Reading cell-type protein states from bulk liver RNA

Most clinical liver data are bulk RNA sequencing of biopsies. A bulk measurement averages thousands of cells into one profile, and it reports messenger RNA, which is an unreliable stand-in for the proteins that actually do the work. Each problem has its own fix. Deconvolution estimates which cell types are in the sample and what each is expressing. Separately, RNA-to-protein models predict a cell's protein levels from its RNA. This proposal asks whether the two errors compound when the fixes are chained. If they do, a single model trained to go straight from a bulk RNA profile to per-cell-type protein levels should do better than running deconvolution first and translation second.

The motivating setting is metabolic dysfunction-associated steatotic liver disease, or MASLD: fat build-up in the liver that can progress to inflammation and scarring. It affects roughly a quarter of people worldwide, and almost no approved drug treats it (Advances in the Study of Intestinal Flora and Its Metabolites in Nonalcoholic Fatty Liver Disease). Candidate drugs are judged largely on bulk tissue or blood markers, so a drug that shifts one cell population's protein state can look like it did nothing. Answering the chaining question requires paired RNA and protein data with known per-cell-type answers. Public datasets that measure RNA and surface protein in the same single cells (CITE-seq, which tags surface proteins with DNA-barcoded antibodies) can supply those answers, because we can pool their cells into synthetic "bulk" samples ourselves.

Core Claim

The claim is that predicting per-cell-type protein abundance from bulk RNA is a distinct learning problem from either deconvolution or translation. A model trained end to end on synthetic bulk samples will recover within-cell-type protein shifts that a deconvolve-then-translate pipeline misses. The mechanism is a distribution mismatch. RNA-to-protein models such as scChord are trained on real single-cell RNA, which is sparse and noisy. Deconvolution outputs are smoothed, systematically biased estimates, so feeding them to a translator puts it on inputs it never saw during training. The claim is narrow on purpose. It concerns protein abundance in cell populations, and mainly shifts in state within a cell type, because that is where a simple reference lookup cannot help.

The application regime is the immune compartment of MASLD livers. This choice is forced by the data. The largest paired dataset in the file, the PBMC atlas GSE164378 with more than 161,000 cells and 228 proteins, measures immune surface proteins. The liver atlas of Andrews et al. also shows that the single-nucleus sequencing needed to recover fragile hepatocytes and stellate cells undercounts immune cells. It found 3% lymphocytes and 5% macrophages, against 7% and 9% with whole-cell sequencing. Bulk biopsies do not suffer that dissociation loss. So inferring liver immune protein state from bulk RNA addresses a population the field's preferred single-cell protocol hides.

Position Relative to Prior Work

Two deconvolution methods supply the starting tools. POPPY maps bulk transcriptomes into a single-cell model's representation space using a cell-type hierarchy and contrastive alignment. Count Bridges is a generative model that works directly on integer counts and resolves bulk or spatial spots into single-cell RNA profiles. Both stop at RNA, and neither has been tested on liver. We reuse Count Bridges as the first stage of the strongest pipeline baseline.

scChord supplies the translation method. It denoises single-cell RNA with a variational autoencoder whose decoder models dropout and overdispersion (a zero-inflated negative binomial, or ZINB, decoder). It then maps RNA to protein distributions with flow matching, a generator trained to transport noise to data along simple paths. It was tested only on blood. Its authors report weaker preservation of protein–protein correlations, measured as Correlation Matrix Distance, once targets reach the hundreds. We do not change scChord. We test what happens when its inputs come from deconvolution rather than measurement.

Two papers motivate the work by showing the gap exists. A high-stringency blueprint of the human proteome puts mRNA–protein agreement at 40–60%. Global molecular landscape of early MASLD progression in obesity profiled 109 obese patients with bulk liver RNA and metabolomics. It found separate programs for fat accumulation and scarring, but attributed them to cell types only by reference to an external atlas, and it measured no protein.

