Bio experimental design randomization blocking

Version Compatibility

Reference examples tested with: designit 0.5+, lme4 1.1-35+, lmerTest 3.1+, pwr 1.3+.

Before using code patterns, verify installed versions match. If versions differ:

• R: packageVersion('<pkg>') then ?function_name to verify parameters

If code throws an error, introspect the installed package and adapt the example to the actual API rather than retrying. designit is an R6 package whose BatchContainer$new(), optimize_design(), and *_score_generator() signatures evolve between releases; confirm against the installed vignette (vignette(package = 'designit')) before relying on argument names.

Randomization and Blocking

"Design the experiment so the statistics will be valid" -> Decide what the experimental unit is, randomize treatments to those units, replicate the unit (not the measurement), and remove known nuisance variation by blocking — so that the analysis model mirrors how the experiment was actually run.

• R: designit::optimize_design() for constrained randomization; lme4::lmer() / lmerTest for the matching mixed model
• The design and the analysis are one decision: "analyze as randomized"

The Single Most Important Modern Insight -- The Experimental Unit, Not the Measurement, Is the n

The most consequential and most violated idea in biological design: the experimental unit (EU) is the smallest entity independently assigned to a treatment — and it, not the number of measurements, is the sample size for inference. Lazic 2018 PLoS Biol 16:e2005282 separates three entities: the biological unit (what conclusions are about), the experimental unit (what randomization acts on, = the n), and the observational unit (what is measured). When observational units are counted as independent replicates, the standard error shrinks illegitimately and p-values become meaningless — pseudoreplication (Hurlbert 1984 Ecol Monogr 54:187). Ten thousand cells from three mice are n = 3, not n = 10,000, for a between-mouse question; mice co-housed in a cage dosed through the chow make the cage the EU, not the mouse. Lazic et al. found ~46% of surveyed animal studies pseudoreplicated. The fix is structural: model the design's hierarchy (random effects) or aggregate to the EU before testing — pseudoreplication is, formally, an omitted random effect.

A second, deeper point (Fisher): randomization is what licenses the p-value. It supplies the physical basis for the error term and converts systematic lurking-variable bias into random error balanced in expectation. Model-based tests are approximations to the randomization distribution. Skip randomization and the causal claim rests entirely on assumptions.

Algorithmic Taxonomy

Design	Controls / estimates	When to use	Fails / costs when
Completely randomized (CRD)	error variance only	units homogeneous; no known nuisance	inefficient if real nuisance structure exists
Randomized complete block (RCBD)	one known nuisance (day, litter, chip, donor)	nuisance factor identifiable and blockable	costs error df; harmful if block variance is ~0 ("blocking on noise")
Latin square	two orthogonal nuisances (day x technician)	n² runs affordable for n treatments	assumes no interaction among row/col/treatment
(Balanced) incomplete block	one nuisance, block smaller than #treatments	plate/chip holds fewer samples than treatments	analysis more complex; needs balance for efficiency
Factorial	main effects + interactions, "hidden replication"	>1 factor; interaction is of interest	#runs grows multiplicatively
Fractional factorial / screening	main effects under sparsity-of-effects	many factors, few runs (Plackett-Burman)	aliases effects; cannot resolve all interactions
Split-plot	two EU sizes, two error strata	one factor hard to randomize finely (lane, incubator, batch)	wrong error term if analyzed as a flat factorial -> anti-conservative
Nested / hierarchical	variance components across levels	sub-sampling within units (cells in mice in cages)	pseudoreplication if the nesting is ignored
Repeated measures	within-unit change over time	longitudinal sampling of the same EU	a split-plot in time; needs the within-unit error term

Decision Tree by Scenario

Scenario	Recommended structure	Why
Treatment given per animal, one tissue measured each	CRD or RCBD; n = animals	EU = animal
Many cells measured per animal, between-animal question	nested; aggregate to per-animal (pseudobulk) before testing	EU = animal, cells are observational units
Treatment delivered per cage (chow/water), several mice/cage	EU = cage; block or model cage as random	randomization acted on the cage
Two factors of interest (genotype x drug)	factorial; estimate the interaction	main effects uninterpretable if interaction is large
One factor fixed per run (incubator temp, sequencing lane)	split-plot; whole-plot = run, sub-plot = sample	two error strata; test whole-plot against whole-plot error
Known batch/day nuisance, all conditions fit per block	RCBD; include block in the model	removes nuisance from error; "analyze as randomized"
Plate holds fewer samples than conditions	incomplete block + include block term	balance preserves estimability
Assigning samples to sequencing batches/lanes	-> experimental-design/batch-design	constrained sample-to-batch allocation lives there
Regulated clinical trial randomization	-> clinical-biostatistics	confirmatory/regulated regime out of scope

Choosing and Counting the Experimental Unit

Goal: Identify the EU and therefore the true n before any power or analysis decision.

