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A randomized complete block design groups similar experimental units into experimental blocks and places every treatment once in each experimental block, independently randomizing treatment allocation within experimental blocks. Blocking removes background between-block variation from within-block treatment comparisons. A balanced incomplete block design has $v$ treatments and $b$ experimental blocks of size $k<v$, with each treatment occurring in $r$ experimental blocks and every distinct treatment pair together in $\lambda$ experimental blocks. Counting treatment occurrences and co-occurrences gives $vr=bk$ and $r(k-1)=\lambda (v-1)$.

A Latin square of order $q$ places each of $q$ treatment symbols once in every row and every column of a $q\times q$ array. This controls two nuisance directions. A Graeco-Latin square superposes two mutually orthogonal Latin squares: each square is Latin, and each ordered pair of symbols from the two squares occurs exactly once. The two symbol factors can then be fitted together with row and column effects. Random permutations of row labels, column labels and treatment symbols provide a suitable randomized allocation without destroying these balances.

For the operator experiment, fit the additive normal linear modelHere $r_i,c_j$ account for the two fabric directions, and ${\tau }_o$ is the operator effect. Additivity, independent equal-variance errors and the normal assumption supply the exact F-test; there is only one observation per cell, so an unrestricted interaction model is not available.

In the analysis of variance for a Latin square, the three centered factor spaces each have dimension $4-1=3$. Together with the intercept the model has rank ten, leaving $16-10=6$ residual statistical degrees of freedom. The corrected total has $16-1=15$. The completed calculation isUnder the null hypothesis ${\tau }_1=\cdots ={\tau }_4=0$, the operator F-statistic isThe upper five-percent critical value for $F_{3,6}$ is $4.76$, so the operator effect is not significant at five percent in this model.

The decision is independent of the order of fitting rows, columns and operators. To prove the required orthogonality, let $u_i$ be any centered row coefficients and $w_o$ any centered operator coefficients. Their observation-space inner product is ${\sum }_{i,j}{u}_i{w}_{o(i,j)}={\sum }_i{u}_i{\sum }_o{w}_o=0$, since every operator occurs once in each row. The same calculation applies to columns and operators, and all row-column pairs occur once as well. Thus the three centered spaces are mutually orthogonal; their projections commute and sequential sums of squares equal adjusted sums of squares in every fitting order.

With machines included, the layout is a Graeco-Latin square: the machine symbols are Latin, and all sixteen operator-machine pairs occur exactly once. Fitin addition to the earlier constraints. The machine space contributes three new statistical degrees of freedom and is orthogonal to the previous factor spaces, so the operator sum of squares remains $18.25$. The residual sum of squares and statistical degrees of freedom becomeHenceThis exceeds $F_{3,3}(0.05)=9.28$ but not $F_{3,3}(0.01)=29.46$. Therefore the operator effect is now significant at five percent, but not at one percent. Adjustment for machines has removed substantial residual variation without altering the operator numerator. This illustrates why a balanced nuisance factor can change precision and significance even when it does not change the estimated treatment contrasts.

Code each factor level by $x_j\in \{-1,1\}$. A nonconstant factorial contrast indexed by a nonempty factor set $A$ has sign column $g_A(x)={\prod }_{j\in A}{x}_j$. Flipping any coordinate in $A$ reverses that sign and pairs the treatment combinations, so exactly $2^{m-1}$ have each sign. Allocating the two signs to two experimental blocks therefore divides the full factorial design into equal experimental blocks. The contrast is confounded with experimental blocks because its column is constant within each experimental block: changing its coefficient and compensating by the two experimental block intercepts leaves every fitted value unchanged. It has no information separate from experimental block differences. Randomize the allocation of the two groups to days and the run order within days.

Write $A,B,C$ for temperature, pressure and catalyst, respectively, with low levels and catalyst one coded minus. In the supplied allocation, $ABC=-1$ on day one and $ABC=1$ on day two. Thus the three-factor interaction $ABC$ is confounded with days. Every other nonconstant factorial column is orthogonal to the day contrast, because its product with $ABC$ is a nonconstant sign column on the full cube and consequently sums to zero.

