5.5 – Importance of randomization in experimental design

Introduction

If the goal of the research is to make general, evidenced-based statements about causes of disease or other conditions of concern to the researcher, then how the subjects are selected for study directly impacts our ability to make generalizable conclusions. The most important concept to learn about inference in statistical science is that your sample of subjects upon which all measurements and treatments are conducted, ideally should be a random selection of individuals from a well-defined reference population.

The primary benefit of random sampling is that it strengthens our confidence in the links between cause and effect. Often after an intervention trial is complete, differences among the treatment groups will be observed. Groups of subjects who participated in sixteen weeks of “vigorous” aerobic exercise training show reduced systolic blood pressure compared to those subjects who engaged in light exercise for the same period of time (Cox et al 1996). But how do we know that exercise training caused the difference in blood pressure between the two treatment groups? Couldn’t the differences be explained by chance differences in the subjects? Age, body mass index (BMI), overall health, family history, etc?

How can we account for these additional differences among the subjects? If you are thinking like an experimental biologist, then the word “control” is likely coming to the foreground. Why not design a study in which all 60 subjects are the same age, the same BMI, the same general health, the same family … history…? Hmm. That does not work. Even if you decide to control age, BMI, and general health categories, you can imagine the increased effort and cost to the project in trying to recruit subjects based on such narrow criteria. So, control per se is not the general answer.

If done properly, random sampling makes these alternative explanations less likely. Random sampling implies that other factors that may causally contribute to differences in the measured outcome, but themselves are not measured or included as a focus of the research study, should be the same, on average, among our different treatment groups. The practical benefits of proper random sampling is that recruiting subjects gets easier — fewer subjects will be needed because you are not trying to control dozens of factors that may (or may not!) contribute to differences in your outcome variable. The downside to random sampling is that the variability of the outcomes within your treatment groups will tends to increase. As we will see when we get to statistical inference, large variability within groups will make it less likely that any statistical difference between the treatment groups will be observed.

Demonstrate the benefits of random sampling as a method to control for extraneous factors.

The study reported by Cox et al included 60 obese men between the ages of 20 and 50. A reasonable experimental design decision would suggest that the 60 subjects be split into the two treatment groups such that both groups had 30 subjects for a balanced design. Subjects who met all of the research criteria and who had signed the informed consent agreement are to be placed into the treatment groups and there are many ways that group assignment could be accomplished. One possibility, the researchers could assign the first 30 people that came into the lab to the Vigorous exercise group and the remaining 30 then would be assigned to the Light exercise group. Intuitively I think we would all agree that this is a suspect way to design an experiment, but more importantly, why shouldn’t you use this convenient method?

Just for argument’s sake, imagine that their subjects came in one at a time, and, coincidentally, they did so by age. The first person was age 21, the second was 22, and so on up to the 30th person who was 50. Then, the next group came in, again, coincidentally in order of ascending age. If you calculate the simple average age for each group you will find that they are identical (35.5 years). On the surface, this looks like we have controlled for age: both treatment groups have subjects that are the same age. A second option is to sort the subjects into the two treatment groups so that a 21 year old is in Group A, and the other 21 year old is in Group B, and so on. Again, the average age of Group A subjects and of Group B subjects would be the same and therefore controlled with respect to any covariation between age and change in blood pressure. However, there are other variables that may covary with blood pressure, and by controlling one, we would need to control the others. Randomization provides a better way.

I will demonstrate how randomization tends to distribute the values in such a way that the groups will not differ appreciably for the nuisance variables like age and BMI differences and, by extension, any other covariable. The R work is attached following the Reading list. The take-home message: After randomly selecting subjects for assignment to the treatment groups, the apparent differences between Group A and Group B for both age and BMI are substantially diminished. No attempt to match by age and by BMI is necessary. The numbers are shown in the table and then in two graphics (Fig 1, Fig 2) derived from the table.

Table 1. Mean age and BMI for subjects in two treatment groups A and B where subjects were assigned randomly or by convenience to treatment groups.

Group	Random assignment of subjects to treatment groups	Convenience assignment of subjects to treatment groups
A	35.2	28
B	35.8	43
A	32.49	28.99
B	32.87	37.37

Just for emphasis, the means from Table 1 are presented in the next two figures (Fig 1 and Fig 2).

Figure 1. Age of subjects by groups (A = blue, B = red) with and without randomized assignment of subjects to treatment groups.

Figure 2. BMI of subjects by groups (A = blue, B = red) with and without randomized assignment of subjects to treatment groups.

