Most of what we know about how a fatty liver becomes an inflamed one comes from single-cell RNA sequencing, a method that counts the messenger RNA molecules in thousands of individual cells. Macrophages are labeled "inflammatory" because they carry more inflammatory transcripts. Yet messenger RNA explains only part of protein abundance. Across human tissues, mRNA and protein correlate at roughly $r \approx 0.4$–$0.6$ (A high-stringency blueprint of the human proteome). The best-characterized brakes and accelerators of the fatty-liver-to-inflammation transition also act on proteins rather than transcripts. TXNIP restrains the NLRP3 inflammasome in Kupffer cells, the liver's resident macrophages (Zhu et al.). A truncated PTPRO isoform boosts NF-κB signaling in liver macrophages (PTPROt aggravates inflammation…). SENP3 stabilizes YAP1 by removing a protein tag called SUMO (Myeloid SENP3 deficiency…). If these controls hold the brake at the protein level, then the relationship between a macrophage's RNA and its protein may itself change as disease progresses. An RNA-only atlas would then place the transition at the wrong time or in the wrong cells.
We propose to measure that directly. We will generate paired RNA and surface-protein profiles of single liver cells from mice sampled along a diet-induced course from healthy liver, through fat accumulation (steatosis), to early inflammation. On these data we will fit a translation model with one specific added ingredient: a disease-stage-dependent correction to the RNA-to-protein mapping, penalized so that it stays at zero unless held-out animals require it. The claim is testable in two sentences. If the RNA-to-protein mapping in liver macrophages is stable across disease stages, existing transcript atlases can be corrected once and reused. If it shifts, and specifically if activation proteins appear before or after their transcripts at the transition, then RNA-based staging of steatohepatitis is systematically biased, and the size and direction of that bias become a measurable property of the disease.
What is already done, and what is not
Transcript atlases of diseased liver motivate the question but do not answer it. Su et al. profiled 171,814 non-parenchymal liver cells across five injury models, including a high-fat, methionine-choline-deficient diet. They built Kupffer cell trajectories and scored ligand–receptor communication with CellPhoneDB, all from mRNA. They also note that this diet lacks obesity and insulin resistance. Coassolo et al. used a more physiological high-fat, high-fructose diet and resolved 12 hepatocyte clusters. They confirmed a single gene, CAR, at the protein level by staining, but only after the fact. Huang et al. showed that maternal obesity reprograms fetal Kupffer cells toward glycolysis through HIF1α, and that the adult cells then drive steatosis by secreting apolipoproteins. They used single-nucleus RNA and bulk proteomics but did not measure protein in single cells. None of these three measured RNA and protein together in single liver cells.
Methods that translate RNA into protein supply the modeling tools, and one of their own admissions constrains the design. totalVI models paired RNA and antibody-tag protein counts jointly. It uses a two-part protein likelihood that separates true signal from background antibody binding. scChord argues that regression to the mean smooths away bimodal proteins such as CD4. It instead maps a noise-aware RNA embedding onto the protein distribution with flow matching, which learns a continuous transport from one distribution to another. scTEL uses a Transformer with an LSTM and multi-task losses. scMHVA fuses the two modalities for clustering. All four were benchmarked only on blood, cord blood, or lymphoid tissue. All four also learn one mapping per dataset and treat any condition dependence as a nuisance or a batch effect to be removed. Our proposal does the reverse. It makes condition dependence the quantity being estimated, and it does so in a solid, lipid-laden organ where no such model has been validated.
The obvious combination would be to run a blood-trained scChord or scTEL on existing liver atlases and then re-score cell communication. We do not propose that as the main contribution. Without liver ground truth it cannot be checked. If the mapping does shift with disease, which is exactly our hypothesis, such transfer would be biased in precisely the cells that matter.
Core Claim
In liver macrophages and monocytes, the RNA-to-protein mapping for activation-related surface proteins changes measurably between steatosis and early inflammation. We expect the change to be concentrated in a small set of proteins, and to be large enough that protein-defined activation and RNA-defined activation diverge in their timing along the disease trajectory.
Research Program
Data generation. The data come from CITE-seq, a single-cell method that reads RNA together with DNA-barcoded antibodies against surface proteins. We will run it on the non-parenchymal liver fraction of mice fed the high-fat, high-fructose diet used by Coassolo et al. Sampling covers chow controls, an established-steatosis time point, and an early-inflammation time point, with several independent mice per stage. A small cohort on the methionine-choline-deficient diet used by Su et al. serves as a fast-inflammation contrast; if the same proteins shift under both diets, the finding is less likely to be a quirk of one diet.
