block experiments

Teach yourself statistics

Randomized Block Experiment: Example

This lesson shows how to use analysis of variance to analyze and interpret data from a randomized block experiment. To illustrate the process, we walk step-by-step through a real-world example.

Computations for analysis of variance are usually handled by a software package. For this example, however, we will do the computations "manually", since the gory details have educational value.

Prerequisites: The lesson assumes general familiarity with randomized block designs. If you are unfamiliar with randomized block designs or with terms like blocks , blocking , and blocking variables , review the previous lessons:

• Randomized Block Designs
• Randomized Block Experiments: Data Analysis

Problem Statement

As part of a randomized block experiment, a researcher tests the effect of three teaching methods on student performance. The researcher selects subjects randomly from a student population. The researcher assigns subjects to six blocks of three, such that students within the same block have the same (or similar) IQ. Within each block, each student is randomly assigned to a different teaching method.

At the end of the term, the researcher collects one test score (the dependent variable) from each subject, as shown in the table below:

Table 1. Dependent Variable Scores

In conducting this experiment, the researcher has two research questions:

• Does teaching method have a significant effect on student performance (as measured by test score)?
• How strong is the effect of teaching method on the student performance?

To answer these questions, the researcher uses analysis of variance.

Analytical Logic

To implement analysis of variance with an independent groups, randomized block experiment, a researcher takes the following steps:

• Specify a mathematical model to describe how main effects and the blocking variable influence the dependent variable.
• Write statistical hypotheses to be tested by experimental data.
• Specify a significance level for a hypothesis test.
• Compute the grand mean and marginal means for the independent variable and for the blocking variable.
• Compute sums of squares for each effect in the model.
• Find the degrees of freedom associated with each effect in the model.
• Based on sums of squares and degrees of freedom, compute mean squares for each effect in the model.
• Find the expected value of the mean squares for each effect in the model.
• Compute a test statistic for the independent variable and a test statistic for the blocking variable, based on observed mean squares and their expected values.
• Find the P value for each test statistic.
• Accept or reject null hypotheses , based on P value and significance level.
• Assess the magnitude of effect, based on sums of squares.

Below, we'll explain how to implement each step in the analysis.

Mathematical Model

For every experimental design, there is a mathematical model that accounts for all of the independent and extraneous variables that affect the dependent variable. Here is a mathematical model for an independent groups, randomized block experiment:

X i j = μ + β i + τ j + ε ij

where X i j is the dependent variable score (in this example, the test score) for the subject in block i that receives treatment j , μ is the population mean, β i is the effect of Block i ; τ j is the effect of Treatment j ; and ε ij is the experimental error (i.e., the effect of all other extraneous variables).

For this model, it is assumed that ε ij is normally and independently distributed with a mean of zero and a variance of σ ε 2 . The mean ( μ ) is constant.

Note: Unlike the model for a full factorial experiment, the model for a randomized block experiment does not include an interaction term. That is, the model assumes there is no interaction between block and treatment effects.

Statistical Hypotheses

With a randomized block experiment, it is possible to test both block ( β  i  ) and treatment ( τ  j  ) effects. Here are the null hypotheses (H 0 ) and alternative hypotheses (H 1 ) for each effect.

H 0 : β i = 0 for all i

H 1 : β i ≠ 0 for some i

H 0 : τ j = 0 for all j

H 1 : τ j ≠ 0 for some j

With a randomized block experiment, the main hypothesis test of interest is the test of the treatment effect(s). For instance, in this example the experimenter is primarily interested in the effect of teaching method on student performance (i.e., test score).

Block effects are of less intrinsic interest, because a blocking variable is thought to be a nuisance variable that is only included in the experiment to control for a potential source of undesired variation. In this example, IQ is a potential nuisance variable.

Significance Level

The significance level (also known as alpha or α) is the probability of rejecting the null hypothesis when it is actually true. The significance level for an experiment is specified by the experimenter, before data collection begins. Experimenters often choose significance levels of 0.05 or 0.01. For this experiment, we'll assume that the experimenter chose 0.05 as the significance level.

A significance level of 0.05 means that there is a 5% chance of rejecting the null hypothesis when it is true. A significance level of 0.01 means that there is a 1% chance of rejecting the null hypothesis when it is true. The lower the significance level, the more persuasive the evidence needs to be before an experimenter can reject the null hypothesis.

Mean Scores

Analysis of variance for a randomized block experiment begins by computing a grand mean and marginal means for independent variables and for blocks. Here are computations for the various means, based on dependent variable scores from Table 1:

• Marginal means for treatment levels. The mean for treatment level j (  X   .  j  ) is computed as follows: X   .  j   = ( 1 / n ) n Σ i=1 ( X  i j  ) X   .  1   = ( 1 / 6 ) 6 Σ i=1 ( X  i 1  ) = 87.33 X   .  2   = ( 1 / 6 ) 6 Σ i=1 ( X  i 2  ) = 87.50 X   .  3   = ( 1 / 6 ) 6 Σ i=1 ( X  i 3  ) = 88.33
• Marginal means for blocks. The mean for block i (  X  i  .   ) is computed as follows: X  i  .    = ( 1 / k ) k Σ j=1 ( X  i j  ) X  1  .    = ( 1 / 3 ) 3 Σ j=1 ( X  1 j  ) = 84.67 X  2  .    = ( 1 / 3 ) 3 Σ j=1 ( X  2 j  ) = 86.67 X  3  .    = ( 1 / 3 ) 3 Σ j=1 ( X  3 j  ) = 87.00 X  4  .    = ( 1 / 3 ) 3 Σ j=1 ( X  4 j  ) = 88.67 X  5  .    = ( 1 / 3 ) 3 Σ j=1 ( X  5 j  ) = 88.67 X  6  .    = ( 1 / 3 ) 3 Σ j=1 ( X  6 j  ) = 90.67

In the equations above, N is the total sample size; n is the number of blocks, and k is the number of treatment levels.

Sums of Squares

A sum of squares is the sum of squared deviations from a mean score. A randomized block design makes use of four sums of squares:

• Sum of squares for treatments. The sum of squares for treatments (SSTR) measures variation of the marginal means of treatment levels (  X  j  ) around the grand mean (  X  ). It can be computed from the following formula: SSTR = n k Σ j=1 (  X  j  -  X  ) 2 SSTR = 6 3 Σ j=1 (  X  j  -  X  ) 2 = 3.44
• Sum of squares for blocks. The sum of squares for blocks (SSB) measures variation of the marginal means of blocks (  X  i  ) around the grand mean (  X  ). It can be computed from the following formula: SSB = k n Σ i=1 (  X  i  -  X  ) 2 SSB = 3 6 Σ i=1 (  X  i  -  X  ) 2 = 64.28
• Error sum of squares. The error sum of squares (SSE) measures variation of all scores ( X  i j  ) attributable to extraneous variables. It can be computed from the following formula: SSE = n Σ i=1 k Σ j=1 ( X  i j   -  X   i   -  X   j   +  X  ) 2 SSE = 6 Σ i=1 3 Σ j=1 ( X  i j   -  X   i   -  X   j   +  X  ) 2 = 3.89
• Total sum of squares. The total sum of squares (SST) measures variation of all scores ( X  i j  ) around the grand mean (  X  ). It can be computed from the following formula: SST = n Σ i=1 k Σ j=1 ( X  i j  -  X  ) 2 SST = 6 Σ i=1 3 Σ j=1 ( X  i j  -  X  ) 2 = 71.61

In the formulas above, n is the number of blocks, and k is the number of treatment levels. And the total sum of squares is equal to the sum of the component sums of squares, as shown below:

SST = SSTR + SSB + SSE

SST = 3.44 + 64.28 + 3.89 = 71.61

Degrees of Freedom

The term degrees of freedom (df) refers to the number of independent sample points used to compute a statistic minus the number of parameters estimated from the sample points.