Note that the apparent difference between A and B for BMI disappear once proper randomization of subjects was accomplished. In conclusion, a random sample is an approach to experimental design that helps to reduce the influence other factors may have on the outcome variable (eg, change in blood pressure after 16 weeks of exercise). In principle, randomization should protect a project because, on average, these influences will be represented randomly for the two groups of individuals. This reasoning extends to unmeasured and unknown causal factors as well.

This discussion was illustrated by random assignment of subjects to treatment groups. The same logic applies to how to select subjects from a population. If the sampling is large enough, then a random sample of subjects will tend to be representative of the variability of the outcome variable for the population and representative also of the additional and unmeasured cofactors that may contribute to the variability of the outcome variable.

What about observational studies? How does randomization work?

However, if you do cannot obtain a random sample, then conclusions reached may be sample-specific, biased. …perhaps the group of individuals that likes to exercise on treadmills just happens to have a higher cardiac output because they are larger than the individuals that like to exercise on bicycles. This nonrandom sample, an example of confounding where an extraneous or nuisance variable, body size, is associated with both the independent variable (exercise preference) and the dependent variable (cardiac output), will bias your results and can lead to incorrect interpretation of results.

Alternatively, perhaps a researcher elects to study the cardiac output of treadmill users versus bicycle users. The researcher sets up their testing station inside a gym’s powerlifting zone, where the largest individuals in the gym hang out. Inevitably because of this choice, the researcher over recruits larger individuals into the treadmill group, leading to a falsely elevated average cardiac output for treadmill users. This is an example of ascertainment bias — the sample is not representative of all treadmill users at the gym.

Random sampling is CRUCIAL in epidemiology, opinion survey work, most aspects of health, drug studies, medical work with human subjects. It’s difficult and very costly to do… so most surveys you hear about, especially polls reported from Internet sites, are NOT conducted using random sampling (included in the catch-all term “probability sampling“)!! As an aside, most opinion survey work involves complex sample designs involving some form of geographic clustering (eg, all phone numbers in a city, random sample among neighborhoods).

Random sampling is the ideal if generalizations are to be made about data, but strictly random sampling is not appropriate for all kinds of studies. Consider the question of whether or not EMF exposure is a risk factor for developing cancer (Pool 1990). These kinds of studies are observational: at least in principle, we wouldn’t expect that housing and therefore exposure to EMF is manipulated (cf. discussion Walker 2009). Thus, epidemiologists will look for patterns: if EMF exposure is linked to cancer, then more cases of cancer should occur near EMF sources compared to areas distant from EMF sources. Thus, the hypothesis is that an association between EMF exposure and cancer occurs non-randomly, whereas cancers occurring in people not exposed to EMF are random. Unfortunately, clusters can occur even if the process that generates the data is random.

Compare Graph A and Graph B (Fig 3). One of the graphs resulted from a random process and the other was generated by a non-random process. Note that the claim can be rephrased about the probability that each grid has a point, eg, it’s like Heads/Tails of 16 tosses of a coin. We can see clusters of points in Graph B; Graph A lacks obvious clusters of points — there is a point in each of the 16 cells of the grid. Although both patterns could be random, the correct answer in this case is Graph B.

Figure 3. An example of clustering resulting from a random sampling process (Graph B). In contrast, Graph A was generated so that a point was located within each grid.

Hard to tell — and truth be told, random process could generate either one. To convince you, Figure 4 reveals the grouping that was done for Group A, in contrast with Group B which was drawn with the truly random process.

Figure 4. Same graphs as Figure 3, but with ellipses around the grouped data (hard to tell, but the centroids are the larger points). 

Implications for sampling

The graphic below shows the transmission grid in the continental United States (Fig 5). How would one design a random sampling scheme overlaid against the obviously heterogeneous distribution of the grid itself? If a random sample was drawn, chances are good that no population would be near a grid in many of the western states, but in contrast, the likelihood would increase in the eastern portion of the United States where the population and therefore transmission grid is more densely placed.

Figure 5. Map of electrical transmission grid for continental United States of America. Image source https://openinframap.org/#3/24.61/-101.16

For example, you want to test whether or not EMF affects human health, and your particular interest is in whether or not there exists a relationship between living close to high voltage towers or transfer stations and brain cancer. How does one design a study, keeping in mind the importance of randomization for our ability to generalize and assign causation?  This is a part of epidemiology which strives to detect whether clusters of disease are related to some environmental source. It is an extremely difficult challenge. For the record, no clear link to EMF and cancer has been found, but reports do appear from time to time (eg, report on a cluster of breast cancer in men working in office adjacent to high EMF, Milham 2004).

