolution reveals cell-type-specific transcriptomic changes in the aging mouse brain
- The spatially informed mFISHseq assay resolves biomarker discordance and predicts treatment response in breast cancer
- High-dimensional single-cell proteomics analysis of esophageal squamous cell carcinoma reveals dynamic alterations of the tumor immune microenvironment after neoadjuvant therapy
- Adapted single-cell consensus clustering (adaSC3)
- scChord: A Probabilistic Manifold Rectification Framework for RNA-to-Protein Translation
- The Bayesian sampling in a canonical recurrent circuit with a diversity of inhibitory interneurons