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A randomized controlled trial assigns experimental units to competing treatments by a specified random mechanism and compares their outcomes. Under complete randomization of $N$ units, exactly $n_1$ receive assignment one and $n_0=N-n_1$ assignment zero. With fixed potential outcomes, each unit has assignment probability $n_1/N$. ThereforeThis proves design-unbiasedness of the mean difference for the finite-population average treatment effect, assuming consistency in causal inference and no interference in causal inference.

Randomization controls the assignment distribution; it does not force every realized baseline covariate difference to be zero. Equal assignment probabilities yield unconditional exchangeability in the design, whereas covariate-dependent randomization can require conditional exchangeability and an analysis respecting that design.^[ref]

When assigned and received treatments differ, an intention-to-treat analysis estimates an assignment-policy effect. A treatment-receipt effect needs additional assumptions. Allocation concealment, blinded outcome assessment and handling of missing follow-up address other sources of distortion beyond random assignment itself.

For each new eligible participant, compare the imbalance that would result from each treatment assignment across prespecified baseline covariate margins. Assign with a probability favoring the less imbalanced choice, while retaining a random component and allocation concealment. This targets marginal balance when a large number of joint strata makes stratified randomization with blocks inefficient. It is a sequential allocation rule, and inference should respect its design.

A regression discontinuity design compares units immediately on either side of a treatment-assignment cutoff. Its causal interpretation requires potential outcomes to vary continuously through that cutoff in the absence of treatment.

A replicate is an instance of a treatment on a distinct experimental unit. independent replicates permit estimation of response variation between experimental units; subsamples within one experimental unit do not supply additional independent treatment replication. In the pot example, another pot receiving A supplies another A replicate, while another leaf from an existing A pot supplies another observational unit.

Replication in experimental design repeats a treatment on multiple independent experimental units, so that variation between those units can inform a treatment contrast and its standard error. Repeated measurements on one experimental unit can improve measurement precision without providing additional independent treatment replication. The experimental unit is identified by where the treatment is applied, rather than by how many responses are recorded.^[ref]

For a constructed example, grow one plant in each of eight separate pots. Apply treatment A to four pots and treatment B to four pots, without sharing drainage water between pots. Measure the length of three leaves per pot. The pot is the experimental unit; the leaf is the observational unit. There are four treatment replicates per group, eight experimental units overall, and $8\cdot 3=24$ measurements. The three leaves in one pot are nested measurements, because they share the same plant and treatment application. The setup assumes that pots do not affect one another; simply putting them in separate containers does not establish statistical independence.

Randomization chooses which experimental units receive which treatments; replication supplies multiple experimental units receiving the same treatment. These solve different problems. In the balanced allocation above, choose the four A pots uniformly among the $\left(\genfrac{}{}{0ex}{}{8}{4}\right)=70$ possible subsets. A particular pot has probability $1/2$ of receiving A. Given that one pot receives A, a second receives A with conditional probability $3/7$, rather than $1/2$. Thus the assignments are not independent random variables, even though the experimental units can supply independent responses conditional on those assignments in a suitable statistical model.

An actual ecology experiment illustrates why the distinction matters. In Stuart H. Hurlbert's account, twelve experimental ponds initially received zero, fifty or 450 fish, with five, four and three ponds respectively. Preparation included assessing variation between ponds before introducing fish; allocation considered both location and existing differences between ponds. The zero-fish ponds supplied the scientific control. These were repeated treatment applications to ponds, not twelve samples from one pond.^[ref]

The original article followed the southern California ponds for ten months. Its readouts included zooplankton populations and total phytoplankton; it reported decreases in some zooplankton populations and increased total phytoplankton.^[ref] Repeated sampling within a pond helps describe its response through time, while ponds supply treatment replication. Unequal group sizes and initial pond variation matter for the statistical model; the treatment counts alone do not establish equal variances or independent responses.

A response variable is the outcome whose variation is described by a statistical model or whose change is compared across treatments. Its unit, measurement procedure and observation time must be specified. An outcome consisting of a feature count is one response per sketch, not one independent experimental response per feature.

Restricted randomization samples assignments from a specified subset preserving features such as block balance, fixed group sizes or allowable treatment sequences. Inference must respect the chosen allocation scheme rather than treating all label permutations as admissible.

Risk compensation is a possible behavioral response to a prevention intervention: feeling better protected can reduce vigilance or increase exposure to hazards, partially offsetting the intervention's direct protective effect. It is a hypothesis to investigate, not a conclusion established merely by an unfavorable treatment comparison. A randomized controlled trial of the overall package estimates its net assignment effect, which can include both physical protection and behavioral changes.

A row-column design has two crossed partitions of experimental units into rows and columns. Equal treatment proportions in every row and every column make treatment contrasts orthogonal to both centered block spaces. A repeated three-treatment arrangement in a six-by-six array can give a balanced example.

Sensitivity analysis for unmeasured confounding asks how an estimated causal effect changes under explicit departures from the assumed conditional exchangeability. It varies parameters describing the omitted variable's assignment imbalance and outcome effect, rather than assuming that measured covariate balance proves the omission harmless.