The degrees of freedom used to compute the various sums of squares for an independent groups, randomized block experiment are shown in the table below:

Notice that there is an additive relationship between the various sums of squares. The degrees of freedom for total sum of squares (df TOT ) is equal to the degrees of freedom for the treatment sum of squares (df TR ) plus the degrees of freedom for the blocks sum of squares (df B ) plus the degrees of freedom for the error sum of squares (df E ). That is,

df TOT = df TR + df B + df E

df TOT = 2 + 5 + 7 = 17

Mean Squares

A mean square is an estimate of population variance. It is computed by dividing a sum of squares (SS) by its corresponding degrees of freedom (df), as shown below:

MS = SS / df

To conduct analysis of variance with a randomized block experiment, we are interested in three mean squares:

MS T = SSTR / df TR

MS T = 3.44 / 2 = 1.72

MS B = SSB / df B

MS B = 64.28 / 5 = 12.86

MS E = SSE / df E

MS E = 3.89 / 10 = 0.39

Expected Value

The expected value of a mean square is the average value of the mean square over a large number of experiments.

Statisticians have derived formulas for the expected value of mean squares, assuming the mathematical model described earlier is correct. Those formulas appear below:

In the table above, MS T is the mean square for treatments; MS B is the mean square for blocks; and MS E is the error mean square.

Test Statistics

The main data analysis goal for this experiment is to test the hypotheses that we stated earlier (see Statistical Hypotheses ). That will require the use of test statistics. Let's talk about how to compute test statistics for this study and how to interpret the statistics we compute.

How to Compute Test Statistics

Suppose we want to test the significance of an independent variable or a blocking variable in a randomized block experiment. We can use the mean squares to define a test statistic F for each source of variation, as shown in the table below:

Using formulas from the table with data from this randomized block experiment, we can compute an F ratio for treatments ( F T  ) and an F ratio for blocks ( F B  ).

F T = MS T / MS E = 1.72/0.39 = 4.4

F B = MS B / MS E = 12.86/0.39 = 33.0

How to Interpret Test Statistics

Consider the F ratio for the treatment effect in this randomized block experiment. For convenience, we display once again the table that shows expected mean squares and F ratio formulas:

Notice that numerator of the F ratio for the treatment effect should equal the denominator when the variation due to the treatment ( σ 2  T ) is zero (i.e., when the treatment does not affect the dependent variable). And the numerator should be bigger than the denominator when the variation due to the treatment is not zero (i.e., when the treatment does affect the dependent variable).

The F ratio for the blocking variable works the same way. When the blocking variable does not affect the dependent variable, the numerator of the F ratio should equal the denominator. Otherwise, the numerator should be bigger than the denominator.

Each F ratio is a convenient measure that we can use to test the null hypothesis about the effect of a source (the treatment or the blocking variable) on the dependent variable. Here's how to conduct the test:

• When the F ratio is close to one, the numerator of the F ratio is approximately equal to the denominator. This indicates that the source did not affect the dependent variable, so we cannot reject the null hypothesis.
• When the F ratio is significantly greater than one, the numerator is bigger than the denominator. This indicates that the source did affect the dependent variable, so we must reject the null hypothesis.

What does it mean for the F ratio to be significantly greater than one? To answer that question, we need to talk about the P-value.

Warning: Recall that this analysis assumes that the interaction between blocking variable and independent variable is zero. If that assumption is incorrect, the F ratio for a fixed-effects variable will be biased. It may indicate that an effect is not significant, when it truly is significant.

In an experiment, a P-value is the probability of obtaining a result more extreme than the observed experimental outcome, assuming the null hypothesis is true.

With analysis of variance for a randomized block experiment, the F ratios are the observed experimental outcomes that we are interested in. So, the P-value would be the probability that an F ratio would be more extreme (i.e., bigger) than the actual F ratio computed from experimental data.

How does an experimenter attach a probability to an observed F ratio? Luckily, the F ratio is a random variable that has an F distribution . The degrees of freedom (v 1 and v 2 ) for the F ratio are the degrees of freedom associated with the mean squares used to compute the F ratio.

For example, consider the F ratio for a treatment effect. That F ratio ( F T  ) is computed from the following formula:

F T = F(v 1 , v 2 ) = MS T / MS E

MS T (the numerator in the formula) has degrees of freedom equal to df TR  ; so for F T  , v 1 is equal to df TR  . Similarly, MS E (the denominator in the formula) has degrees of freedom equal to df E  ; so for F T  , v 2 is equal to df E  . Knowing the F ratio and its degrees of freedom, we can use an F table or Stat Trek's free F distribution calculator to find the probability that an F ratio will be bigger than the actual F ratio observed in the experiment.

To illustrate the process, let's find P-values for the treatment variable and for the blocking variable in this randomized block experiment.

Treatment Variable P-Value

From previous computations, we know the following:

• The observed value of the F ratio for the treatment variable is 4.4.
• The degrees of freedom (v 1 ) for the treatment variable mean square (MS T ) is 2.
• The degrees of freedom (v 2 ) for the error mean square (MS E ) is 10.

Therefore, the P-value we are looking for is the probability that an F with 2 and 10 degrees of freedom is greater than 4.4. We want to know:

P [ F(2, 10) > 4.4 ]

Now, we are ready to use the F Distribution Calculator . We enter the degrees of freedom (v1 = 2) for the treatment mean square, the degrees of freedom (v2 = 10) for the error mean square, and the F value (4.4) into the calculator; and hit the Calculate button.

The calculator reports that the probability that F is greater than 4.4 equals about 0.04. Hence, the correct P-value for the treatment variable is 0.04.

Blocking Variable P-Value

The process to compute the P-value for the blocking variable is exactly the same as the process used for the treatment variable. From previous computations, we know the following:

• The observed value of the F ratio for the blocking variable is 33.

F B = F(v 1 , v 2 ) = MS B / MS E

• The degrees of freedom (v 1 ) for the blocking variable mean square (MS B ) is 5.

Therefore, the P-value we are looking for is the probability that an F with 5 and 10 degrees of freedom is greater than 33. We want to know:

P [ F(5, 10) > 33 ]

Now, we are ready to use the F Distribution Calculator . We enter the degrees of freedom (v1 = 5) for the block mean square, the degrees of freedom (v2 = 10) for the error mean square, and the F value (33) into the calculator; and hit the Calculate button.

The calculator reports that the probability that F is greater than 33 is about 0.00001. Hence, the correct P-value is 0.00001.

Interpretation of Results

Having completed the computations for analysis, we are ready to interpret results. We begin by displaying key findings in an ANOVA summary table. Then, we use those findings to (1) test hypotheses and (2) assess the magnitude of effects.

ANOVA Summary Table

It is traditional to summarize ANOVA results in an analysis of variance table. Here, filled with key results, is the analysis of variance table for the randomized block experiment that we have been working on.

Analysis of Variance Table

This ANOVA table provides all the information that we need to (1) test hypotheses and (2) assess the magnitude of treatment effects.

Hypothesis Test

Recall that the experimenter specified a significance level of 0.05 for this study. Once you know the significance level and the P-values, the hypothesis tests are routine. Here's the decision rule for accepting or rejecting a null hypothesis:

• If the P-value is bigger than the significance level, accept the null hypothesis.
• If the P-value is equal to or smaller than the significance level, reject the null hypothesis.

A "big" P-value for a source of variation (an independent variable or a blocking variable) indicates that the source did not have a statistically significant effect on the dependent variable. A "small" P-value indicates that the source did have a statistically significant effect on the dependent variable.

The P-value (shown in the last column of the ANOVA table) is the probability that an F statistic would be more extreme (bigger) than the F ratio shown in the table, assuming the null hypothesis is true. When a P-value for an independent variable or a blocking variable is bigger than the significance level, we accept the null hypothesis for the effect; when it is smaller, we reject the null hypothesis.

