When researchers engineer T cells to fight cancer, the difference between a therapy that lasts for years and one that burns out in weeks often comes down to a cell-fate choice: does an activated T cell become a short-lived terminal killer, or a durable memory cell that persists and patrols? The field has strong mechanistic handles on this choice — costimulatory signaling through 4-1BB sustains tissue-resident memory in influenza infection (Wagar et al.), hydrogel activation during manufacturing skews products toward effector-memory phenotypes with high short-term killing (Underwood et al.), and population pharmacokinetic modeling shows that clinical persistence of a BCMA-targeting CAR-T is governed by the memory fraction rather than any hyper-proliferating clone (Mu et al.). But nearly every claim about which memory phenotype predicts success is derived from tiny cohorts — 3 donors, 18 patients — while measurements span hundreds of thousands of gene features per cell. That is precisely the regime where statistics fails predictably: the Winner's Curse, where only noise-inflated effects pass significance thresholds, and multiple-testing corrections that no subtle true effect can survive (Sculley et al.; Yin et al.).
We now have, for the first time, a resource that lets us do something the field has never done: treat a large harmonized cohort as ground truth and measure how badly small-N memory-phenotype biomarker discovery distorts findings as a function of sample size. The open CAR-T single-cell atlas (Camara-Peña et al.) pools over 1,000,000 cells from 13 studies covering 102 cancer patients, harmonized into a shared latent space with 414,000 high-quality CAR-positive T cells annotated across 11 phenotypes, including central and effector memory subsets. This proposal uses that atlas not as another pooled analysis, but as a population-scale reference against which to quantify the sample-size scaling curve of memory biomarker discovery, and to build a shrinkage-based estimator that lets a small new cohort borrow strength from the atlas without pooling its raw data. The end product is a concrete answer to a question every cell-therapy group faces and no one can currently answer: how many patients or donors do you need before a memory-phenotype finding is worth believing, and how should you analyze a cohort too small to reach that threshold?
Core Claim
Small-cohort claims that a given memory phenotype ($T_{CM}$, $T_{EM}$, or stem memory $T_{SCM}$) determines clinical outcome are systematically inflated by selection noise, and the inflation follows a measurable scaling curve in cohort size. Two things follow. First, a quantified scaling law — effect inflation factor, false discovery rate, and cross-cohort replication probability as functions of $N$ — can be estimated by subsampling the 102-patient atlas, which nobody has done; the closest existing work aggregates data centrally but performs a single pooled analysis rather than characterizing how conclusions degrade with cohort size (Camara-Peña et al.). Second, once the between-study variance is known, a precision-weighted shrinkage estimator lets a new small cohort be analyzed against the atlas as a prior, a mechanism the pooled-atlas approach does not provide. Specifically, for a memory-phenotype effect $\delta$ estimated from a local cohort of $N$ patients with within-cohort variance $\sigma^2/N$, we shrink toward the atlas-level effect $\delta_{\text{atlas}}$:
$$\hat{\delta}_N = w_N\,\delta_{\text{local}} + (1 - w_N)\,\delta_{\text{atlas}}, \qquad w_N = \frac{\tau^2}{\tau^2 + \sigma^2/N},$$
where $\tau^2$ is the between-study variance, estimated once from the 13 source studies. The form is standard empirical-Bayes partial pooling; what is new is applying it to single-cell memory-phenotype associations, calibrating $\tau^2$ on the atlas, and validating that it repairs the Winner's Curse at small $N$.
Research Program
The program has three components. The first is a scaling audit: treat the full harmonized atlas as the population, draw subsampled cohorts of sizes spanning $N = 5$ to $102$ (both uniformly at random and clustered by source study, to mimic the non-identical distributions of real multi-site data, as the federated clustering work of FedSC shows is the realistic case), and re-run the atlas's own differential-abundance pipeline at each size. For every $N$, we measure the inflation factor of the memory-phenotype-to-complete-response association relative to the full-cohort estimate, the replication rate across independent subsamples, and whether the demographic interactions the atlas discovered — memory enrichment mattering most in patients over 60, CD4+ central memory in responding men versus CD8+ effector memory in responding women — are detectable at all. The output is a published curve with a threshold: the minimum $N$ at which inflation drops below a stated bound and replication exceeds, say, 80%.