The antibody panel, on the order of 100–150 proteins, will include Kupffer cell identity markers, markers of monocyte-derived macrophages, CD44 (a receptor implicated in metabolic macrophage recruitment by Liu et al.), activation and scavenger receptors, and isotype controls. Hepatocytes are fragile in droplet workflows. We will keep those we recover, but we do not make claims about them unless enough cells survive. The inflammasome and SUMO regulators named above are intracellular and cannot be read by surface antibodies. For TXNIP and NLRP3 we will run a small, separate validation on sorted Kupffer cells, and we treat it as supporting evidence rather than a benchmark.
Model. The translation model reuses totalVI's likelihood: a negative binomial for RNA counts, and a two-part negative binomial mixture for protein that separates signal from background. For the mapping from RNA to the protein signal mean, it follows scChord's argument and uses a distributional, not mean-only, mapping. The new ingredient is a stage term. For protein $p$ in a cell with RNA embedding $z$ at disease stage $s$, the log mean of true protein signal is
$$\log \mu_{p}(z, s) = f_p(z) + g_{p,s}(z),$$
Here $f_p$ is the stage-independent mapping shared by all cells, and $g_{p,s}$ is a stage-specific correction whose chow-stage value is fixed at zero. A group-sparsity penalty on each $g_{p,\cdot}$ pushes whole proteins back to a stage-independent mapping unless the data resist.
We define the discordance shift of protein $p$ at stage $s$ as $D_{p,s} = \mathbb{E}_{z}\,|g_{p,s}(z)|$, the average size of the correction over the cells of the relevant type. Because the RNA embedding already contains whatever the transcripts say about disease state, $D_{p,s}$ measures only the protein change that the transcripts cannot explain.
Downstream use. A liver-calibrated model then gives two things. First, it projects predicted surface protein onto the large RNA-only atlases of Su et al. and Coassolo et al. Second, it lets us re-rank predicted ligand–receptor interactions using receptor protein rather than receptor transcript. This responds to the concern, raised in the cell–communication survey by Cheng et al., that more than 140 inference tools score interactions from mRNA alone. Secreted ligands such as osteopontin and apolipoproteins cannot be measured with surface antibodies, so only the receptor side is corrected. We state that limitation openly.
Baselines
The naive reference point is to do nothing: use each surface protein's own transcript, normalized and denoised, as its proxy. This is what current liver atlases implicitly do, and every other method must beat it on held-out mice. A second naive reference for the central question is a per-protein comparison of the RNA–protein correlation within each disease stage, computed on the same CITE-seq data. It asks "does the mapping shift?" with no model at all.
The strongest existing methods are scChord and totalVI, run as published. The file reports no numeric protein-prediction accuracy for either. scChord states only that it had the lowest RMSE and highest Pearson correlation on the cord-blood and PBMC benchmarks, and totalVI reports high but unquantified imputation correlation. The one concrete number available is from scTEL: 86.6% cell-type classification accuracy on PBMC, against 77.0% for sciPENN and 76.1% for Seurat. That is a cell-typing figure, not a protein-prediction figure, and no reported result was found on Lacuna for any RNA-to-protein model on liver tissue.
Each published model is run in two modes. The first is zero-shot, trained on the PBMC atlas (GSE164378) and applied to liver. The second is retrained on our liver chow-plus-steatosis-plus-inflammation data with stage treated as a batch covariate, which is how these tools handle conditions by default. A ridge regression and a mean-squared-error multilayer perceptron on the same inputs complete the set of simple competitors.
Fairness rules apply to every comparison. Training and test splits are made by mouse, never by cell, so that no animal contributes to both. Every method receives the same gene set and preprocessing and the same hyperparameter search budget, measured in trials and GPU hours, tuned on the same validation mice.
Two ablations isolate the proposal's own ingredients. The first removes the stage term $g$ and keeps everything else, which is the direct test of the core claim. The second replaces the distributional likelihood with mean-squared error, which tests whether scChord's argument about over-smoothing matters in liver macrophages.
Beating the baselines means two things. The stage-conditioned model must improve held-out-mouse log-likelihood and per-protein distributional distance over its own stage-free ablation by more than a stage-label permutation null. And the liver-trained models together must beat zero-shot PBMC transfer on per-protein Pearson correlation for Kupffer cells and monocyte-derived macrophages.
Why not just…?