Based on the P-values in the table above, we can draw the following conclusions:

• The P-value for treatments (i.e., the independent variable) is 0.04. Since the P-value is smaller than the significance level (0.05), we reject the null hypothesis that the independent variable (training method) has no effect on the dependent variable.
• The P-value for the blocking variable is less than 0.01. Since this P-value is also smaller than the significance level (0.05), we reject the null hypothesis that the blocking variable (IQ) has no effect on the dependent variable.

In addition, two other points are worthy of note:

• The fact that the blocking variable (IQ) is statistically significant is good news in a randomized block experiment. It confirms the suspicion that the blocking variable was a nuisance variable that could have obscured effects of the dependent variable. And it justifies the decision to use a randomized block experiment to control nuisance effects of IQ.
• The independent variable (training method) was also statistically significant with a P-value of 0.04. Had the experimenter used a different design that did not control the nuisance effect of IQ, the experiment might not have produced a significant effect for the independent variable.

Magnitude of Effect

The hypothesis tests tell us whether sources of variation in our experiment had a statistically significant effect on the dependent variable, but the tests do not address the magnitude of the effect. Here are some issues:

• When the sample size is large, you may find that even small effects (indicated by a small F ratio) are statistically significant.
• When the sample size is small, you may find that even big effects are not statistically significant.
• When the blocking variable in a randomized block design is strongly correlated with the dependent variable, you may find that even small treatment effects are statistically significant.

With this in mind, it is customary to supplement analysis of variance with an appropriate measure of effect size. Eta squared (η 2 ) is one such measure. Eta squared is the proportion of variance in the dependent variable that is explained by a source of variation. The eta squared formula for an independent variable or a blocking variable is:

η 2 = SS SOURCE / SST

where SS SOURCE is the sum of squares for a source of variation (i.e., an independent variable or a blocking variable) and SST is the total sum of squares.

Using sum of squares entries from the ANOVA table, we can compute eta squared for the treatment variable ( η 2 T  ) and for the blocking variable ( η 2 B  ).

η 2 T = SSTR / SST = 3.44 / 71.61 = 0.05

η 2 B = SSB / SST = 64.28 / 71.61 = 0.90

The treatment variable (test method) accounted for about 5% of the variance in test performance, and the blocking variable (IQ) accounted for about 90% of the variance in test performance. Based on these findings, an experimenter might conclude:

• IQ accounted for most of the variance in test performance.
• Even though the test method effect was statistically significant, test method accounted for only a small proportion of test variation.

Note: Given the very strong nuisance effect of IQ, it is likely that a different experimental design would not have revealed a statistically significant effect for test method.

An Easier Option

In this lesson, we showed all of the hand calculations for analysis of variance with a randomized block experiment. In the real world, researchers seldom conduct analysis of variance by hand. They use statistical software. In the next lesson, we'll demonstrate how to conduct the same analysis of the same problem with Excel. Hopefully, we'll get the same result.

Blocking in experimental design

Are you wondering what blocking is in experimental design? Then you are in the right place! In this article we tell you everything you need to know about blocking in experimental design. First we discuss what blocking is and what its main benefits are. After that, we discuss when you should use blocking in your experimental design. Finally, we walk through the steps that you need to take in order to implement blocking in your own experimental design.

What is blocking in experimental design?

What is blocking in experimental design? Blocking is one of those concepts that can be difficult to grasp even if you have already been exposed to it once or twice. Why is that? Because the specific details of how blocking is implemented can vary a lot from one experiment to another. For that reason, we will start off our discussion of blocking by focusing on the main goal of blocking and leave the specific implementation details for later.

At a high level, blocking is used when you are designing a randomized experiment to determine how one or more treatments affect a given outcome . More specifically, blocking is used when you have one or more key variables that you need to ensure are similarly distributed within your different treatment groups . If you find yourself in this situation, blocking is a method you can use to determine how to allocate your observational units (or the individual subjects in your experiment) into your different treatment groups in a way that ensures that the distribution of these key variables is the same across all of your treatment groups.

So what types of variables might you need to balance across your treatment groups? Blocking is most commonly used when you have at least one nuisance variable . A nuisance variable is an extraneous variable that is known to affect your outcome variable that you cannot otherwise control for in your experiment design. If nuisance variables are not evenly balanced across your treatment groups then it can be difficult to determine whether a difference in the outcome variable across treatment groups is due to the treatment or the nuisance variable.

So how is blocking performed at a high level? It is a two step process. First the individual observational units are split into blocks of observational units that have similar values for the key variables that you want to balance over. After that, the observational units from each block are evenly allocated into treatment groups in a way such that each treatment group is allocated similar numbers of observational units from each block.

When should you use blocking?

When should you use blocking in your experimental design? In general you should use blocking if you are designing an experiment that fits the following two criteria.

• There are key variables(s) you need to balance across treatment groups . The first criteria that needs to be met in order for blocking to make sense for your experimental design is that you need to have at least one variable that needs to be equally distributed across your different treatment groups. If you are not in this situation, then you generally do not need to perform blocking.
• You have a relatively small sample size . The second criteria is that you are working with a relatively small sample size. So how small is small? That can vary depending on the type of experiment you are performing. As a general rule, you should use blocking when your sample size is small enough that you are not confident that simply randomizing your observations into treatment groups without performing any blocking will result in treatment groups that are balanced across the key variables called out in the previous criteria.

A simple example where blocking may be useful

As an example, imagine you were running a study to test two different brands of soccer cleats to determine whether soccer players run faster in one type of cleats or the other. Further, imagine that some of the soccer players you are testing your cleats on only have grass fields available to them and others only have artificial grass or turf fields available to them. Now, say you have reason to believe that athletes tend to run 10% faster on turf fields than grass fields.

In this case, an observational unit is a soccer player and your treatment is the type of soccer cleats that a soccer player wears. The main outcome of your study is how fast an athlete can run. You also have a nuisance variable which is the type of field a soccer is running on when their time is recorded. In this experimental design, you need to ensure that the proportion of players running on turf fields is similar for each treatment group.

Why is it important to make sure that the number of soccer players running on turf fields and grass fields is similar across different treatment groups? Because the type of field is another variable that is known to impact the speed a player runs at and if this variable is not balanced across treatment groups then you will not know whether any changes in your outcome between treatment groups are due to the type of soccer cleat or the type of field.

Imagine an extreme scenario where all of the athletes that are running on turf fields get allocated into one group and all of the athletes that are running on grass fields are allocated into the other group. In this case it would be near impossible to separate the impact that the type of cleats has on the run times from the impact that the type of field has.

How does blocking work in experimental design?

So how does blocking work in experimental design? Here are the main steps you need to take in order to implement blocking in your experimental design.

1. Choose your blocking factor(s)

The first step of implementing blocking is deciding what variables you need to balance across your treatment groups. We will call these blocking factors . Here are some examples of what your blocking factor might look like.

• Nuisance variable(s) . It is most common for your blocking factors to be nuisance variables that affect your outcome. It is important to ensure that these variables are balanced across your treatment groups so that you can feel assured that the changes you see in your outcome across treatment groups are a result of your treatments and not differences in a nuisance variable.
• The outcome . In some scenarios, you might also want to use your outcome variable as a blocking factor. For example, if there is a large skew in your outcome variable and 10% of observations have much higher values than the rest of the observations then it might make sense to ensure that these outlying observations with high values are equally distributed across groups.

2. Allocate you observations into blocks

The next thing you need to do after you determine your blocking factors is allocate your observations into blocks. To simplify things, we will assume that you have one main blocking factor that you want to balance over.