 

Questions

1. Use the sample() with and without replacement on the object (see help with R below)

fruit <- c("apple", "banana", "grape", "kiwi", "pear", "pineapple", "tomato")

a) set of 3

b) set of 4

2. Confirm the claim by calculating the probability of Graph A result vs Graph B result (see R script below).

Quiz Chapter 5.5

Importance of randomization in experimental design

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R code!

Code you type is shown in red; responses or output from R are shown in blue. Recall that statements preceded by the hash # are comments and are not read by R (ie, no need for you to type them).

First, create some variables. Vectors aa and bb contain my two age sequences.

 aa = seq(21,50)
 bb = seq(21,50)

Second, append vector bb to the end of vector aa

 age = append(aa,bb)
 age           #submit the vector (variable) name to print the records for verification - looks good! 
  [1] 21 22 23 24 25 26 27 28 29 30 31 32 33 34 35 36 37 38 39 40 41 42 43 44 45 46 47 48 49 50 21 22 23 24 25 26 27 28 29 30 31 32 33 34 35 36 37
 [48] 38 39 40 41 42 43 44 45 46 47 48 49 50

Third, get the average age for the first group (the aa sequence)  and for the second group (the bb sequence). Lots of ways to do this, I made a two subsets from the combined age variable; could have just as easily taken the mean of aa and the mean of bb (same thing!).

 A = age[1:30]
 mean(A)
 [1] 35.5
 B = age[31:60]
 mean(B)
 [1] 35.5

Fourth, start building a data frame, then sort it by age. Will be adding additional variables to this data frame

 ex.random = data.frame(age)
 AO.all = sort(ex.random$age)
 AO.age           #submit the vector (variable) name to print the records for verification - looks good! 
  [1] 21 21 22 22 23 23 24 24 25 25 26 26 27 27 28 28 29 29 30 30 31 31 32 32 33 33 34 34 35 35 36 36 37 37 38 38 39 39 40 40 41 41 42 42 43 43 44
 [48] 44 45 45 46 46 47 47 48 48 49 49 50 50

Fifth, divide the variable again into two subsets of 30 and get the averages

 AO = AO.age[1:30]
 AO
  [1] 21 21 22 22 23 23 24 24 25 25 26 26 27 27 28 28 29 29 30 30 31 31 32 32 33 33 34 34 35 35
 mean(AO)
 [1] 28 
 BO = AO.age[31:60]
 BO
  [1] 36 36 37 37 38 38 39 39 40 40 41 41 42 42 43 43 44 44 45 45 46 46 47 47 48 48 49 49 50 50
 mean(BO)
 [1] 43

Sixth, create an index variable, random order without replacement

 rand.index = sample(1:60,60,replace=F)

Add the new variable to our existing data frame, then print it to check that all is well

 ex.random$rand = rand.index
 ex.random
    age rand
 1   21   43
 2   22   15
 3   23   17
 4   24   35
 5   25   19
 6   26   18
 7   27   22
 8   28   31
 9   29   12
 10  30   44
 11  31   24
 12  32    5
 13  33    2
 14  34   50
 15  35   23
 16  36   20
 17  37   41
 18  38   56
 19  39   36
 20  40    8
 21  41   45
 22  42   38
 23  43   42
 24  44   46
 25  45   16
 26  46   21
 27  47   28
 28  48   10
 29  49   32
 30  50   54
 31  21   57
 32  22   51
 33  23   27
 34  24   40
 35  25   14
 36  26   48
 37  27   26
 38  28   58
 39  29    9
 40  30   11
 41  31    4
 42  32   52
 43  33   37
 44  34   53
 45  35    6
 46  36   34
 47  37   39
 48  38    7
 49  39    1
 50  40   47
 51  41   33
 52  42   60
 53  43   49
 54  44   30
 55  45   29
 56  46   55
 57  47   13
 58  48    3
 59  49   25
 60  50   59

Seventh, select for our first treatment group the first 30 subjects from the randomized index. There are again other ways to do this, but sorting on the index variable means that the subject order will be change too.

 AR.age = ex.random[order(ex.random$rand),]     #created a new data frame to distinguish it from the presorted version "ex.random"

Print the new data frame to confirm that the sorting worked. It did. we can see that the rows have been sorted by ascending order based on the index variable.

