# Design Types and the Replication Structure Choosing the right design structure is mostly about matching the *unit of randomization* and the *unit of replication* to your question, and respecting any nesting in the analysis. This file walks through the standard structures and then treats the single most common fatal error — pseudoreplication — in depth. ## Table of contents - [Completely randomized design](#completely-randomized-design) - [Randomized complete block design](#randomized-complete-block-design) - [Latin square](#latin-square) - [Repeated-measures and crossover](#repeated-measures-and-crossover) - [Split-plot designs](#split-plot-designs) - [Cluster / group-randomized designs](#cluster--group-randomized-designs) - [Nested designs and pseudoreplication](#nested-designs-and-pseudoreplication) ## Completely randomized design Units are assigned to treatments purely at random, no blocking. Simplest design; appropriate when units are homogeneous and there's no identifiable nuisance factor. Analyze with one-way ANOVA / regression. If units are *not* homogeneous, the nuisance variation inflates error — block instead. ## Randomized complete block design Group units into **blocks** of similar units (day, batch, litter), and randomize all treatments *within* each block. Every treatment appears once per block. The between-block variation is removed from the error term, sharply increasing precision when blocks differ. Analyze with `treatment + block` in the model. This is the default upgrade over a completely randomized design whenever a nuisance factor exists. ## Latin square Controls **two** nuisance factors simultaneously with a square layout: each treatment appears exactly once in every row and every column. Classic uses: row = day, column = position/order, cell = treatment. Requires #treatments = #rows = #columns, and assumes no interactions between the blocking factors and treatment. Efficient when both nuisance dimensions matter and runs are limited. (Graeco-Latin squares extend this to three nuisance factors.) ## Repeated-measures and crossover Each subject receives more than one condition, serving as its own control. This removes between-subject variation — usually the largest noise source — so these designs are far more powerful per subject. - **Repeated measures:** the same units measured under several conditions or over time. - **Crossover:** each subject receives each treatment in sequence, with **washout** periods between to clear carry-over. Subjects are randomized to treatment *orders* (e.g. an AB/BA crossover; or a Williams square for ≥3 treatments to balance order). Watch for: - **Carry-over / residual effects** — an effect of the previous treatment persisting into the next period. Adequate washout is essential; otherwise the design is biased. - **Period effects** — systematic change over time (learning, fatigue, disease progression). Balanced orders let you separate period from treatment. - **Correlation within subject** — the repeated observations are not independent; the analysis must model it (mixed model / repeated-measures ANOVA). Sample-size/power for these depends on the within-subject correlation — use simulation in the **statistical-power** skill. ## Split-plot designs Arises when some factors are **hard to change** (applied to large units) and others are **easy to change** (applied to sub-units). The hard-to-change factor is randomized to whole plots; the easy factor is randomized to subplots within each whole plot. Example: oven temperature (whole plot — you can't re-set it per sample) × coating type (subplot — applied per sample). Crucially there are **two different error terms** — one for whole-plot factors, one for subplot factors — and the analysis must use both. Treating a split-plot as a completely randomized factorial gives wrong (usually anticonservative) tests for the whole-plot factor. Industrial DOE and agricultural trials are full of accidental split-plots; recognize when a factor can't be reset per run. ## Cluster / group-randomized designs When the intervention is delivered to a *group* (a clinic's protocol, a classroom curriculum, a village water supply), you can only randomize at the group level. The **cluster is the unit of randomization**, and because members of a cluster are correlated, it is effectively the unit of replication too. - Power depends on the number of **clusters** far more than the number of individuals, and on the **intraclass correlation (ICC)**. Adding people to existing clusters helps much less than adding clusters. - The **design effect** `DEFF = 1 + (m − 1)·ICC` (m = cluster size) quantifies how much the effective sample size shrinks; even a small ICC with large clusters costs dearly. Power these by simulation (see **statistical-power**). - Analyze with a method that accounts for clustering (mixed model with a cluster random effect, or GEE). Analyzing individuals as independent is pseudoreplication. ## Nested designs and pseudoreplication **Pseudoreplication** is treating non-independent measurements as independent replicates. It is the most common and most damaging design error in experimental biology, and it cannot be fixed after data collection — only by designing and analyzing at the correct level. The principle: **the replicate is whatever the treatment is independently applied and randomized to.** Measurements taken below that level are *technical replicates* — they improve the precision of a single unit's value but do **not** add degrees of freedom for testing the treatment. Worked examples: - **One dish per treatment, 50 cells imaged.** Treatment applied to the dish ⇒ n = 1 per treatment. The 50 cells describe that one dish; they are not 50 independent tests of the treatment. You need multiple independently treated dishes. - **3 mice per group, 100 cells each.** n = 3 (mice) for a treatment given to the mouse, not 300 (cells). Average within mouse, or use a mixed model with mouse as a random effect. - **One tank of fish given a diet, every fish measured.** The tank is the unit (the diet was randomized to the tank) ⇒ n = number of tanks, not number of fish. Shared tank water, temperature, and social effects make fish within a tank correlated. - **Repeated measurements over time on the same subject** are nested within subject; the subject is the replicate. How to avoid it: 1. **Identify the experimental unit** = the smallest physical entity to which a treatment level is independently and randomly assigned. 2. **Replicate at that level** — more independently treated units, not more measurements per unit (though technical replicates can reduce measurement noise). 3. **Analyze with the nesting respected** — average to the unit level, or fit a mixed model with random effects for the nesting (cells in mice, fish in tanks, time in subjects). The fixed-effect treatment test then uses the correct, larger error and correct degrees of freedom. Technical replicates are still worth taking — they sharpen each unit's estimate — but report and analyze them as what they are, never as independent biological replicates. For sample size of nested/clustered designs, use simulation in **statistical-power**.