• One block for each level of a variable . If your main blocking factor is a categorical variable that only has a few levels then one common choice is to have one block per level of that variable. For example, in the previous example where the main blocking factor was a categorical variable with two levels that represented different types of soccer fields, a common choice would be to have two blocks. One block would contain soccer players that ran on turf and would contain soccer players that ran on grass.
• A few blocks based on standard cutoffs . But what if your main blocking factor is a continuous variable? If your blocking factor is a continuous variable and there are any standard cutoffs that are used to group observations into levels for other purposes then you should feel free to use those cutoffs to create blocks. For example, if your main blocking factor was blood pressure then you could use standard cutoffs for classifying low, average, and high blood pressure to classify your observations into three blocks.
• A few blocks based on quantiles . But what if your blocking factor is continuous and there are no obvious cutoffs to use? Then you can also create blocks based on quantiles of your blocking factor. For example, you can create one block with the observations that have values for your blocking factor that are in the top 50th percentile and another with observations that are in the bottom 50th percentile.
• Many small blocks that contain one observation per treatment group . A fourth option is to create many small blocks that contain one observation per treatment group. This is a somewhat non-traditional setup, but it might be useful if you have a continuous blocking factor that has a highly skewed distribution and it has some values that are much higher or lower than the average value. One way to handle this is to sort your observations by the blocking factor then go down the list and assign small blocks with one observation per treatment group. For example, if you had two treatment groups then you would assign the observations with the two highest values for the blocking factor to one block, the observations with the third and fourth highest values to another, and so on. This will ensure that the distribution of your blocking factor is balanced across treatment groups.

3. Allocate your observations into treatments

The final step in the blocking process is allocating your observations into different treatment groups. In most blocking designs, this is relatively straightforward. All you have to do is go through your blocks one by one and randomly assign observations from each block to treatment groups in a way such that each treatment group gets a similar number of observations from each block.

Related articles

• How to choose an experimental design
• When to use CUPED to reduce variance in an experiment?

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Randomized Block Design: An Introduction

A randomized block design is a type of experiment where participants who share certain characteristics are grouped together to form blocks , and then the treatment (or intervention) gets randomly assigned within each block.

The objective of the randomized block design is to form groups where participants are similar, and therefore can be compared with each other.

An Example: Blocking on gender

Santana-Sosa et al. set to study the effect of a 12-week physical training program on the ability to perform daily activities in Alzheimer’s disease patients.

And because physical capability differs substantially between males and females, the authors decided to block on gender.

Why gender?

Because gender satisfies the following 2 conditions:

• It will certainly affect the test measurements (i.e. the outcome)
• It is not an interesting variable in itself to be studied (as it is better to study variables that CAN be manipulated by patients in order to improve their physical ability)

Therefore, it would be very useful to block on gender in order to remove its effect as an alternative explanation of the outcome.

16 patients participated in the study: 10 females and 6 males.

The blocks were created as follows:

When to use a randomized block design?

Use a randomized block design if:

• An unwanted/uninteresting variable affects the outcome.
• This variable can be measured.
• Your sample size is not large enough for simple randomization to produce equal groups (see Randomized Block Design vs Completely Randomized Design ).

What happens if you don’t block?

If you don’t block, all the variability associated with the blocks end up in the error term which makes it hard to detect an effect when in fact there is one.

So if you don’t block, you will reduce the statistical power of the study.

In other words, when the error term is inflated, the percentage of variability explained by the statistical model diminishes. Therefore, the model becomes a less accurate representation of reality.

BOTTOM LINE:

Blocking reduces the error term, making your statistical model more predictive and more generalizable.

Limitations of the randomized block design

Here are some of the limitations of the randomized block design and how to deal with them:

1. We cannot block on too many variables

As the number of blocking variables increases, the number of blocks created increases, approaching the sample size — i.e. the number of participants in each block would be very low, creating a problem for the randomized block design.

2. Difficulty in choosing the number of blocks

Since the number of blocks is the number of categories of the blocking variable, choosing a blocking variable that does not have too much or too few categories will be important because:

• If you used fewer blocks than you need: You may have a hard time maintaining homogeneity within each block.
• If you used more blocks than your sample size allows: You may end up with few participants in each block to be properly randomized to treatment options.

When in doubt, decide on the number of blocks based on previous literature.

3. Difficulty in detecting/measuring the blocking variable

We will divide this section into 3 categories [ Source: Design and Analysis of Experiments ]:

• When the blocking variable is known and controllable : Solution: Use a randomized block design.
• When the blocking variable is known but uncontrollable : Solution: Try to adjust for it in the statistical analysis.
• When the blocking variable is unknown : Solution: Use simple randomization in the hope that it will produce equal and comparable study groups.
• Lewis-Beck M, Bryman A, Liao T. The SAGE Encyclopedia of Social Science Research Methods .; 2004. doi:10.4135/9781412950589
• Lawson J. Design and Analysis of Experiments with R . 1 edition. Chapman and Hall/CRC; 2014.
• Design of Experiments . Coursera. Accessed August 18, 2020.

Further reading

• Matched Pairs Design
• Posttest-Only Control Group Design
• Pretest-Posttest Control Group Design
• Experimental vs Quasi-Experimental Design

5   Complete Block Designs

5.1 introduction.

In many situations we know that our experimental units are not homogeneous. Making explicit use of the special structure of the experimental units typically helps reduce variance (“getting a more precise picture”). In your introductory course, you have learned how to apply the paired \(t\) -test. It was used for situations where two treatments were applied on the same “object” or “subject.” Think for example of applying two treatments, in parallel, on human beings (like the application of two different eye drop types, each applied in one of the two eyes). We know that individuals can be very different. Due to the fact that we apply both treatments on the same subject, we get a “clear picture” of the treatment effect within every subject by taking the difference of the response values corresponding to the two treatments. This makes the subject-to-subject variability completely disappear. We also say that we block on subjects or that an individual subject is a block. This is also illustrated in Figure  5.1 (left): The values of the same subject are connected with a line. With the help of these lines, it is obvious that the response value corresponding to treatment is larger than the value corresponding to the control group, within a subject. This would be much less obvious if the data would come from two independent groups. In this scenario, we would have to delete the lines and would be confronted with the whole variability between the different subjects.

We will now extend this way of thinking to the situation \(g > 2\) , where \(g\) is the number of levels of our treatment factor (as in Chapter  2 ). An illustration of the basic idea can be found in Figure  5.1 (right). We simply consider situations where we have more than two levels on the \(x\) -axis. The basic idea stays the same: Values coming from the same block (here, subject) can be connected with a line. This helps both our eyes and the statistical procedure in getting a much clearer picture of the treatment effect.

5.2 Randomized Complete Block Designs

Assume that we can divide our experimental units into \(r\) groups, also known as blocks , containing \(g\) experimental units each. Think for example of an agricultural experiment at \(r\) different locations having \(g\) different plots of land each. Hence, a block is given by a location and an experimental unit by a plot of land. In the introductory example, a block was given by an individual subject.

The randomized complete block design (RCBD) uses a restricted randomization scheme : Within every block, e.g., at each location, the \(g\) treatments are randomized to the \(g\) experimental units, e.g., plots of land. In that context, location is also called the block factor . The design is called complete because we observe the complete set of treatments within every block (we will later also learn about incomplete block designs where this is not the case anymore, see Chapter  8 ).

Note that blocking is a special way to design an experiment, or a special “flavor” of randomization. It is not something that you use only when analyzing the data. Blocking can also be understood as replicating an experiment on multiple sets, e.g., different locations, of homogeneous experimental units, e.g., plots of land at an individual location. The experimental units should be as similar as possible within the same block, but can be very different between different blocks. This design allows us to fully remove the between-block variability, e.g., variability between different locations, from the response because it can be explained by the block factor. Hence, we get a much clearer picture for the treatment factor. The randomization step within each block makes sure that we are protected from unknown confounding variables. A completely randomized design (ignoring the blocking structure) would typically be much less efficient as the data would be noisier, meaning that the error variance would be larger. In that sense, blocking is a so-called variance reduction technique.