 AR.age
    age rand
 49  39    1
 13  33    2
 58  48    3
 41  31    4
 12  32    5
 45  35    6
 48  38    7
 20  40    8
 39  29    9
 28  48   10
 40  30   11
 9   29   12
 57  47   13
 35  25   14
 2   22   15
 25  45   16
 3   23   17
 6   26   18
 5   25   19
 16  36   20
 26  46   21
 7   27   22
 15  35   23
 11  31   24
 59  49   25
 37  27   26
 33  23   27
 27  47   28
 55  45   29
 54  44   30
 8   28   31
 29  49   32
 51  41   33
 46  36   34
 4   24   35
 19  39   36
 43  33   37
 22  42   38
 47  37   39
 34  24   40
 17  37   41
 23  43   42
 1   21   43
 10  30   44
 21  41   45
 24  44   46
 50  40   47
 36  26   48
 53  43   49
 14  34   50
 32  22   51
 42  32   52
 44  34   53
 30  50   54
 56  46   55
 18  38   56
 31  21   57
 38  28   58
 60  50   59
 52  42   60

Eighth, create our new treatment groups, again of n = 30 each, then get the means ages for each group.

 AR = AR.age$age[1:30]
 mean(AR)
 [1] 35.16667
 AR2 = AR.all$all[31:60]
 mean(AR2)
 [1] 35.83333

Get the minimum and maximum values for the groups

 min(AR)
 [1] 22
 min(AR2)
 [1] 21
 max(AR)
 [1] 49
 max(AR2)
 [1] 50

Ninth, create a BMI variable drawn from a normal distribution with coefficient of variation equal to 20%. The first group with we will call cc

 cc = rnorm(n=30,m=27.5, sd=5.5)          #mean was 27.5 for this group with standard deviation of 5.5

The second group called dd

 dd = rnorm(n=30,m=37.5, sd=7.5)          #mean was 37.5 for this group with standard deviation of 7.5

Create a new variable called BMI by joining cc and dd

 BMI=append(cc,dd)
 BMI            #print out BMI to confirm. Looks good!
  [1] 27.87528 27.83250 31.88703 34.99041 24.06751 23.50952 22.57779 31.48394 31.04321 25.60258 25.41081 22.34619 34.62213 36.41348 41.17740
 [16] 20.56529 27.25238 21.85205 32.11690 32.37168 23.11314 33.29110 34.99106 38.22016 18.72105 26.22030 25.13412 27.50475 34.79361 32.81267
 [31] 47.57872 27.58428 40.17211 38.22195 26.91893 37.02784 53.72671 34.94727 30.35245 38.32571 40.52111 36.15627 30.36592 36.20397 47.63142
 [46] 40.30846 36.47643 50.86804 43.63741 37.84994 42.82665 41.71008 28.44976 24.57906 42.37762 38.38512 35.22879 31.34063 34.02996 27.28038

Add the BMI variable to our data frame.

 ex.random$BMI = BMI
 ex.random              #Print out the revised data frame. Looks good. We now have three variables: age, the index "rand," and now BMI
    age rand      BMI
 1   21   43 27.87528
 2   22   15 27.83250
 3   23   17 31.88703
 4   24   35 34.99041
 5   25   19 24.06751
 6   26   18 23.50952
 7   27   22 22.57779
 8   28   31 31.48394
 9   29   12 31.04321
 10  30   44 25.60258
 11  31   24 25.41081
 12  32    5 22.34619
 13  33    2 34.62213
 14  34   50 36.41348
 15  35   23 41.17740
 16  36   20 20.56529
 17  37   41 27.25238
 18  38   56 21.85205
 19  39   36 32.11690
 20  40    8 32.37168
 21  41   45 23.11314
 22  42   38 33.29110
 23  43   42 34.99106
 24  44   46 38.22016
 25  45   16 18.72105
 26  46   21 26.22030
 27  47   28 25.13412
 28  48   10 27.50475
 29  49   32 34.79361
 30  50   54 32.81267
 31  21   57 47.57872
 32  22   51 27.58428
 33  23   27 40.17211
 34  24   40 38.22195
 35  25   14 26.91893
 36  26   48 37.02784
 37  27   26 53.72671
 38  28   58 34.94727
 39  29    9 30.35245
 40  30   11 38.32571
 41  31    4 40.52111
 42  32   52 36.15627
 43  33   37 30.36592
 44  34   53 36.20397
 45  35    6 47.63142
 46  36   34 40.30846
 47  37   39 36.47643
 48  38    7 50.86804
 49  39    1 43.63741
 50  40   47 37.84994
 51  41   33 42.82665
 52  42   60 41.71008
 53  43   49 28.44976
 54  44   30 24.57906
 55  45   29 42.37762
 56  46   55 38.38512
 57  47   13 35.22879
 58  48    3 31.34063
 59  49   25 34.02996
 60  50   59 27.28038

Tenth, repeat our protocol from before: Set up two groups each with 30 subjects, calculate the means for the variables and then sort by the random index and get the new group means.