If all interactions are negligible, the fitted model contains an intercept, one day contrast and the three main effects. The corrected total statistical degrees of freedom partition asThe three residual statistical degrees of freedom are the unused two-factor interaction columns $AB,AC,BC$, pooled as error under the stated negligible-interaction assumption. There is no independent pure-error replication of treatment combinations.

For four days with two runs each, all three main effects can be estimated. One regular allocation pairs each treatment combination with its complete opposite:The block-generating columns can be $AB$ and $AC$; their product $BC$ is also constant in experimental blocks. Thus $AB,AC,BC$ span the three experimental block contrasts, while $A,B,C$ and $ABC$ vary within experimental blocks. The main effects remain mutually orthogonal and separate from the experimental block effects; with an additive main-effect model there is one residual degree of freedom, represented by $ABC$.

For the further request about $AC$, the distinction between regular confounding and unrestricted pairing is important. A regular four-block allocation cannot retain all three main effects and $AC$. Its three confounded columns form a rank-two defining subgroup. To preserve main effects, these columns must lie in $\{AB,AC,BC,ABC\}$. If the subgroup includes $ABC$ and a two-factor column, their product is a main-effect column, which is forbidden. Hence the only permissible nonidentity subgroup is $\{AB,AC,BC\}$, and it necessarily confounds $AC$. This proves impossibility in the usual regular factorial-blocking framework, rather than relying on a count of available statistical degrees of freedom.

The literal request does not explicitly restrict arrangements to regular experimental blocks. If arbitrary pairings are permitted, a nonregular construction can estimate $A,B,C,AC$ together, assuming the other interactions are omitted from the model. An explicit allocation isEvery treatment combination occurs exactly once. Fit one unrestricted intercept per day and the four coefficients ${\beta }_A,{\beta }_B,{\beta }_C,{\beta }_{AC}$. By estimability from within-block differences, subtracting the second run from the first in each experimental block removes all day effects and yields the coefficient matrixThus all four coefficients are uniquely determined from the four day differences. In this broader design class the answer is yes, under the reduced four-effect model. The resulting fit is saturated: four experimental block intercepts plus four treatment coefficients use all eight observations, leaving no residual estimate of error variance. Replication or external error information would be needed for inference. This does not contradict the impossibility for regular orthogonal confounding, and it does not claim simultaneous unbiased estimation when arbitrary additional interactions are retained.

An orthogonal block design has treatment contrasts orthogonal to block contrasts after removing the grand mean. This is a statement about vectors on the experimental units, with the usual inner product; the two full spaces are not orthogonal because both contain the constant vector.

For a counting criterion, let $n_{ij}$ count experimental units receiving treatment $i$ in block $j$, let $r_i={\sum }_j{n}_{ij}$, let $k_j={\sum }_i{n}_{ij}$, and let $n={\sum }_i{r}_i$. The inner product of the centered indicators for treatment $i$ and block $j$ is $n_{ij}-r_i{k}_j/n$. ConsequentlyIn particular, equal-sized blocks must contain each treatment in the same proportion. Under an additive block-and-treatment model, adjustment for blocks then does not change the fitted treatment contrasts.

Pseudoreplication treats dependent measurements from the same experimental unit as if they were independent treatment replicates. It exaggerates the effective sample size and commonly makes standard errors too small. In the pot example of replication in experimental design, counting twelve leaves per group as twelve independent treatment replicates ignores the four containing pots. The variance of nested measurements quantifies the resulting understatement of uncertainty. Nested measurements themselves are useful; pseudoreplication is the error of using them as independent replicates for the wrong level of inference.^[ref]

A randomized complete block design places every treatment in every block, with a common replication pattern, and uses independent within-block randomization. The usual basic version has one occurrence of each treatment per block; equal repeated occurrences give a replicated complete-block version. Such equal-proportion designs are orthogonal block designs.

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.