Approach: Trace the randomization: the EU is the smallest entity to which a treatment level was independently assigned. Anything measured below that level is an observational unit and is summarized (mean/sum) up to the EU, or modeled as a nested random effect — never counted as an independent replicate.

# Between-condition question with multiple cells per donor:
# the donor is the experimental unit, NOT the cell.
# Correct: aggregate observational units to the EU, then test on EU-level values.
library(dplyr)
eu_level <- cells |>
  group_by(donor, condition) |>
  summarise(value = mean(measurement), .groups = 'drop')   # one row per experimental unit
# n for inference = number of donors per condition, not number of cells

Randomization Mechanics

Goal: Assign treatments to units with a documented random mechanism, optionally restricted to guarantee balance on known factors.

Approach: Use a seeded pseudo-random generator (never "haphazard" order, which aliases treatment with processing position/time). For known prognostic factors, restrict the randomization (block/stratify) and then include those factors in the model. When finite-sample imbalance matters, rerandomize against a pre-specified balance criterion (Morgan & Rubin 2012 Ann Stat 40:1263) or use minimization for sequential enrollment (Pocock & Simon 1975 Biometrics 31:103).

set.seed(20260528)                      # record the seed for reproducibility
units <- data.frame(id = sprintf('S%02d', 1:24),
                    block = rep(c('day1','day2','day3'), each = 8))

# Restricted (block) randomization: randomize treatment WITHIN each block
units$treatment <- ave(units$id, units$block,
                       FUN = function(ids) sample(rep(c('ctrl','treat'),
                                                      length.out = length(ids))))
# Also randomize RUN ORDER so processing position is not confounded with treatment
units$run_order <- sample(nrow(units))

Blocking and Local Control

Goal: Remove a known nuisance source from the error term to sharpen the treatment comparison.

Approach: Group units into homogeneous blocks (day, litter, chip, donor), randomize treatments within block, and add the block as a term in the model. The paired t-test is the special case of an RCBD with block size 2. Block only on factors with real between-block variation; blocking on a noise factor spends error df for nothing.

library(designit)                        # constrained assignment; verify API vs installed vignette
bc <- BatchContainer$new(dimensions = list(block = 3, position = 8))
bc <- assign_in_order(bc, samples = units)
bc <- optimize_design(
  bc,
  scoring = osat_score_generator(batch_vars = 'block',
                                 feature_vars = c('treatment')))  # balance treatment across blocks

Split-Plot and Nested Designs -- the Genomics Trap

A split-plot has two experimental-unit sizes and therefore two error strata: a whole-plot factor that is hard to randomize finely (incubator temperature, the sequencing run/lane, the 10x chip, the staining batch) and a sub-plot factor randomized within each whole plot (the individual sample, the genotype). Analyzing a split-plot as a flat factorial uses the wrong, too-small error term for the whole-plot factor and gives anti-conservative tests for exactly the factor that was hardest to replicate. In genomics the lane/run/chip is almost always a whole plot; "batch effects" are frequently a split-plot structure to be modeled, not a nuisance to scrub.

Goal: Match the model's random-effects structure to the design's randomization structure.

Approach: Encode each randomization level as a random effect; fixed effects carry the questions. Crossed vs nested structure determines the denominator for each fixed effect; with few EUs use Satterthwaite or Kenward-Roger degrees of freedom (lmerTest / pbkrtest).

library(lme4); library(lmerTest)
# Whole plot = run (random); sub-plot factor = condition (fixed); cells nested in sample
fit <- lmer(expression ~ condition + (1 | run/sample), data = df)   # run, and sample within run
anova(fit)                               # Satterthwaite df via lmerTest

Factorial Designs and Interactions

A factorial design crosses factors so every observation informs every main effect ("hidden replication") and, uniquely, estimates interactions — the joint action one-factor-at-a-time (OFAT) cannot see. When an interaction is large, main effects are not interpretable alone; reporting a main effect while ignoring a strong interaction is the most common misreading of a 2x2 design. OFAT is less efficient and silently assumes additivity.

Per-Method Failure Modes

Pseudoreplication (observational units counted as n)

• Trigger: treating cells/wells/sections/technical aliquots as independent replicates.
• Mechanism: units within an EU are correlated; the SE is computed as if they were independent (Hurlbert 1984; Lazic 2018).
• Symptom: implausibly small p-values that fail to replicate; reviewers ask "what is n?".
• Fix: aggregate to the EU (pseudobulk) or add the EU as a random effect; the n is the number of EUs.