 AO = ex.random$BMI[1:30]
 mean(AO)
 [1] 28.99333
 BO = ex.random$BMI[31:60]
 mean(BO)
 [1] 37.36943

All we did was confirm that the unsorted groups had mean BMI of around 27.5 and 37.5 respectively. Now, proceed to sort by the random index variable. Go ahead and create a new data frame

 AR.age = ex.random[order(ex.random$rand),]
 AR.age                 #Print out the new data frame to confirm. Looks good.
    age rand      BMI
 49  39    1 43.63741
 13  33    2 34.62213
 58  48    3 31.34063
 41  31    4 40.52111
 12  32    5 22.34619
 45  35    6 47.63142
 48  38    7 50.86804
 20  40    8 32.37168
 39  29    9 30.35245
 28  48   10 27.50475
 40  30   11 38.32571
 9   29   12 31.04321
 57  47   13 35.22879
 35  25   14 26.91893
 2   22   15 27.83250
 25  45   16 18.72105
 3   23   17 31.88703
 6   26   18 23.50952
 5   25   19 24.06751
 16  36   20 20.56529
 26  46   21 26.22030
 7   27   22 22.57779
 15  35   23 41.17740
 11  31   24 25.41081
 59  49   25 34.02996
 37  27   26 53.72671
 33  23   27 40.17211
 27  47   28 25.13412
 55  45   29 42.37762
 54  44   30 24.57906
 8   28   31 31.48394
 29  49   32 34.79361
 51  41   33 42.82665
 46  36   34 40.30846
 4   24   35 34.99041
 19  39   36 32.11690
 43  33   37 30.36592
 22  42   38 33.29110
 47  37   39 36.47643
 34  24   40 38.22195
 17  37   41 27.25238
 23  43   42 34.99106
 1   21   43 27.87528
 10  30   44 25.60258
 21  41   45 23.11314
 24  44   46 38.22016
 50  40   47 37.84994
 36  26   48 37.02784
 53  43   49 28.44976
 14  34   50 36.41348
 32  22   51 27.58428
 42  32   52 36.15627
 44  34   53 36.20397
 30  50   54 32.81267
 56  46   55 38.38512
 18  38   56 21.85205
 31  21   57 47.57872
 38  28   58 34.94727
 60  50   59 27.28038
 52  42   60 41.71008

Get the means of the new groups

 AR = AR.age$BMI[1:30]
 mean(AR)
 [1] 32.49004
 min(AR)
 [1] 18.72105
 max(AR)
 [1] 53.72671
 AR2 = AR.all$BMI[31:60]
 mean(AR2)
 [1] 33.87273
 min(AR2)
 [1] 21.85205
 max(AR2)
 [1] 47.57872

That’s all of the work!

Data set

nonrandom

X	Y
0.779	0.747
0.098	1.248
0.697	2.811
0.59	3.553
1.295	0.075
1.858	1.207
1.172	2.388
1.597	3.051
2.051	0.242
2.081	1.546
2.016	2.738
2.587	3.088
3.833	0.088
3.776	1.264
3.017	2.254
3.657	3.712

random

X1	Y1
1.157	3.203
2.407	0.62
1.033	1.946
3.676	2.866
3.57	2.703
3.056	0.685
1.568	3.355
1.041	1.753
0.643	2.295
2.884	0.687
3.53	2.591
2.838	2.431
3.945	1.518
0.34	1.64
2.45	0.386
3.921	2.976

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Chapter 5 contents

• The basics explained
• Experiments
• Experimental and Sampling units
• Replication, Bias, and Nuisance Variables
• Clinical trials
• Importance of randomization in experimental design
• Sampling from Populations
• References and suggested readings

5.4 – Clinical trials

Introduction

Two areas of inquiry have contributed enormously to our understanding of experimental design: agriculture research (Verdooren 2020) and human subject clinical trials. This page outlines types of clinical trial designs and briefly introduces the subject of research ethics with human subject research (Huang and Hadian 2006). After completing this page, the reader will be able to identify key clinical trial types and recognize the fundamental ethical principles governing human subject research.