Phosphorus biology plays a constraining role. In rice, adaptation to low phosphate is switched on when hydrogen peroxide oxidizes a cysteine on the regulator PHR2 (Meng et al.), and by 14-3-3 scaffold proteins that shuttle regulators between nucleus and cytoplasm (Kuang et al.). Neither switch need change transcript or protein abundance. These are clean cases where no abundance model, ours included, can see the biology. The proposal therefore makes no claim about protein activity or modification state. It instead reports, for each protein, how much of its variation the model can predict at all. This gives a measured boundary between abundance-driven and modification-driven regulation. Plant phosphate-starvation tissues are a natural later test of the same method once paired data exist, but none are in hand.

Research Program

We build pseudobulk training data from GSE164378, and from GSE100866 (about 8,600 cord blood cells, 13 proteins) as a small sanity set. Each pseudobulk sums the RNA counts of a sampled set of cells. Its targets are the cell-type proportions and the per-cell-type protein mean and spread. The design choice that matters is how cells are sampled. Proportions vary across samples, as in standard deconvolution benchmarks. In addition, within each cell type, we vary which sub-states are drawn, for example by reweighting subclusters along an activation axis. This makes protein state shift within a type and not only through composition.

For a pseudobulk sample $b$ and cell type $k$, let $\mu_{k,b}$ be the true mean protein vector of type-$k$ cells in that sample, and $\bar\mu_k$ the reference mean of type $k$ over the whole training atlas. The primary metric is within-type shift recovery: the Pearson correlation, across held-out samples, between predicted and true deviations from the reference.

$$ r_{\text{shift}} = \operatorname{corr}_b\big(\hat\mu_{k,b} - \bar\mu_k,\; \mu_{k,b} - \bar\mu_k\big) $$

Here $\hat\mu_{k,b}$ is the model's prediction. The metric is averaged over proteins and over types that make up at least a set fraction of the sample. It is zero by construction for any method that only estimates proportions and looks up reference proteins. We also report RMSE on $\mu_{k,b}$, proportion error, and Correlation Matrix Distance on the predicted per-type protein covariance.

The model is an encoder over bulk counts with a negative binomial likelihood term for reconstructing the RNA. It has two heads. One outputs proportions. The other outputs, for each cell type, a protein mean and a diagonal variance, trained with a Gaussian negative log-likelihood. We start with this simple head and move to a flow-matching head like scChord's only if variance calibration demands it.

Splits hold out whole donors, plus one held-out sub-state per major type, so the test distribution of within-type shifts is not seen in training. For each protein we report the model's attainable $r_{\text{shift}}$. Proteins with near-zero values become the candidate list of modification-regulated proteins.

The liver stage applies the trained model to the bulk cohorts already in the file: the Melbourne cohort of 109 patients, VA GSE130970, and EU GSE135251. A liver reference supplies the cell-type vocabulary, built from GSE115469 and the Andrews atlas. Only immune types covered by the protein panel are scored. No protein ground truth exists for these biopsies, so the liver stage tests two things. First, whether predicted macrophage and lymphocyte surface-protein shifts associate with histological stage beyond what deconvolved RNA explains. Second, whether the steatosis-versus-fibrosis separation reported by the Melbourne study appears or disappears at the immune-protein level.

Baselines

The naive reference point is the proportions-times-reference baseline. We estimate cell-type fractions with the same deconvolution front end and predict each type's protein as its atlas mean $\bar\mu_k$. It shows how much of the task is just composition. It scores $r_{\text{shift}}=0$ by definition, and its RMSE is the bar any method must clear.

The strongest existing method is the two-stage pipeline. Count Bridges deconvolves each pseudobulk into single-cell RNA profiles, and scChord, trained on real single cells of the same training donors, translates those into protein. It is the strongest competitor because each stage is the best-performing method for its sub-problem in the file. Count Bridges is reported to beat CIBERSORTx and MuSiC on proportion recovery. scChord reports the lowest RMSE and highest Pearson correlation against totalVI, sciPENN and scTranslator on GSE100866 and GSE164378. No exact RMSE or correlation value for scChord was found on Lacuna; the only reported figures are training on 100,000 cells in about 27 minutes using 229 MB of GPU memory. No reported number for Count Bridges deconvolution accuracy was found on Lacuna either. We therefore rerun both on our splits. Both pipeline stages and our model get the same training cells, the same number of hyperparameter trials, and matched GPU hours.