The second component is the shrinkage estimator built on that curve, delivered in two deployment modes: centralized (the new cohort's counts are combined with atlas statistics), and federated, where only summary statistics travel — following the pattern Gazula et al. demonstrated in neuroimaging, where sharing local beta weights and residual errors via COINSTAC matched centralized pooling across 1,979 subjects while halving runtime. This matters here because raw CAR-T single-cell data with clinical outcomes is exactly the kind of GDPR- and HIPAA-constrained material that never leaves institutions, which is why the atlas had to be assembled from public deposits rather than prospective collaboration.
The third component relinks phenotype to persistence. Mu et al. fit a biexponential pharmacokinetic model to 469 blood transgene measurements from 18 multiple myeloma patients and showed that slow contraction constants and a high memory fraction, not peak expansion, track durable response — but they used bulk PCR with no single-cell phenotypic readout. We extend their nonlinear mixed-effects structure so that infusion-product memory composition, estimated with atlas-calibrated shrinkage, becomes a covariate on the contraction constants. This directly tests the tension flagged by the manufacturing literature: Underwood et al. found that Cloudz hydrogel activation produced the highest 24-hour tumor killing while skewing products toward terminal CD8+ effectors (67.9% CD8+, CD4/CD8 ratio 0.4) with lower expansion, and Zhang et al. similarly pushed cells into an effector-memory phenotype with a small molecule, JK184, that boosted perforin and granzyme. Screens that reward short-term lysis may be selecting against the very cells that persist. A persistence-weighted selection objective — memory fraction under the shrinkage estimator, combined with acute killing — is the deliverable, and its stability across donor resamples is itself an $N$-scaling question our audit answers.
Baselines
The naive reference point is current practice: deep phenotyping of a handful of donors with per-cohort analysis, exactly as Underwood et al. did with 3 healthy donors, where the authors themselves report that donor-to-donor variability confounded interpretation of subset distributions. This "do nothing" baseline is what the field actually runs on, and beating it means showing concretely which of its conclusions invert or lose error bars under resampling. The strongest existing competitor is the centralized atlas pipeline of Camara-Peña et al.: scVI harmonization across 13 studies, manual annotation of 11 phenotypes, and Milo differential-abundance testing, which established that complete responders' infusion products are enriched in memory phenotypes and identified a rare neurotoxicity-associated cell population with an odds ratio of 6.067, present in over 80% of severe ICANS cases. We will run our scaling audit and shrinkage estimator on exactly their data, their latent space, and their testing framework, with identical compute and the same tuning budget, so the only difference is the estimator and the cohort size being analyzed. Beating this baseline means matching its full-cohort findings (we should, since at $N = 102$ the shrinkage weight approaches full local estimation) while additionally producing calibrated, replicable estimates at $N \leq 30$ where their pooled pipeline, applied to a single small cohort, has no mechanism for correcting inflation. For the persistence component, the strongest competitor is the NONMEM bulk pharmacokinetic model of Mu et al., which resolved biexponential contraction from 18 patients and 469 measurements; we compare on their data with the same model structure and differ only by adding single-cell memory composition as a covariate, so any predictive gain is attributable to that ingredient. The key ablation removes the atlas prior: a flat per-cohort estimator with $w_N = 1$, isolating shrinkage as the operative mechanism — if the flat estimator matches the shrinkage estimator across $N$, the proposal's core ingredient is doing nothing and we will say so.
Why not just…?
Why not just pool all public datasets centrally, since the atlas already did? This is the most serious alternative, and in one sense it already succeeded: Camara-Peña et al. pooled over a million cells and found associations invisible to small cohorts. But their own numbers show what pooling cannot fix: 90.1% of cells come from CD19-targeted products, so central aggregation of existing deposits cannot generate the missing non-CD19 phenotypic distributions — you cannot pool your way to data that was never deposited. And pooling is a one-shot analysis of what exists; it yields no guidance for the next group running a 20-patient trial. Our proposal is complementary rather than adversarial: the pooled atlas is our ground truth and our prior, and the scaling curve we produce is precisely the piece their design cannot output. Where central pooling is possible, we expect it to remain the best primary analysis; our claim is about the regime pooling cannot reach.
Why not just deep-phenotype 3 to 5 donors with multi-omics, as many elite studies do? Deep phenotyping builds rich within-subject models — Antonello et al. mapped language representations to fMRI in 3 subjects with ~33,000 data points each — but Underwood et al. explicitly report that 3 donors left subset-distribution conclusions confounded, and the atlas showed that memory-phenotype associations are modulated by age and sex in ways a 3-donor panel cannot even represent. The honest version of this objection is that depth sometimes substitutes for breadth; our Experiment 1 settles it empirically by reporting exactly which conclusions from the activator-platform study survive resampling at $N = 3$ and which do not.