Typical block factors are location (see example above), day (if an experiment is run on multiple days), machine operator (if different operators are needed for the experiment), subjects, etc.

Blocking is very powerful and the general rule is, according to George Box ( Box, Hunter, and Hunter 1978 ) :

“Block what you can; randomize what you cannot.”

In the most basic form, we assume that we do not have replicates within a block. This means that we only observe every treatment once in each block.

The analysis of a randomized complete block design is straightforward. We treat the block factor as “just another” factor in our model. As we have no replicates within blocks, we can only fit a main effects model of the form \[ Y_{ij} = \mu + \alpha_i + \beta_j + \epsilon_{ij}, \] where the \(\alpha_i\) ’s are the treatment effects and the \(\beta_j\) ’s are the block effects with the usual side constraints. In addition, we have the usual assumptions on the error term \(\epsilon_{ij}\) . According to this model, we implicitly assume that blocks only cause additive shifts. Or in other words, the treatment effects are always the same, no matter what block we consider. This assumption is usually made based on domain knowledge. If there would be an interaction effect between the block and the treatment factor, the result would be very difficult to interpret. Most often, this is due to unmeasured variables, e.g., different soil properties at different locations.

We consider an example which is adapted from Venables and Ripley ( 2002 ) , the original source is Yates ( 1935 ) (we will see the full data set in Section  7.3 ). At six different locations (factor block ), three plots of land were available. Three varieties of oat (factor variety with levels Golden.rain , Marvellous and Victory ) were randomized to them, individually per location. The response was yield (in 0.25lbs per plot). A conceptual layout of the design can be found in Table  5.1 .

The data can be read as follows:

We use the usual aov function with a model including the two main effects block and variety . It is good practice to write the block factor first; in case of unbalanced data, we would get the effect of variety adjusted for block in the sequential type I output of summary , see Section  4.2.5 and also [C]hapter Chapter 8 ].

We first focus on the p-value of the treatment factor variety . Although we used a randomized complete block design, we cannot reject the null hypothesis that there is no overall effect of variety (a reason might be low power, as we only have 10 degrees of freedom left for the error term). Typically, we are not inspecting the p-value of the block factor block . There is some historic debate why we should not do this, mainly because of the fact that we did not randomize blocks to experimental units. In addition, we already knew (or hoped) beforehand that blocks are different. Hence, such a finding would not be of great scientific relevance. However, we can do a quick check to verify whether blocking was efficient or not. We would like the block factor to explain a lot of variation, hence if the mean square of the block factor is larger than the error mean square \(MS_E\) we conclude that blocking was efficient (compared to a completely randomized design). Here, this is the case as \(794 > 150\) . See Kuehl ( 2000 ) for more details and a formal definition of the relative efficiency which compares the efficiency of a randomized complete block design to a completely randomized design. If blocking was not efficient, we would still leave the block factor in the model (as the model must follow the design that we used), but we might plan not to use blocking in a future similar experiment because it didn’t help reduce variance and only cost us degrees of freedom.

Instead of a single treatment factor, we can also have a factorial treatment structure within every block. Think for example of a design as outlined in Table  5.2 .

In R , we would model this as y ~ Block + A * B . In such a situation, we can actually test the interaction between \(A\) and \(B\) even if every level combination of \(A\) and \(B\) appears only once in every block. Why? Because we have multiple blocks, we have multiple observations for every combination of the levels of \(A\) and \(B\) . Of course, the three-way interaction cannot be added to the model.

Interpretation of the coefficients of the corresponding models, residual analysis, etc. is done “as usual.” The only difference is that we do not test the block factor for statistical significance, but for efficiency.

5.3 Nonparametric Alternatives

For a complete block design with only one treatment factor and no replicates, there is a rank sum based test, the so-called Friedman rank sum test which is implemented in function friedman.test . Among others, it also has a formula interface, where the block factor comes after the symbol “ | ”, i.e., for the oat example the formula would be yield ~ variety | block :

5.4 Outlook: Multiple Block Factors

We can also block on more than one factor. A special case is the so-called Latin Square design where we have two block factors and one treatment factor having \(g\) levels each (yes, all of them!). Hence, this is a very restrictive assumption. Consider the layout in Table  5.3 where we have a block factor with levels \(R_1\) to \(R_4\) (“rows”), another block factor with levels \(C_1\) to \(C_4\) (“columns”) and a treatment factor with levels \(A\) to \(D\) (a new notation as now the letter is actually the level of the treatment factor). In a Latin Square design, each treatment (Latin letters) appears exactly once in each row and once in each column. A Latin Square design blocks on both rows and columns simultaneously . We also say it is a row-column design . If we ignore the columns of a Latin Square designs, the rows form an RCBD; if we ignore the rows, the columns form an RCBD.

For example, if we have a factory with four machine types (treatment factor with levels \(A\) to \(D\) ) such that each of four operators can only operate one machine on a single day, we could perform an experiment on four days and block on days ( \(C_1\) to \(C_4\) ) and operators ( \(R_1\) to \(R_4\) ) using a Latin Square design as shown in Table  5.3 .

By design, a Latin Square with a treatment factor with \(g\) levels uses (only) \(g^2\) experimental units. Hence, for small \(g\) , the degrees of freedom of the error term can be very small, see Table  5.4 , leading to typically low power.

We can create a (random) Latin Square design in R for example with the function design.lsd of the package agricolae ( de Mendiburu 2020 ) .

To analyze data from such a design, we use the main effects model \[ Y_{ijk} = \mu + \alpha_i + \beta_j + \gamma_k + \epsilon_{ijk}. \] Here, the \(\alpha_i\) ’s are the treatment effects and \(\beta_j\) and \(\gamma_k\) are the row- and column-specific block effects with the usual side constraints.

The design is balanced having the effect that our usual estimators and sums of squares are “working.” In R , we would use the model formula y ~ Block1 + Block2 + Treat . We cannot fit a more complex model, including interaction effects, here because we do not have the corresponding replicates.

Multiple Latin Squares can also be combined or replicated. This allows for more flexibility. In that sense, Latin Square designs are useful building blocks of more complex designs, see for example Kuehl ( 2000 ) .

With patients, it is common that one is not able to apply multiple treatments in parallel, but in a sequential manner over multiple time periods (think of comparing different painkillers: a different painkiller per day). In such a situation, we would like to block on patients (“as usual”) but also on time periods, because there might be something like a learning or a fatigue effect over time. Such designs are called crossover designs , a standard reference is Jones and Kenward ( 2014 ) . If the different periods are too close to each other, so-called carryover effects might be present: the medication of the previous period might still have an effect on the current period. Such effects can be incorporated into the model (if this is part of the research question). Otherwise, long enough washout periods should be used.

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What is a block in experimental design?

I have two questions about the notion of block in experimental design : (1) What is the difference between a block and a factor ? (2) I tried to read some books but something is not clear: it seems that the authors always assume that there is no interaction between the "block factor' and other factors. Is it right, and if it is, why ?

• interaction
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• experiment-design

5 Answers 5

The block is a factor. The main aim of blocking is to reduce the unexplained variation $(SS_{Residual})$ of a design -compared to non-blocked design-. We are not interested in the block effect per se , rather we block when we suspect the the background "noise" would counfound the effect of the actual factor. We group experimental units into "homogeneous" blocks where all levels of the main factor are equally represented. The analysis of variance of a Randomized Control Block design splits the residual term of an equivalent single factor Complete Randomized design in block and residual components. We should note, however, that the latter component has fewer degrees of freedom than in single factor CR designs, leading to higher estimates for $MS_{Residual} = {SS_{Residual}}/{d.f.}$. The decision to block or not to block should be made when we reckon that the decrease in the residuals will more than compensate for the decrease in d.f.