Although this page does not address the many concerns for ethical research in ecology and environmental studies, many parallels can be drawn (Crozier and Schulte-Hostedde 2014, Samuel and Richie 2022). To name just one example, both disciplines mandate a “do no harm,” principle. In clinical research this amounts to minimizing risks to human subjects; in environmental and ecology studies, acknowledging experimental studies through sampling or chemical releases can damage ecosystems (Resnik 2009).

An outline of clinical trials

Much has been written about biomedical research study design; a couple of accessible articles that can supplement the material presented here include Benson and Hart 2000, Concato et al 2000, Gabriella 2012. Even if you never work in clinical research, understanding how clinical trials are designed and under what circumstances limitations of particular designs arise is helpful to all of us who do experimental work. In Mike’s Workbook for Biostatistics we will present descriptions of research activities and step through situations where you will attempt to align the research by analogy to clinical trials. A second approach to learning about experimental design is to read about someone’s study, and reworking it in terms of a clinical trial design perspective. We will use a discussion of clinical trials, used in biomedical research to investigate effectiveness of treatments of disease, as our starting point for learning how statistics informs experimentation.

Types of clinical trials are distinguished by their design and include:

Case studies are a thorough analysis of an individual patient, or a few individuals (a group), focusing on symptoms, diagnostics, treatments and outcomes. Case studies can utilize quantitative or qualitative research methods. Case studies, of course, are not restricted to medical research. The main disadvantage of case studies is that by definition they are not generalizable to the population and, by their very nature, researcher subjectivity (choice of diagnostics, interpretations) and other kinds of bias may be challenging to control. A 2025 case study received considerable news coverage: a 60 year old man developed bromism — a toxic condition resulting from excessive exposure to bromides — consulting ChatGPT for health information (Eichenberger et al 2025).

Experimental studies are just that, research designs that apply techniques of experimental science — controls, randomization, attempts to account for sources of bias. They are intended to make direct comparisons among subjects assigned by the researcher to treatment groups. By definition experiments are longitudinal studies. Longitudinal studies are experimental or observational studies in which multiple observations are recorded for each individual and individuals are tracked over time. Many excellent resources about experimental design, beginning with R.A. Fisher’s 1935 book, The design of experiments, to Scheiner and Gurevitch (Editors) 2001, Design and Analysis of Ecological Experiments (2nd edition), to the many books on randomized control trials, eg, the 5th edition of Designing clinical research (2022), edited by Browner et al.

Observational (or epidemiological) studies — no direct intervention is administered and so observational studies tend to be retrospective; we identify individuals with and without the condition and attempt to identify associations between the condition and any number of potential causal factors.

Cross-sectional studies are examples of descriptive study designs. They take observations at one point in time on a variety of individuals. It can be used to associate factors with the condition in question, and can be used to estimate the prevalence of a condition in the population. Omair (2015) provides an accessible  summary of case and cross-sectional study designs.

Cross-sectional studies are referred to as method = cross.sectional in the package epiR.

Cohort studies involve a group of subjects (eg, patients) who receive the same treatment at the same time. A cohort consists of subjects who are linked in some way. It could be a trivial link, like the cohorting done at university (all incoming Freshmen students who enroll for a class offered at 9:30AM), or it could be based on shared experience due to an exposure event (eg, all passengers on a jet traveling with an index case or “patient zero”).

• Prospective cohort studies enroll people as cohorts at the beginning of a study and follow them over time
• Retrospective cohort studies may utilize archived records.

Cohort and other variations of observational studies (eg, case control, test-negative design), can establish associations between risk factors and conditions or specific adverse events, but cannot by themselves establish cause and effect (Benson and Hartz 2000). A search of PUBMED for “cohort study” reports more than 3.2 million studies since 1914. A 2025 prospective cohort study with more than 1800 pregnant women found no change in risk of major birth defects after maternal mRNA COVID-19 vaccination in the first trimester of pregnancy (Kayser et al 2025).

Cohort studies are referred to as method = cohort.count in the package epiR.

Case control studies are similar to cohort studies, except they are retrospective. Case refers to subjects with one or more characteristics of interest.  Used to infer the exposure risk factor by evaluating historical records. Omair (2016) provides an accessible  summary of cohort and case control study designs. Designed to identify associations between exposure and particular outcomes, case control studies are retrospective and observational studies: Retrospective because the outcomes are already known, and observational because the event was caused by nature, not experiment. In principle, researchers identify a number of cases with a particular outcome (eg, lung cancer), then attempt to match cases to individuals who do not have the outcome (controls). Work is done to look back to see if the exposure (eg, smoking) is more frequent in the case group than the control group.

