Worked Design of a Multi-Condition Donor Study

From a Study Question to an Allocation Plan

A multi-condition single-cell study is not defined by how many cells it sequences. Its inferential strength depends first on how many independent donors contribute information to the comparisons, and on whether condition effects can be distinguished from donor and technical differences. A useful design therefore specifies, before data collection, which donors receive which conditions, how specimens are blocked and distributed across batches, and which contrasts answer the scientific questions.

The worked plan here considers a hypothetical ex vivo experiment in which cells from each donor are split among a vehicle control, a low treatment dose, and a high treatment dose. The outcome used for planning is a donor-level pseudobulk expression summary for a prespecified cell type, measured in log2 expression units. The plan is an example of design reasoning, not a claim about a real study.

The target question is whether either treatment dose changes the mean donor-level outcome relative to vehicle, and whether the two doses differ. Because each donor contributes all three conditions, comparisons can be made within donors. This controls stable donor characteristics in the contrast, provided the conditions are applied and measured comparably. Randomized assignment of donor aliquots to condition and balanced laboratory handling support interpretation of condition differences; they do not by themselves guarantee generalization beyond the sampled donor population.

Specify the Design Before Counting Cells

The proposed design has 24 complete donors. Each donor contributes one biological specimen to each condition, yielding 72 donor-condition libraries before any technical quality-control material is added. The vehicle is the reference condition. Aliquots from a donor should be assigned to conditions at random, and processing order should be randomized or rotated so that a condition is not always handled first or last.

Use six library-preparation batches, with four complete donor blocks in each batch. Each batch therefore contains 12 study libraries: four vehicle, four low-dose, and four high-dose libraries. Keeping a donor's three condition libraries in the same preparation batch makes the within-donor comparison operationally coherent. It does mean that donor and batch main effects cannot be separated simply by comparing overall levels across batches; the main condition contrasts are protected from a batch-wide shift because all three conditions occur in every batch. A condition-specific batch artifact remains possible, so it is important to repeat each condition in every batch and inspect condition patterns across batches.

Sequencing lanes are a further technical allocation, not additional biological replicates. Pool libraries across lanes so that each lane receives a mixture of preparation batches and conditions, with approximately equal condition representation. Do not place all vehicle libraries on one lane and treated libraries on another. If a pooled reference preparation is included once per batch to monitor technical consistency, it is a quality-control sample, not a donor and not an observation in the treatment contrast.

Define the Contrasts and Their Priority

For a cell type and outcome fixed in advance, let \(\mu_V\), \(\mu_L\), and \(\mu_H\) denote the population mean donor-level outcomes under vehicle, low dose, and high dose. A concise set of comparisons is:

Make the two treatment-versus-vehicle comparisons co-primary if both are confirmatory. For example, control their familywise type I error rate at 0.05 using a Bonferroni allocation of \(\alpha=0.025\) to each two-sided test. The high-versus-low contrast can be designated secondary or exploratory, or included in a prespecified multiplicity procedure. Its status should be declared before looking at results. A reference condition does not automatically determine the multiplicity plan.

For a paired comparison, define \(D_{d,L}=Y_{d,L}-Y_{d,V}\) for donor \(d\), with an analogous difference \(D_{d,H}\). The estimate of a condition contrast is the mean of the donor-level differences. Its precision depends on the variation among independent donors' differences, not on variation among cells treated as if they were independent.

Why Blocking Can Improve Precision

The reason to measure every condition within each donor can be seen from the variance of a paired difference. If the condition outcomes for a donor have standard deviations \(\sigma_1\) and \(\sigma_0\), and within-donor correlation \(\rho\), then:

When the within-donor correlation is positive, the covariance term reduces the variance of the difference relative to an unpaired comparison with the same marginal variances. This is the statistical benefit of blocking. It is not a guarantee of a smaller standard error in every realized data set, and it does not compensate for too few donors or for confounding of condition with technical processing.

A Feasible Sample-Size Rationale

Sample-size planning should use independent donors and a scientifically meaningful difference. Suppose pilot and subject-matter input suggest that the standard deviation of donor-level paired differences is approximately 0.50 log2 expression units, and that a difference of 0.40 log2 units is worth detecting. These are planning assumptions, not known constants. For two co-primary two-sided comparisons with familywise \(\alpha=0.05\), a Bonferroni calculation uses \(\alpha=0.025\) per comparison.

As a transparent first-pass screen, a normal approximation for a paired mean difference with desired power 90% gives:

The calculation suggests about 20 complete donors as a screening estimate. It uses a normal approximation and does not fully account for estimating the standard deviation from a finite sample. Choosing 24 complete donors provides a practical margin above that screen, but it does not prove that the design has exactly 90% power. Before finalizing the study, use the planned paired analysis and plausible variation, missingness, and cell-yield scenarios in a simulation-based power assessment. A modest feasibility target is to recruit 30 donors to obtain 24 complete donor blocks if roughly 80% completion is expected: \(24/0.80=30\). Replacements should follow prespecified rules and occur without using observed treatment outcomes to select donors.

For orientation, if the paired-difference standard deviation were exactly 0.50 and there were 24 complete donors, the standard error would be \(0.50/\sqrt{24}\approx0.1021\) log2 units. A two-sided \(t\) test with \(df=23\) and per-comparison \(\alpha=0.025\) uses a critical value of approximately 2.398. The corresponding observed-mean threshold is \(2.398(0.1021)\approx0.2447\) log2 units. This threshold is not a power calculation: power also depends on the true effect and the sampling distribution of the test statistic.

Diagnostics, Alternatives, and Limits

Before processing, inspect a balance table indexed by donor, condition, preparation batch, and lane. Confirm that every planned donor has all three conditions, every batch contains all conditions, and no lane is dominated by one condition. After processing, review library yield, cell recovery, and quality metrics by condition and batch. A condition-associated failure rate, systematic lane imbalance, or a treatment effect that appears only in one batch is a warning that the planned contrast may not represent a consistent condition effect. Document exclusions and missing-sample handling; do not silently drop incomplete donor blocks or replace them based on observed outcomes.

A paired donor-blocked design is appropriate when each donor can meaningfully contribute material to every condition, as in this hypothetical ex vivo allocation. An unpaired parallel-group design may be necessary when conditions cannot be applied to aliquots from the same donor, but it generally needs more donors for comparable precision and requires careful balance of donor characteristics. A partially paired design can use within-donor comparisons where available, but its analysis and power calculation must reflect the missing pairing pattern. None of these alternatives makes cells from the same donor independent biological replicates.

The design also has limits. Results from an ex vivo experiment do not automatically describe in vivo effects. A cell type absent or poorly recovered in some conditions may make its donor-level outcome unavailable, and this missingness can be informative. The sample-size screen is sensitive to the assumed variation and meaningful effect; if either is wrong, the achieved power and precision will differ. Batch balance reduces avoidable confounding but cannot remove all technical variation or guarantee that condition effects are homogeneous across donors.