Usually an additive model is fitted to RCB design data, in which the response variable is an additive combination of the factor and the block effects and it is assumed that no interaction exists between the two. I think this is accounted for by the fact that RCB does not enable us to tell apart the interaction BxF from the within Block variability and the variability within experimental units. The bottom line is that we have to assume no interaction since we can't measure it. We can test whether it is present either visually or with Tukey's test, though.

A good resource on experimental design is this .

• $\begingroup$ (+1) Another good read is Montgomery's Design and Analysis of Experiments . $\endgroup$ –  chl Commented Jan 9, 2012 at 14:58
• $\begingroup$ Thank you @chl. Montgomery's was on my shopping list but I chosed not to buy it since it was more geared towards engineering than ecology. I have noticed a new edition is due to be published on April, 2012, will you update your R companion to it? $\endgroup$ –  Charlie Commented Jan 9, 2012 at 17:49
• 1 $\begingroup$ Thanks everybody. I rather have a mathematical mind, then I have difficulties to read books such as the one of Montgomery in which there is too much text and not enough mathematics $\endgroup$ –  Stéphane Laurent Commented Jan 9, 2012 at 18:38
• $\begingroup$ @Charlie Yup, that's a project that dates back to 2006 when the Doe CRAN Task view didn't exist at all. I will continue to work on the 6th version with the hope of finishing it this year (but I say that each new year, so...). Besides the 'biased' field of application, I still think the text remains excellent for psychologists and biologists. $\endgroup$ –  chl Commented Jan 9, 2012 at 20:04
• 1 $\begingroup$ @Stéphane I can suggest to have a look at Plane Answers to Complex Questions , by Christensen: less DoE, more math, and a nice intro to Linear Models. $\endgroup$ –  chl Commented Jan 9, 2012 at 20:09

Here is a concise answer. A lot of details and examples might be found in most documents treating the design of experiments; especially in agronomy.

Often, the researcher is not interested in the block effect per se, but he only wants to account for the variability in response between blocks. So, I use to view the block as a factor with a particular role. Of note, the block effect is typically considered as a random effect. Finally, if you expect the 'treatment effect' to differ from block to block, then interactions should be considered.

Experimental designs are a combination of three structures:

• The treatment structure: How are treatments formed from factors of interest?
• The design structure: How are experimental units grouped and assigned to treatments?
• The response structure: How are observations taken?

Blocks are "factors" that belong to the design structure (to distinguish, it's not a bad idea to call them "blocking factors" vs "treatment factors"). They are good examples of nuisance parameters : model parameters you have to have and whose presence you must account for, but whose values are not particularly interesting. Please note that this has nothing to do with the nature of a factor -- blocking factors may be fixed or random, just as treatment factors may be fixed or random.

My personal rule of thumb regarding where a factor belongs in an experimental design is this: If I want to estimate the parameters associated with the factor and compare them either within the factor or other factor parameters, then it belongs to the treatment structure. If I don't care about the values of the associated parameters and don't care to compare them, the factor belongs to the design structure.

Thus, in the bread example elsewhere in this thread, I have to worry about run-to-run differences. But I don't care to compare Run 1 vs Run 24. Oven run belongs to the design structure . I do want to compare the two dough recipes: recipe belongs to the treatment structure. I care about oven temperature: that belongs to the treatment structure, too. Let's build an Experimental Design.

The Design Structure has one factor (oven run, Run), and the Treatment Structure two factors (Recipe and Temperature). Because every run has to be a single (nominal) temperature, Temperature and Run must occur at the same level of the experimental design. However, there is space for 4 loaves in each Run. Obviously, we can choose to bake 1, 2, 3 or 4 loaves per run.

If we bake one loaf per run, and randomize the order of Recipe presentation we get a Completely Randomized Design (CRD) Structure. If we bake two loaves, one of each Recipe per Run, we have a Randomized Complete Block Design (RCB) Structure. Please note that it is important that each Recipe occur within each Run. Without that balance, Recipe comparisons will be contaminated by Run differences. Remember: the goal of blocking is to get rid of Run differences . If we bake three loaves per Run, we would probably be crazy: 3 is not a factor of 160, so we will have one or two different-sized blocks. The other reasonable possibility is four loaves per Run. In this case we would bake two loaves of each recipe in each Run. Again, this is a RCB Structure. We can estimate the within-run variability using differences between the two loaves of each Recipe in each Run.

If we choose one of the RCB Design Structures, Temperature effects are completely randomized at the Run level. Recipe is nested within temperature and has a different error structure than temperature, because each dough appears within each run. The contrasts looking at recipe and recipe by dough non-additivity (interaction) do not have run-to-run variability in them. Technically, this is called variously a split-plot design structure or a repeated-measures design structure.

Which would the investigator use? Probably the RCB with four loaves: 40 runs vs 80 vs 160 carries a lot of weight. However, this can be modified -- if the concern is home ovens rather than industrial production, there may well be reason to use the CRD if it is believed that home bakers rarely bake multiple loaves.

• 2 $\begingroup$ I do not follow your analysis of the bread experiment, perhaps because several different designs of that experiment were mentioned and you do not specify which one(s) you are referring to. That makes most of your comments confusing rather than illuminating. If you could clear this up I believe your answer would stand out. $\endgroup$ –  whuber ♦ Commented Jul 11, 2014 at 13:00
• 1 $\begingroup$ The importance of #2 deserves to be brought out. Analysis can be carried out based on the random assignment of experimental treatments: blocks represent restrictions on that random assignment. $\endgroup$ –  Scortchi - Reinstate Monica ♦ Commented Jul 11, 2014 at 13:28
• 2 $\begingroup$ @whuber That's because I wasn't analyzing it, I was designing an experiment from those parameters de novo . Clarified in the edit. $\endgroup$ –  Dennis Commented Jul 11, 2014 at 14:46

Here's a paraphrase of my favorite explanation, from my former teacher Freedom King.

You are studying how bread dough and baking temperature affect the tastiness of bread. You have a rating scale for tastiness. And let's say you're purchasing packaged bread dough from some food company rather than mixing it yourself. Each baked loaf of bread is an experimental unit.

Let's say that you have 2 doughs and 8 temperatures, you can fit 4 loaves of bread in the oven at once and you want to run $n=160$ loaves.

In a completely randomized $2\times2$ factorial layout (no blocks), you would completely randomly decide the order in which the breads are baked. For each loaf, you would preheat the oven, open a package of bread dough, and bake it. This would involve running the oven 160 times, once for each loaf of bread.

Alternatively, you could treat oven run as a blocking factor . In this case, you would run the oven 40 times, which might make data collection faster. Each oven run would have four loaves, but not necessarily two of each dough type. (The exact proportion would be chosen randomly.) You would have 5 oven runs for each temperature; this could help you to account for variability among same-temperature oven runs.

Even fancier, you could block by dough as well as oven run. In this design, you would have exactly two of each type of dough in each of the oven runs.

When I have time to think it through, I'll update this further with the appropriate fancy names for those experiment designs.

• 1 $\begingroup$ BTW, it is a $2 \times 8$ factorial treatment structure, not a $2 \times 2$. $\endgroup$ –  Dennis Commented Jul 11, 2014 at 16:24
• $\begingroup$ Is this an example of incomplete blocking? $\endgroup$ –  SmallChess Commented Sep 18, 2016 at 4:22

I think most of the time it’s just a matter of convention, likely proper to each field. I think that in medical context, in a two factors anova one of the factors is almost always called "treatment" and the other "block".

Typically, as ocram says, the block effect will be a random effect, but I don’t think this is systematic. Let says you want to assess the effectiveness of different medical treatments:

First design: each patient takes only one treatment, and the efficiency is measured on an appropriate scale. You suspect that the sex of the patient is of interest: you will have a "block" of male and a block of female patients. In this case, the block is a factor with a fixed effect.

Second design: each patients tries all treatments at different moments. As there is some variability between patients, you consider each patient as a "block". You are interested in the existence of such a variability in the population, but not in its value in these particular patients. In this case, the block is a factor with a random effect.

