Growth Charts for Smooth Muscle Cells: Time-Matched Reference Scores for Tracking Phenotypic Switching

Smooth muscle cells in artery walls normally contract to hold vessel tone. Under injury, oxidized lipids, or inflammation they can "switch": they stop contracting, start dividing and migrating, and some become macrophage-like or bone-like cells. This switching drives atherosclerosis, restenosis after stenting, and aortic dissection. Most mechanistic work studies switching in cultured cells measured over time. The problem is that cultured smooth muscle cells lose their contractile genes on plastic dishes even when nothing is done to them. Tissue dissociated at 37°C also acquires a heat-shock stress signature. Any trajectory drawn through such data mixes three things: the disease stimulus, drift caused by the dish, and stress caused by sample preparation.

Pediatric cardiology solved the same structure of problem decades ago. A child's coronary artery diameter means nothing on its own. It only means something as a Z-score, a deviation measured against the healthy mean and spread for children of that body size, and Z ≥ 2.5 defines a high-risk lesion (Guideline for incomplete Kawasaki disease). We propose to build the equivalent "growth chart" for smooth muscle gene expression. The covariate is time in culture, or time since dissociation, rather than age. Each perturbed cell is then scored by how far, and in which genes, it deviates from untreated cells at the same moment. Trajectory inference runs on these deviation scores instead of raw expression. Our central claim is that switching kinetics, meaning which programs fire first and which cells are ahead of their cohort, become cleaner and more transferable once dish drift is removed this way.

Core Claim

In time-course data on cultured smooth muscle cells, the main axis of variation in untreated cells is culture drift, and it points in the same direction as the switching program. We therefore claim that per-gene reference scores, conditioned on culture time and computed with a count-aware model, will do three things. First, untreated cells will collapse to a calibrated null with no trajectory. Second, the known ordering of events will be recovered more faithfully than with raw expression, fold-change, or batch correction. Third, the deviation axis learned in vitro will transfer better to human plaque cells, which never experienced dish drift.

The reference scores must not assume a bell curve, because single-cell counts are sparse and overdispersed. For gene $g$ in cell $c$ with count $x_{gc}$, capture time $t_c$ and sequencing depth $s_c$, we define

$$z_{gc} = \Phi^{-1}\big(F_g(x_{gc} \mid t_c, s_c)\big),$$

Here $F_g$ is a negative binomial cumulative distribution whose mean $\mu_g(t)$ and dispersion $\phi_g(t)$ vary smoothly with culture time. These are fit only on vehicle-treated reference cells. Ties at zero are broken by randomization, and $\Phi^{-1}$ is the standard normal quantile function. By construction, held-out reference cells should give $z \sim \mathcal{N}(0,1)$ at every time point, whatever the gene's sparsity. This directly answers the normality objection that the research file raises against naive Z-scoring.

Relation to Prior Work

Three lines of work motivate the proposal without solving it.

The first is clinical normative modeling. The Kawasaki guideline above and the body-surface-area-indexed aortic diameter of Jiang et al. show that vascular measurements only become interpretable relative to a covariate-dependent healthy reference. Both apply this to single scalar anatomical measures. We apply it per gene, in high dimension, with time as the covariate.

The second is time-series trajectory inference, which supplies our method. Campbell & Yau model each gene's expression over time as a Gaussian process and anchor each cell's pseudotime to its capture time, which lets them flag "precocious" cells. Tempora orders clusters using pathway scores and capture times. PACE uses geometry-aware optimal transport to stop inferred paths from cutting across the data manifold. All three build trajectories relative to the dataset's own distribution and have no notion of an external healthy reference. We reuse the capture-time-anchored Gaussian process as the downstream model and change only its input.

The third is the smooth muscle switching literature, which supplies the ground truth. Karagiannis et al. found transient G-protein-coupled receptor signaling at 3 hours that was gone by 21 hours, and Serpin downregulation only at 21 hours, in moxLDL-treated coronary smooth muscle cells. Fang et al. on METTL3 showed that METTL3 brakes serum-induced switching through autophagy genes and cell-cycle arrest. The single-cell atherosclerosis review constrains the design: it warns that warm dissociation distorts contractile and stress profiles. This is exactly why a time-matched reference, rather than a single time-zero control, is necessary.

Research Program

The first step is data. We will generate dense single-cell RNA sequencing time courses of primary human aortic smooth muscle cells sampled at roughly eight times over 0–72 hours. There are three arms: serum stimulation, moxLDL, and vehicle. The vehicle arm is sampled at every time point and makes up about 40% of cells, because the reference surfaces are only as good as their coverage. A METTL3-overexpression arm under serum provides an intervention with a known direction of effect. At three time points we will split each sample between warm enzymatic dissociation and cold-protease dissociation. This lets us estimate the dissociation-stress signature as a second reference covariate. Where vehicle arms exist, we will also reanalyze GSE36487 as a bulk check. We have not yet confirmed whether that dataset contains time-matched vehicle samples, and we will verify this before relying on it.