Why not just use classical mixed models or SVMs with cross-validation? These work more often than the ML literature admits: Mu et al. fit 18 patients successfully with nonlinear mixed effects, and a classical SVM achieved a median F1 of 0.73 on the 246-construct CAR endodomain screen, only slightly below the 0.75 median of the quantum-kernel method (Quantum-Kernel CAR-T Cytotoxicity Study). Our estimator is a classical mixed model — the shrinkage form above is textbook partial pooling — so this alternative is not a rival but a component. What classical tooling lacks is calibration: cross-validation gives a fit score, not the probability that a memory-phenotype association will replicate in the next cohort. The scaling audit supplies that, and nothing in the existing small-sample literature for CAR-T does.
Why not just screen constructs and culture conditions on 24-hour tumor killing? Because the two best-powered lines of evidence in the file point the other way: killing assays favored the Cloudz condition, which skewed cells toward terminal effectors with reduced expansion (Underwood et al.), while clinical pharmacokinetics showed persistence is governed by the memory fraction and slow contraction, not peak expansion (Mu et al.). Still, this objection has real force — JK184, selected by a killing screen, induced an effector-memory phenotype and delivered complete regressions in vivo (Zhang et al.) — so we do not claim short-term lysis is uninformative. The decisive check is Experiment 3: if memory composition carries no predictive weight on contraction constants beyond what killing carries, the persistence-weighted objective collapses to the standard screen and we will report that.
Proposed Experiments
Experiment 1 runs the scaling audit on the open CAR-T atlas (Camara-Peña et al.): 500 subsampled cohorts per size across $N = 5$ to $102$, in both uniform and study-clustered sampling, re-running their Milo differential-abundance tests. Metrics are the inflation factor of the memory-to-response association relative to the full-cohort estimate, replication rate across draws, false discovery rate on permuted outcomes, and detectability of the age and sex interactions. We expect inflation well above 2 at $N \leq 15$, decaying toward unity with growing $N$; the deliverable is the empirical curve and the minimum reliable $N$. No reported result found on Lacuna for any existing sample-size scaling analysis of single-cell memory biomarkers, so the reference is our own full-cohort reproduction.
Experiment 2 tests generalizability across targets: train the memory-response classifier on CD19 cohorts, hold out non-CD19 products, and measure the AUROC drop, since the atlas leaves this explicitly unvalidated. The shrinkage estimator with an atlas prior is compared against the flat estimator at matched sample sizes; beating the baseline means retaining direction of association with inflation below 1.2 at $N = 20$ where the flat estimator exceeds 2.
Experiment 3 links phenotype to persistence on the CT103A cohort of Mu et al., where extramedullary spreading significantly reduced peak concentration ($p = 0.0258$): add atlas-shrunk memory-fraction covariates to their mixed-effects structure and compare predictive intervals for the contraction constants against their bulk-only model. The decisive check is a small prospective manufacturing study replicating the activator comparison of Underwood et al. with the donor count dictated by Experiment 1's threshold, pre-registering the phenotype shifts and persistence predictions before a single donor is run — the first time a cell-therapy experiment will be sized by a measured scaling law rather than convenience.
References
- Intrinsic 4-1BB signals are indispensable for the establishment of an influenza-specific tissue-resident memory CD8 T-cell population in the lung
- T Cell Activators Exhibit Distinct Downstream Effects on Chimeric Antigen Receptor T Cell Phenotype and Function
- A Model Perspective Explanation of the Long-Term Sustainability of a Fully Human BCMA-Targeting CAR (CT103A) T-Cell Immunotherapy
- Winner's Curse? On Pace, Progress, and Empirical Rigor
- Reduced White Matter Integrity With Cognitive Impairments in End Stage Renal Disease
- An open CAR-T single-cell atlas to enable in-depth characterization and rational engineering of CAR-T products
- Federated Self-Supervised Single-cell Clustering of scRNA-seq Data
- Federated Analysis in COINSTAC Reveals Functional Network Connectivity and Spectral Links to Smoking and Alcohol Consumption in Nearly 2,000 Adolescent Brains
- A drug screening to identify novel combinatorial strategies for boosting cancer immunotherapy efficacy
- Scaling laws for language encoding models in fMRI
- Enhanced Prediction of CAR T-Cell Cytotoxicity with Quantum-Kernel Methods