Case control studies have several advantageous compared to other approaches: rapid to conduct compared to longitudinal studies (the even has already happened), and efficient because small sample sizes may be enough to reach conclusions. Among their limitations, however, is the problem of how to match cases with controls. Obvious matching accomplished by grouping by age categories, body mass index, gender, socio-economic status, and so on. Three papers authored by Wacholder published in American Journal of Epidemiology 1992 describe in detail, from theory to practice, case control selection (Wacholder 1992abc). A search of PUBMED for “case control” reports more than 400 thousand studies since 1950. A 2025 case control study with more than one million records found no effect of aluminum adjuvant in childhood vaccines on chronic autoimmunity, atopy or allergy, and neurodevelopmental disorders (Andersson et al 2025).

Case control studies are referred to as method = case.control in the package epiR.

Test-negative designs are a kind of case control studies where the cases are those testing positive for the specific agent and controls are those who test negative for the agent, but importantly, both groups are individuals seeking care for symptoms characteristic of exposure to the agent (Kissling et al 2009, Fukushima and Hirota 2017). This design is intended to reduce the effects of health-care seeking behavior, therefore minimizing possible selection bias, and, therefore false associations between exposure and disease.  Note however, that test-negative studies rely on test accuracy (discussed in Chapter 7.3 – Conditional Probability and Evidence Based Medicine); false negatives, where a person has the disease but test results return negative, incorrectly assigns the individual to the control group. This leads to underestimation of true effect of the intervention, eg, vaccination Fukushima and Hirota 2017).

Randomized Control (interventional or experimental) Trials (RCT): compares an experimental treatment group with a control) placebo group. The groups are assigned to groups randomly. Another variant of a RCT is a randomized clinical trial, with the only difference that the clinical trial compares different treatments and may not include a control group.

Double-blind: The “gold standard” RCT. Both the patient and those interacting with the patient do not know what treatment the patient has received.

Placebo: a treatment in name only. The placebo is a designed but medically ineffective agent given to a study subject. There is considerable debate about what a placebo should contain and as to the ethics and general merits of its use in clinical trials (Temple and Ellenberg 2000).

• active control or comparator studies are now common in place of placebo studies where treatment is clearly better than not giving the subject something of benefit (i.e., the placebo which is designed to not benefit the subject). Active control is not automatically a better choice than placebo control because they may be less effective in evaluating cause and effect (Temple and Ellenberg 2000).

The controlled clinical trial has a long history: Daniel’s vegetarian diet (Daniel’s training in Babylon, Book of Daniel, Old Testament, discussed in Bhatt 2010, h/t Treece 1990) — after ten days those on Daniel’s diet looked healthier than the others who ate the King’s prescribed meal of meat and wine; James Lind’s scurvy trials on board HMS Salisbury British ship in 1747 (references in Bhatt 2010). Randomized control trials (RCT) were introduced by Hill and others in 1946 study of streptomycin efficacy against tuberculosis. The effectiveness of RCT are now established and integral to regulation of drug development.

Use of clinical trials unfortunately has a longer history than recognition of human rights (Rice 2008). World War II Nazi medical research atrocities are well known (Berger 1990), so too the longitudinal study of Tuskegee syphilis study on African-Americans (Brandt 1978). But there are too many other examples: 1884 Hawaii, inoculation of Keanu by Dr. Arning with leprosy in exchange for commuting Keanu’s death sentence to life imprisonment (Keanu developed leprosy and died in 1890, Binford 1936); many studies of American Indians/Alaskan natives (Hodge 2012). Concerns about ethical treatment of participants in studies remains a challenge; see controversy over prospective randomized control trial (NCT00078182) of safety and efficacy of an HIV prophylactic tenofovir treatment in Cambodia (Singh and Mills 2005, Mills et al 2005).

Rules of conduct were established at Nuremberg, and subsequently extended and codified by Belmont Accords: core principles of respect for persons, beneficence, and justice. Ethical standards of who participates are institutionalized by IRB boards. True informed consent remains challenging (Rothwell et al 2021 and references therein).

Figure 1 shows how common in PUBMED randomized control trials and references to use of double blind design in research (Fig 1).

Figure 1. Search of PUBMED for “RCT” and “double blind” studies from 1950 to 2024.