POPPY is a second deconvolution front end, so the comparison does not depend on one deconvolver. Its reported 714% gain in composition-similarity correlation, on the simulated Kassandra profiles, concerns proportions, not protein.

Two ablations isolate the key ingredient. The first trains our model on pseudobulks where only proportions vary, so within-type sub-state sampling is removed. If $r_{\text{shift}}$ collapses, the gain comes from the training distribution and not the architecture. The second replaces the protein head with per-type RNA prediction followed by scChord. This tests whether the end-to-end objective matters or only the shared encoder.

Beating the pipeline means a higher $r_{\text{shift}}$ on held-out donors and held-out sub-states, across three seeds, with the confidence interval of the difference excluding zero. It also means no worse proportion error and RMSE.

Why not just…?

Why not just deconvolve proportions and look up reference protein levels? This is the real threat. If most protein variation between samples comes from composition, the reference lookup wins on RMSE, cheaply. The proposal does not argue this away. It reports RMSE alongside $r_{\text{shift}}$ and limits the claim to within-type shifts, where the lookup scores zero by construction. If our model's $r_{\text{shift}}$ on held-out sub-states is not clearly above zero, the conclusion is that bulk RNA does not carry recoverable within-type protein signal. That would itself be a useful negative result for drug-response monitoring.

Why not just chain Count Bridges and scChord? Each component is strong on its own data. But scChord's documented failure mode is over-smoothing toward conditional averages, and deconvolved profiles are already averaged, so the chain may lose exactly the bimodal states it is meant to capture. The head-to-head comparison and the second ablation decide this directly. If the chain matches our model, we report that the off-the-shelf chain suffices.

Why not just treat bulk mRNA of a marker gene as its protein level? The proteome blueprint's 40–60% agreement figure argues against it. scChord also documents that linear RNA-to-protein assumptions miss bimodal CD4 and heavy-tailed CD45RA. We include a per-type RNA-proxy baseline, using deconvolved transcript level of each antibody's gene, so the cost of this assumption is measured on our splits rather than assumed.

Why not just run single-cell or single-nucleus sequencing on MASLD biopsies? Whole-cell sequencing destroys hepatocytes, and single-nucleus sequencing halves the immune fraction (Andrews et al.). Neither measures protein. Deep Visual Proteomics does measure protein, quantifying more than 5,000 proteins from about 100 microdissected cells with reproducibility of Pearson r = 0.96 (Deep Visual Proteomics), but it needs specialized laser and mass-spectrometry hardware. It is the right future ground truth for the liver stage, not a substitute for using thousands of existing bulk biopsies.

Decisive Checks

The central experiment compares $r_{\text{shift}}$ on GSE164378 held-out donors and held-out sub-states for four methods: our model, the Count Bridges–scChord chain, the POPPY-fronted chain, and the reference lookup. It is repeated on GSE100866 as a sanity check. A second check tracks Correlation Matrix Distance as the number of target proteins grows from 13 to 228, to see whether the end-to-end model escapes the degradation scChord reports. The per-protein predictability ranking is then inspected: proteins known to be governed by modification or trafficking should sit at the bottom, as the phosphate-switch biology predicts for this class of regulation.

On the liver cohorts, the decisive test is whether predicted immune surface-protein shifts add explanatory power for fibrosis stage beyond deconvolved RNA, within GSE130970 and GSE135251. The test uses nested cross-validation with stage labels never seen in training. A null result there, after a positive synthetic result, would point to blood-to-liver transfer as the barrier. That would make a small Deep Visual Proteomics validation set the next study to fund.