The second step is the reference model. For each gene we fit the negative binomial mean and dispersion as smooth functions of culture time and dissociation protocol, using splines with shrinkage of dispersion across genes for stability. We check calibration on held-out vehicle cells before using the model for anything else.

The third step is trajectory inference. We run the capture-time-anchored Gaussian process on the deviation scores of perturbed cells, using sparse inducing points to avoid cubic cost. We compare it against the same model run on conventionally normalized expression.

The fourth step is transfer. We fit a deviation axis in vitro and project smooth muscle cells from human carotid plaques (GSE159677) onto it. If the dataset's annotations permit, we test whether cells from more advanced lesion regions score further along the axis.

Baselines

The naive reference point is raw log-normalized expression fed into the same Gaussian process pseudotime model. This is current practice, and it is what our score replaces.

The strongest competitor is fold-change or residualization against time-matched vehicle controls. Each gene's log expression in each cell is centered on the vehicle mean at the same time point, interpolated between sampled times, and the result is passed to the identical Gaussian process. This shares our key idea of a time-matched reference. It drops only the time-varying dispersion and the count-aware transform, so it is the right test of whether those additions matter.

The batch-correction baseline integrates time points with Harmony or ComBat before trajectory inference.

We also include Tempora and PACE run on raw expression. These represent the strongest published trajectory methods. On their own benchmarks they report the following: Tempora reaches an accuracy of 0.78 on the skeletal myoblast time course and 0.90 on cerebral cortex; PACE reduces distributional error by 23.7% on average versus its baselines; and the capture-time Gaussian process reaches a Spearman correlation of 0.996 versus Monocle's 0.927 for recovering held-out capture times in Arabidopsis (Campbell & Yau). No reported result found on Lacuna exists for any method on smooth muscle switching time courses, so every comparison will be newly run.

All methods receive the same cells, the same highly variable gene set, the same compute, and the same hyperparameter search budget, with tuning done on a validation split of time points.

Two ablations isolate the key ingredient. One uses a Gaussian Z-score with time-varying mean and variance but no count model. The other uses a time-invariant reference, a single time-zero control. Beating the strongest competitor means three things: lower false-trajectory signal in held-out vehicle cells, better recovery of the planted and known event orderings, and higher transfer accuracy to plaque cells, each by a margin exceeding bootstrap variability over donors.

Why not just…?

Why not just compute fold-change against untreated controls? Against a time-zero control, fold-change folds culture drift into the "treatment effect," because the contractile genes are already falling in vehicle cells. Against time-matched controls, this is a serious threat. Its only weaknesses are that it ignores how spread changes over time and how sparse genes behave. If the time-matched fold-change baseline matches our score on calibration, ordering recovery and transfer, the honest conclusion is that time matching, not the distributional model, is the contribution. We would report it as such and drop the negative binomial machinery.

Why not just batch-correct across time points? Harmony and ComBat treat capture time as a nuisance and remove variation aligned with it. In a time course, the switching program is itself aligned with time, so correction should remove both drift and signal. The planted-signal experiment below measures directly how much true signal each method keeps.

Why not just compare early versus late endpoints? Endpoint comparisons find major regulators but miss transient events. In Karagiannis et al., receptor signaling was present at 3 hours and absent at 21 hours, so a single late comparison would miss it entirely. Endpoints also cannot identify cells progressing faster than their cohort. We include a two-endpoint differential-expression analysis to show which orderings it cannot recover.

Proposed Experiments

The first decisive check is the null. On held-out vehicle cells, raw-expression pseudotime should correlate strongly with capture time and with loss of α-SMA, SM22α and calponin. That correlation is the drift artifact. Under our scores, held-out vehicle cells should show about 4.6% of gene-cell entries beyond |z| > 2, consistent across time points and across expression levels, and no pseudotime correlated with capture time. The Gaussian ablation is expected to fail this calibration for sparse genes.

The second check is planted signal. We add a known synthetic switching program to a subset of vehicle cells, with a specified onset time and rate, by resampling counts. We then measure Spearman correlation between recovered and true per-cell progress, and the accuracy of recovered onset times. This gives a ground truth that real data lack.

The third check is biological ordering. In the serum and moxLDL arms, the method should place receptor-signaling and cholesterol-synthesis deviations before contractile-gene loss and Serpin decline, as reported by Karagiannis et al. METTL3 overexpression should slow progress along the deviation axis and shift autophagy genes upward, as Fang et al.'s endpoint data predict. We report the fraction of these expected orderings each method recovers, together with held-out capture-time Spearman correlation.

The fourth check is transfer. A classifier or axis trained in vitro is projected onto GSE159677 plaque cells. We compare how well it separates lesion-associated cells from adjacent-tissue cells, as measured by area under the curve, when the axis is built from our scores versus from each baseline. Dish drift has no counterpart in vivo, so only a drift-free axis should transfer.

If our scores win the null and planted-signal tests but not the transfer test, the method is a good denoiser for in vitro work but not a bridge to patients. We would state that limitation explicitly.