Why not just apply a blood-trained scChord or scTEL to existing liver atlases? This is the cheapest route. The file's own caution about context dependency says a PBMC-trained mapping cannot be assumed to hold in inflamed, metabolically stressed tissue, and no liver validation exists. Kupffer cells have no close counterpart in blood, so the zero-shot model will be asked to extrapolate. Our zero-shot baseline measures the cost directly. If zero-shot transfer matches the liver-trained model on held-out mice, this proposal's premise weakens and we will say so.
Why not just run CITE-seq and compare RNA–protein correlations stage by stage? This is the most serious alternative, and it is included as a baseline rather than dismissed. Its weakness is that raw per-stage correlations mix biology with measurement. Lipid-laden, activated cells differ in RNA capture, ambient RNA, and background antibody binding, and totalVI exists because antibody background is substantial. A correlation drop could therefore reflect worse measurement rather than altered translation. Our model separates these through the background component and the dropout-aware RNA likelihood. If the simple per-stage correlations nonetheless flag the same proteins, with similar effect sizes, as $D_{p,s}$, we will report the simple analysis as sufficient and treat the model's value as limited to projection onto RNA-only atlases.
Why not just use ridge regression or a small neural network? For predicting the average protein level these may be competitive, and we expect them to be close on Pearson correlation. The question here is about distributions, though: whether a subpopulation of macrophages gains a receptor. scChord shows that mean-fitting erases bimodal proteins such as CD4 in blood. The mean-squared-error ablation and the ridge baseline show whether that happens for activation receptors in liver, judged by bimodality recovery and per-protein distributional distance rather than correlation alone.
Why not just use bulk liver proteomics with deconvolution? Hepatocytes dominate liver mass, so Kupffer cell and monocyte signal is diluted to near invisibility in bulk. Even within hepatocytes, Coassolo et al. found 12 states that bulk averaging would merge. Bulk proteomics remains useful here as a check on overall protein abundance in sorted populations, not as a substitute.
Proposed Experiments and Decisive Checks
The first check is transfer. For each method we report held-out-mouse per-protein Pearson correlation, RMSE, per-protein Wasserstein distance, and scChord's correlation-matrix distance on Kupffer cells, monocyte-derived macrophages, stellate cells, and endothelial cells. We compare zero-shot PBMC models against liver-trained ones. The size of the gap is itself a publishable answer to whether blood-derived translation tools can be used on liver.
The second and decisive check is stage dependence. We compare the stage-conditioned model with its stage-free ablation on held-out mice and calibrate against a null in which stage labels are permuted among mice. The result is a ranked list of proteins with nonzero $D_{p,s}$. We then re-run the analysis within the methionine-choline-deficient cohort to see whether the same proteins recur across diets.
The third check is timing. We build Kupffer cell trajectories twice on the same cells, once from RNA and once from measured protein, and ask whether protein-defined activation begins earlier or later along the dietary time course than RNA-defined activation. The sorted-cell TXNIP and NLRP3 measurements test whether the intracellular brake shows a similar lead or lag.
The fourth check is downstream relevance. On held-out mice we rank candidate ligand–receptor interactions three ways: with receptor transcript, with predicted receptor protein, and with measured receptor protein. The measured-protein ranking serves as the reference, and the test is whether predicted protein moves the ranking closer to it than transcript does.
A null result on the second check is still useful. It would tell the field that one liver-calibrated correction suffices for transcript atlases of fatty liver disease.
References
- A high-stringency blueprint of the human proteome
- Inhibition of NLRP3 inflammasome by thioredoxin-interacting protein in mouse Kupffer cells as a regulatory mechanism for non-alcoholic fatty liver disease development
- PTPROt aggravates inflammation by enhancing NF-κB activation in liver macrophages during nonalcoholic steatohepatitis
- Myeloid SENP3 deficiency protects mice from diet and age-induced obesity via regulation of YAP1 SUMOylation
- A single-cell transcriptomic atlas characterizes liver non-parenchymal cells in healthy and diseased mice
- Single-cell analysis of non-alcoholic fatty livers identifies a role for the constitutive androstane receptor
- Kupffer cell programming by maternal obesity triggers fatty liver disease
- Joint probabilistic modeling of paired transcriptome and proteome measurements in single cells
- scChord: A Probabilistic Manifold Rectification Framework for RNA-to-Protein Translation
- A joint analysis of single cell transcriptomics and proteomics using transformer
- Dynamic Synthesis of Multi‐Modal Representations for CITE‐seq Data Integration and Analysis
- The receptor CD44 is associated with systemic insulin resistance and proinflammatory macrophages in human adipose tissue
- Cell-cell communication inference and analysis: biological mechanisms, computational approaches, and future opportunities