Split-plot analyzed as a flat factorial

• Trigger: lane/run/incubator factor crossed with a within-run factor, fit with one error term.
• Mechanism: whole-plot factor tested against sub-plot error (too small).
• Symptom: the hard-to-randomize factor looks significant on thin evidence.
• Fix: two-stratum model; whole-plot factor uses whole-plot error ((1 | run)).

Haphazard assignment mistaken for randomization

• Trigger: processing units "in the order they arrived".
• Mechanism: order aliases treatment with time/position/temperature gradients.
• Symptom: apparent treatment effect tracks run order.
• Fix: seeded PRNG assignment; randomize run order too; record the seed.

Blocking on a noise factor

• Trigger: adding a block term with negligible between-block variance.
• Mechanism: spends error df without removing variance.
• Symptom: power lower than the unblocked design.
• Fix: block only on factors with documented between-block variation.

Over-/under-specified random effects

• Trigger: maximal random structure that will not converge, or a structure missing a randomization level.
• Mechanism: maximal protects Type-I but may be singular (Barr 2013); too-lean inflates Type-I (pseudoreplication).
• Symptom: singular-fit warnings, or anti-conservative tests.
• Fix: keep the structure justified by the design; for small EU counts prune by a selection criterion (Matuschek 2017) and report the choice.

Quantitative Thresholds

Threshold	Source	Rationale
EU = level of independent treatment assignment	Hurlbert 1984; Lazic 2018	defines the n for inference
Paired design = RCBD with block size 2	Fisher; standard	pairing is blocking
Latin square needs n² runs for n treatments	standard design theory	controls two nuisances orthogonally
Use Kenward-Roger/Satterthwaite df when EU count is small (roughly < ~10/group)	Kenward & Roger 1997 Biometrics 53:983	naive F df are anti-conservative with few units
Maximal random effects for confirmatory; prune for small samples	Barr 2013; Matuschek 2017	Type-I protection vs convergence/power tradeoff

Common Errors

Error / symptom	Cause	Solution
Significant result that will not replicate	pseudoreplication (cells as n)	aggregate to EU or add EU random effect
Whole-plot factor over-significant	split-plot analyzed flat	two-stratum mixed model
Treatment effect tracks processing order	no run-order randomization	seeded randomization of run order
Blocked design analyzed without block term	"design but don't analyze"	include block in the model; analyze as randomized
Main effect reported despite strong interaction	factorial misread	interpret simple effects within the interaction
Mixed model singular fit	over-specified random effects	prune to the design-justified structure (Matuschek 2017)

References

• Hurlbert SH. 1984. Pseudoreplication and the design of ecological field experiments. Ecol Monogr 54:187-211.
• Lazic SE, Clarke-Williams CJ, Munafò MR. 2018. What exactly is 'N' in cell culture and animal experiments? PLoS Biol 16:e2005282.
• Blainey P, Krzywinski M, Altman N. 2014. Points of significance: replication. Nat Methods 11:879-880.
• Krzywinski M, Altman N. 2014. Points of significance: designing comparative experiments. Nat Methods 11:597-598.
• Krzywinski M, Altman N. 2014. Points of significance: analysis of variance and blocking. Nat Methods 11:699-700.
• Morgan KL, Rubin DB. 2012. Rerandomization to improve covariate balance in experiments. Ann Stat 40:1263-1282.
• Pocock SJ, Simon R. 1975. Sequential treatment assignment with balancing for prognostic factors in the controlled clinical trial. Biometrics 31:103-115.
• Barr DJ, Levy R, Scheepers C, Tily HJ. 2013. Random effects structure for confirmatory hypothesis testing: keep it maximal. J Mem Lang 68:255-278.
• Matuschek H, Kliegl R, Vasishth S, Baayen H, Bates D. 2017. Balancing Type I error and power in linear mixed models. J Mem Lang 94:305-315.
• Kenward MG, Roger JH. 1997. Small sample inference for fixed effects from restricted maximum likelihood. Biometrics 53:983-997.
• Auer PL, Doerge RW. 2010. Statistical design and analysis of RNA sequencing data. Genetics 185:405-416.

Related Skills

• batch-design - Assigning samples to sequencing batches/lanes and batch-effect correction
• sample-size - The experimental unit defines what is replicated and counted
• power-analysis - Blocking and nesting change the effective error variance
• multiple-testing - The design fixes what counts as a family of tests
• single-cell/preprocessing - Pseudobulk aggregation to the donor (experimental unit) for scRNA-seq
• differential-expression/deseq2-basics - The DE model that consumes the design's structure
• clinical-biostatistics/power-and-sample-size - Randomization and design in the regulated-trial regime