Well, I only teach this stuff, trying to stick with the conventions of the domain (in France) as I got them from textbooks, but I never participated to a clinical trial (and don’t want to)... so this is just my two cents...!

• 3 $\begingroup$ It seems to me that blocking denotes a more general strategy to reduce experimental errors (by accounting for the within-block homogeneity), one manifestation of this approach being the use of repeated measurements . I mean, blocking as seen in RBD is a way to combine randomization and control for potential confounder(s) at the level of statistical units. Blocking is also used when we cannot perform a complete replicate of a ($2^k$ or other) factorial design in a single block. $\endgroup$ –  chl Commented Jan 9, 2012 at 13:05
• $\begingroup$ @chl I think you’re right! I was just giving some very basic examples... $\endgroup$ –  Elvis Commented Jan 9, 2012 at 15:48
• $\begingroup$ They are good (one example with a yield/crop experiment from agronomy would have make it even clearer); I was just pointing out that "blocking" extends beyond the "factor" concept and the fixed vs. random distinction. $\endgroup$ –  chl Commented Jan 9, 2012 at 20:00
• $\begingroup$ @chl, if you have a good (and simple) reference on this kind of stuff I’d be glad to read it (and you should post as an answer)... (not so simple references accepted as well!) $\endgroup$ –  Elvis Commented Jan 9, 2012 at 20:05
• $\begingroup$ You mean example(aov) or the R agricolae package? :-) $\endgroup$ –  chl Commented Jan 9, 2012 at 20:11

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What is a Randomized Complete Block Design (RCBD)?

A Randomized Complete Block Design (RCBD) is defined by an experiment whose treatment combinations are assigned randomly to the experimental units within a block. Generally, blocks cannot be randomized as the blocks represent factors with restrictions in randomizations such as location, place, time, gender, ethnicity, breeds, etc. It is not simply possible to randomly assign a particular gender to a person. It is not possible to pick a country and call X country. However, the presence of these factors (also known as nuisance factors ) will introduce systematic variation in the study. For example, the crops produced in the northern vs the southern part will get exposed to different climate conditions. Therefore, they should be controlled whenever possible. Controlling these nuisance factors by blocking will reduce the experimental error, thereby increasing the precision of the experiment and many other benefits. In the completely randomized design (CRD) , the experiments can only control the random unknown and uncontrolled factors (also known as lucking nuisance factors). However, the RCBD is used to control/handle some systematic and known sources ( nuisance factors ) of variations if they exist.

Randomized Complete Block Design (RCBD) is arguably the most common design of experiments in many disciplines, including agriculture, engineering, medical, etc. In addition to the experimental error reducing ability, the design widens the generalization of the study findings. For example, if the study contains the place as a blocking factor, the results could be generalized for the places. A fertilizer producer can only claim that it is effective regardless of the climate conditions when it is tested in various climate conditions.

The “ complete block ” part of the name indicates that each treatment combination is applied in all blocks. If a block misses one or more treatment combinations, the experiment would be called Randomized Incomplete Block Design. The design would still be called randomized because the treatment combinations are randomly assigned to the experimental units within the blocks. If a block is only missing data points from a couple of observation units , the experiment will still be called randomized complete block design (RCBD) with missing data, but not “incomplete block design.”

Randomized Complete Block Design Analysis Model

The effects model for the RCBD is provided in Equation 1.

The primary interest is the treatment effect in any RCBD, therefore the hypothesis for the design is statistically written as.

Test Your Knowledge

Example problem on randomized complete block design.

What is a block?

A block is a categorical variable that explains variation in the response variable that is not caused by the factors. Although each measurement should be taken under consistent experimental conditions (other than the factors that are being varied as part of the experiment), this is not always possible. Use blocks in designed experiments and analysis to minimize bias and variance of the error because of nuisance factors. For example, you want to test the quality of a new printing press. However, press arrangement takes several hours and can only be done four times a day. Because the design of the experiment requires at least eight runs, you need at least two days to test the press. You should explain any differences in conditions between days by using "day" as a blocking variable. To distinguish between any block effect (incidental differences between days) and effects because of the experimental factors (temperature, humidity, and press operator), you must include the block (day) in the designed experiment. You should randomize run order within blocks.

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7.1 - blocking in an unreplicated design.

We begin with a very simple replicated example of blocking. Here we have \(2^2\) treatments and we have n = 3 blocks. In the graphic below the treatments are labeled using the standard Yates notation. Here the \(2^2\) treatments are the full set of treatment combinations so we can simply put each replicate within a block and assign them in this way.

We can use the Minitab software to construct this design as seen in the video below.

Now let’s consider the case when we don't have any replicates, hence when we only have one set of treatment combinations. We go back to the definition of effects that we defined before. We did this using following table, where {(1), a, b, ab} is the set of treatment combinations, and A, B, and AB are the effect contrasts:

The question is: what if we want to block this experiment? Or, more to the point, when it is necessary to use blocks, how would we block this experiment?

If our block size is less than four we are only going to consider, in this context of \(2^k\) treatments, block sizes in the same family, i.e. \(2^p\) number of blocks. So in the case of this example let's use blocks of size 2, which is \(2^1\). If we have blocks of size two then we must put two treatments in each block. One example would be twin studies where you have two sheep from each ewe. The twins would have homogeneous genetics and the block size would be two for the two animals. Another example might be two-color micro-arrays where you have only two colors in each micro-array.

So now the question: How do we assign our four treatments to our blocks of size two?

In our example each block will be composed of two treatments. The usual rule is to pick an effect you are least interested in, and this is usually the highest order interaction, as a means of specifying how to do blocking. In this case it is the AB effect that we will use to determine our blocks. As you can see in the table below we have used the high level of AB to denote Block 1, and the low-level of AB to denote Block 2. This determines our design.

Now, using this design we can assign treatments to blocks. In this case treatment (1) and treatment ab will be in the first block, and treatment a and treatment b will be in the second block.

Blocks of size 2

This design confounds blocks with the AB interaction. You can see this by these contrasts - the comparison between block 1 and Block 2 is the same comparison as the AB contrast. Note that the A effect and the B effect are orthogonal to the AB effect. This design gives you complete information on the A and the B main effects, but it totally confounds the AB interaction effect with the block effect.

Although our block size is fixed at size = 2 we still might want to replicate this experiment in addition. What we have above is two blocks which is one unit of the experiment. We could replicate this design additionally let's say r times and each replicate of the design would be 2 blocks of the design laid out in this way.

We show how to construct this with four replicates. Review the movie below to see how this occurs in Minitab.

Cold water shots into the Colorado River slow a bass invasion in the Grand Canyon

GRAND CANYON NATIONAL PARK — A shot of cold water from Glen Canyon Dam appears to have stalled a smallmouth bass invasion of the Grand Canyon and protected rare Colorado River fish there, federal officials say.

In early July, two years after first finding the predatory bass spawning below the dam and in threatened humpback chub territory, the U.S. Bureau of Reclamation began releasing cold water from deep in Lake Powell in an effort to chill the river past the temperature at which bass are known to reproduce.

So far this summer, numerous netting, snorkeling and electrofishing trips on the river have turned up no newly hatched bass, biologists reported to an advisory committee meeting on Grand Canyon’s South Rim on Thursday.

“That’s huge,” said Kelly Burke, executive director at Wild Arizona and its Grand Canyon Wildlands Council, which had pushed for flow alterations from the dam to disrupt the bass invasion.

Cooler water was a must for preventing possible biological disaster this summer in particular, she said. “It couldn’t be better timed. We’re having an extraordinarily hot summer.”

The initial success also means the National Park Service will not dump a fish-killing chemical into spawning grounds a few miles downstream of the dam this year as it did last summer. Last year’s effort drew a rebuke from some tribal officials associated with Grand Canyon, who prefer nonlethal controls.