For a transparent additive linear structural equation model, take a pretreatment variable $U$ andAssume intervening on $A$ leaves $U$ unchanged, so the constant treatment effect in this model is $\tau$. Subtracting the two conditional outcome means givesThus the adjusted effect for a hypothesized parameter pair is $\tau =D_{\mathrm{obs}}-\gamma {\Delta }_U$. An observed difference five would fall to three when $\gamma =2$ and ${\Delta }_U=1$; explaining it entirely would require $\gamma {\Delta }_U=5$.

The product is a bias term derived for this particular additive model. Other outcome scales and interactions need different formulas. Plausible ranges can be compared with measured pretreatment predictors or external evidence, but the observed treatment-outcome table alone cannot determine the omitted parameters. A sensitivity result quantifies a model-dependent robustness claim; it does not establish that unmeasured confounding is absent.

For treatment history ${\bar{A}}_t$, observed history $H_t$, and final potential outcome $Y(\bar{a})$, sequential exchangeability requiresat every treatment time. Together with consistency of potential outcomes and positivity in causal inference, it identifies longitudinal effects by G-computation.

A split-plot design randomizes one factor to whole plots and another to subplots within each whole plot. Whole-plot treatment effects and subplot treatment effects therefore use different error ANOVA strata. Whole plots provide replication for the first factor; their subplots do not supply extra independent whole-plot replication. Within-whole-plot comparisons can remove a shared additive whole-plot variance component.

Divide participants into strata defined by prespecified baseline prognostic variables and randomize independently within each stratum. Permuted blocks can keep treatment counts close throughout recruitment. This supports balance of the stratification variable between arms by design, while allocation concealment keeps upcoming assignments hidden. Analyses should account for important design strata where appropriate.

A sufficient adjustment set is a collection of pretreatment variables for which treatment and every relevant potential outcome are conditionally independent. Adjustment for that set identifies the corresponding causal contrast under consistency and positivity.

A balanced incomplete block design is symmetric when its number of blocks equals its number of treatments. The identity $bk=tr$ then gives $r=k$. Its square incidence matrix of a set system $N$ obeys $N{N}^T=(r-\lambda )I+\lambda J$, with eigenvalues $r-\lambda$ of multiplicity $t-1$ and $r^2$ of multiplicity one.

Assume treatment receipt gives event risk $p_1$, nonreceipt gives risk $p_0$, and a fraction $c$ in each equally sized randomized arm crosses to the opposite treatment. The two assignment risks are $(1-c)p_1+c{p}_0$ and $c{p}_1+(1-c)p_0$. Subtracting yields the displayed attenuation, with ${\Delta }_{\mathrm{receipt}}=p_0-p_1$. It depends on the stated equal crossover fractions and unchanged receipt-specific risks; it is not a universal formula for every form of treatment contamination.

A technical replicate repeats a measurement or analytical procedure on the same biological preparation. For example, read the length of the same leaf three times to assess measurement error. Measuring three different leaves within one pot instead samples variation within the plant; it should be described explicitly rather than silently equated with repeated readings of one leaf. Neither procedure supplies another pot-level treatment replicate.

A treatment is an intervention assigned or received by a study unit. In causal inference it indexes the unit's potential outcomes.

A belief about the likely consequences of treatment that can influence attention, interpretation, behaviour and symptom experience. Experimental changes in expectation at constant drug exposure can distinguish contextual modulation from differences in administered dose.^[ref]

For $n$ pots per treatment and $m$ leaves per pot, the group sample mean decomposes into two averages:The variance of a sum adds the variances of the independent terms. Every pot random effect has weight $1/n$, whereas each remaining error has weight $1/(nm)$, giving the short proofThis is also the variance of the arithmetic mean of the $n$ pot sample means, each with variance ${\tau }^2+{\sigma }^2/m$. Equal numbers of leaves per pot make the two averaging procedures identical.

If all $nm$ leaf measurements were falsely treated as independent, the predicted variance would instead be $({\tau }^2+{\sigma }^2)/(nm)$. The ratio of correct to false variance isThus pseudoreplication can underestimate a standard error by the square root of this ratio. Equality holds when $m=1$ or ${\tau }^2=0$; sharing a pot creates an error here precisely when the shared influence has positive variance.

Choose ${\tau }^2=4$, ${\sigma }^2=1$, $n=4$ and $m=3$ as constructed model parameters in squared length units. These are assumptions rather than fitted experimental values. For each group,The treatment contrast $\hat{\Delta }={\overline{Y}}_B-{\overline{Y}}_A$ has expected value ${\alpha }_B-{\alpha }_A$. Since the group errors are independent conditional on the allocation, its variance is twice the group variance, namely $13/6$, whereas the false calculation gives $5/6$. Its correct standard error is $\sqrt{13/6}\approx 1.472$ length units; the false value is $\sqrt{5/6}\approx 0.913$. The variance ratio is $13/5=2.6$.

With four pots fixed, increasing $m$ drives the error contribution ${\sigma }^2/(4m)$ towards zero, but the limit of the group variance remains ${\tau }^2/4=1$. Measuring twelve leaves on each of four pots gives $49/48$. Using the same forty-eight measurements on sixteen pots, with three leaves per pot, gives $13/48$. More independent experimental units reduce both contributions. Extra nested measurements are useful for characterizing each experimental unit, but cannot average away its shared random effect. This is why sample collection effort and the number of independent treatment replicates answer different questions.^[ref]