Federal officials considered the bass invasion an emergency requiring quick action to prevent a population explosion that could devastate humpback chubs, 90% or more of which live in the Canyon. Cooling the river below 60 degrees Fahrenheit has at least stalled that explosion.

With potentially hundreds of adult or year-old bass still swimming upstream of or within the Canyon, though, Reclamation and the National Park Service are contemplating more lasting changes, such as dredging a river channel through the prime spawning habitat of a backwater slough and draping a screen across lower Lake Powell to prevent more fish from spilling through the dam’s power turbines, as the initial invaders are thought to have done.

At this point, it may be impossible to remove the bass already living in the Lees Ferry zone above Grand Canyon, committee members acknowledge. Instead, the goal is to keep their numbers from swelling to the point where they consume large numbers of native fish downstream, or ideally to let them eventually die out without replacing themselves.

Protecting native fish cuts into power production

The cooling program’s apparent initial success comes at a cost, as the Western Area Power Administration is forced to spend several million dollars a month to replace power that Glen Canyon could have generated if the water had poured through the hydropower turbines as usual, instead of into the dam’s deeper and consequently colder bypass intakes.

Hydroelectricity’s value is not just measured in dollars but in life-preserving summer cooling, Sheri Farag of Phoenix-area Salt River Project reminded fellow members of the Glen Canyon Adaptive Management Work Group , who advise the U.S. Interior Department on such programs.

“People do need it, especially in the desert Southwest, to stay alive,” she said.

The committee has endorsed the river-cooling experiment, which required an environmental assessment that federal officials signed off on just days before water temperatures required action to prevent bass spawning.  

“It truly has been a race against time,” said Wayne Pullan, Reclamation’s Upper Colorado regional director who leads the advisory committee that includes representatives from federal, state, tribal, energy, environmental and recreational interests.

A legal requirement to study the experiment’s possible effects before getting Interior Secretary Deb Haaland’s approval caused enough delay to give the bass a short head start.

Studies show that smallmouth bass spawn when water reaches 16 degrees Celsius. The approved experiment in cooling calls for the dam to release water through the bypass tubes when temperatures at the Colorado’s confluence with the Little Colorado — some 76 miles downstream, and a major humpback chub rearing area — reaches 15.5 degrees Celsius for three days.

A water temperature model had suggested that wouldn’t happen until mid-August, but this year it happened during the week of June 23, according the Bureau of Reclamation. The secretary OK’d the program on July 3, and the cold water started flowing six days later.

So far, various agency biologists report, there’s no evidence that the bass were able to capitalize. Fish-trapping trips will continue through fall, and the committee will then consider whether to recommend a second year of cooling flows for next year.

Non-native species: As Lake Powell shrinks, voracious smallmouth bass are staging for a Grand Canyon invasion

How non-native fish found their way downstream

Water temperature has been a point of worry for protecting Grand Canyon’s native fish, including the humpback chub , ever since Glen Canyon Dam began impounding river water in Lake Powell in 1963. For years, the fear was that by drawing relatively deep and cool water through its power plant, the dam harmed native fish by year-round chilling of a river that had previously been flashy, flush with cold snowmelt in springtime but warm during the summer and fall.

Some native fish disappeared from the Canyon, including the salmon-length Colorado pikeminnow. But the chub, a smaller, silvery eater of insects and small fish, found refuge and spawning habitat in the Little Colorado.

More recently it has proliferated in the Colorado mainstem, where it warms farther from the dam in western Grand Canyon, enough so that the U.S. Fish and Wildlife Service upgraded the species' status from endangered to threatened.

As the warming climate dried the mountain streams that supply the Colorado and Lake Powell, though, it seems the river may have warmed too much for the chub’s own good. As more than two decades of drought drained much of Lake Powell’s capacity, the water line plunged closer to the hydropower intakes. That brought both the warm surface layer and the warm-water invaders swimming in it closer to those intakes.

Non-native bass, stocked in Lake Powell for decades as sport fish, were known to have occasionally made it through the dam before, but until 2022 they were not known to have subsequently spawned in the river below. Now the dam’s warming outflows created welcoming conditions for them and their young.

To cool the river and restore a buffer for the chubs downriver, Reclamation is mixing deeper outlet tube water with some of the warmer water now passing through the power turbines. To minimize the economic harm, that only happens outside of peak power demands in the late afternoon and evening hours.

So far, according to Brian Sadler with the Western Area Power Administration, it’s costing $5 million or more per month in power that the organization must purchase elsewhere on the grid. If the experiment lasts as expected into October, he said, it will have cost $15 million to $20 million, not counting potentially higher prices that individual utilities may pay when bidding for the same power the Western Area Power Administration distributes to its customers.

The long-term costs worry Leslie James, who represents the Colorado River Energy Distributors Association on the committee. Losing potential hydropower year after year to cool the river for fish would cost utilities that rely on the power, including rural and tribal providers. Better to make physical changes such as the slough alteration that the government is currently considering, she said.

The slough in question, about 3 miles downstream from the dam, provides a warm-water nursery that connects to the river but holds still water behind a sandbar. The Interior Department is studying the possibility of dredging a river channel through that sandbar as early as this winter to allow the Colorado’s flow to better disrupt spawning beds there.

The cost, estimated at $26 million, sounds high except when compared with continuing bypass flows that reduce power production, James said.

“Flow options cannot be the only alternative,” she said.

Besides, James said, she believes it’s too early to call the so-called “cool-mix” flows a success.

“I’m very glad they haven’t found evidence of spawning,” she said. “Can the scientists say for sure that’s the result of the experiment? No.”

A natural resource: To keep the Colorado River's heart beating, people step in to do what nature once did

An 'existential threat' to native species

Others on the committee say it will take multiple measures, including flow changes, to protect native fish and ultimately prevent even costlier changes that the Endangered Species Act could trigger.

“This is an existential threat to the native fish,” Grand Canyon National Park Superintendent Ed Keable said.

Some Native tribal officials remain troubled by some components of the bass-control program, such as the electrofishing rigs with which biologists stun and then remove and kill non-native fish. The cooling program, though, has broad support.

“It’s the more ethical approach,” said Erik Stanfield, the Navajo Nation’s representative on the committee.

Serendipitously for sport anglers, the cooling program may aid in recovery of the one-time trophy rainbow trout fishery that gained notoriety after Glen Canyon Dam cooled and cleared the river around Lees Ferry. That fishery has suffered in recent years as the river warmed and consequently lost oxygen. The cool mix is reversing that damage this summer.

“It’s providing good, cool water and dissolved oxygen that trout like,” said Jim Strogen of Trout Unlimited.

Rainbow trout are, like the bass, non-native in the Colorado, but they are considered less of a threat to native fish. (Brown trout are more of a threat to eat chubs, and a separate program pays cash incentives to anglers who catch and keep them.)   

While officials and advocates hope the cold water continues to block a larger bass invasion into Grand Canyon, other threats loom ominously in Lake Powell. The reservoir holds other non-native predators that have devoured chubs and other native fishes on the Upper Colorado, upstream of Powell. Some of them, like the walleye, have been spotted below Glen Canyon Dam but are not known to have reproduced there.

Such threats may warrant a costlier barrier above the dam in coming years, and Interior has begun studying the options. Meantime, Grand Canyon Wildlands Council ecologist Larry Stevens said, diverting cold water downstream is the river’s best medicine, despite the cost.

Stevens described floating on the river more than 50 miles downstream of the dam this year and glancing down to see an adult walleye swimming there.

“To randomly see one out of the blue, just looking at the river, tells me we’re well on the way to a walleye invasion,” he said. “It’s hugely concerning.”

Brandon Loomis covers environmental and climate issues for The Arizona Republic and azcentral.com. Reach him at   [email protected] .

Environmental coverage on azcentral.com and in The Arizona Republic is supported by a grant from the Nina Mason Pulliam Charitable Trust. 

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