Ethics of clinical and experimental research

Informed consent of subjects before proceeding in a clinical trial is a required, essential component of the design of a clinical trial. Guidelines for research conducted on human subjects originated from The Nuremberg Code (Shuster 1997). The Code was formulated 67 years ago, in August 1947, in Nuremberg, Germany, by American judges sitting in judgment of Nazi doctors accused of conducting torturous experiments on humans in the concentration camps (Shuster 1997). It served as a blueprint for today’s principles that ensure the rights of subjects in medical research. Achieving informed consent is not always straightforward (Nijhawan et al 2013), and we continue to see research that challenges ethical standards (eg, discussion in Suba 2014). Additionally, and perhaps less appreciated, the Nuremberg Code is justification for invasive animal research: animal research must precede human subject testing (Shuster 1997).

While informed consent is required, clearly, it is not enough. Emmanuel et al (2000) provide a framework for evaluating the ethics of a research program involving human subjects:

1. Value
2. Scientific validity
3. Fair subject selection
4. Favorable risk-benefit ratio
5. Independent review
6. Informed consent
7. Respect for enrolled subjects

An additional concept, clinical equipoise (Freedman 1987) is relevant. Freedman noted that the researcher must have “genuine uncertainty” with respect to the merits of each treatment, or an “honest null hypothesis.” If a consensus exists that one treatment is better than another, including placebo, then there is no null hypothesis and the research would be invalid (Emmanuel et al 2000). Take, for example, the suggestion that clinicians should withhold angiotensin converting inhibitors (ACE2) from their hypertensive Covid-19 patients (Fang et al 2020; discussed in Tignaneli et al 2020). The hypothesis comes from the observation that SARS-COV2, like SARS-Cov, binds with ACE2 receptor in order to invade the cell. Blocking ACE2 inhibitors then would reduce activation of pulmonary renin angiotensin system and subsequent lung injury. Tignaneli et al (2020) called this a case of clinical equipoise — they argued no evidence supports “routine discontinuation” of ACE inhibitors.

Returning to the framework, Emmanuel et al left the equipoise consideration off their list for a number of reasons — for example, clinical equipoise can lead researchers to view pursuit of research has the same weight as therapy. Importantly, the proposed framework shifts the focus from the researcher views to a structured process of oversight that may minimize exploitation. It emphasizes factors like independent review and informed consent as more reliable ethical safeguards.

Moreover, the Nuremberg Code is foundational but not the current, nor the sole guidance for research conducted on human subjects; modern biomedical research is guided by more comprehensive documents like the Declaration of Helsinki and the Belmont Report, in addition to federal regulations and Institutional Review Boards or IRB.

Guidelines mandate detail about experimental design.

Professional journals expect authors to provide detailed descriptions of all methodology, including aspects of experimental design. Fundamental to the aim of science, to increase our knowledge  An essential component of science To improve this kind of communication many journals and professional societies have promoted standards about what must be included in these descriptions. For example, efforts of the CONSORT, which stands for CONsolidated Standards Of Reporting Trials, at www.consort-statement.org, to improve the reporting of clinical trials by authors and provide guidelines for reviewers and editors is endorsed by more than 400 journals. The CONSORT checklist address

• Trial design
• Participants
• Interventions
• Outcomes
• Sample size
• Randomization
• Implementation
• Blinding
• Statistical methods

These nine elements were judged essential for authors to report how their study implemented or did not implement. The purpose of these items is to in order to improve reproducibility of published research. For animal research a similar list is available from ARRIVE (Kilkenny et al 2010). ARRIVE also addresses additional criteria and directs how these should be reported throughout the paper, not just in the methods section. Like CONSORT, hundred of journals have endorsed the ARRIVE 20-item checklist.

Clinical researchers must implement protocols to insure data management guidelines are followed. Clinical data management is a large topic in and of itself, so we won’t discuss this area further. However, good data management practice across disciplines share a number of features. For example, all data records should include metadata, where metadata refers to “information about data,” and would include enough information about the experiment, including

• dates and times of observations
• personnel
• facilities
• protocols used
• number of subjects
• list of variables with definitions
  • full name of variable plus any acronym
  • measurement units
  • instrumentation
  • notes about data quality
• conditions

and more (this is hardly an exhaustive list). Metadata therefore explains how data were obtained. Lists of variables are also called data dictionaries. If data are stored in spreadsheets, for example, then good practice includes including a worksheet with the metadata for the data set.

Note 1: We introduced metadata and data dictionaries with our discussion about data types in Chapter 3.1.

Questions

1. Be able to define the following terms

• case control
• case study
• cohort study
• cross sectional study
• observational study
• experimental study
• single arm trial
• single blind vs double-blinding in research design

2. Early in the Covid-19 pandemic, hydroxycholoquine was suggested for treating Covid-19 patients, and some called for prophylactic use of the malarial drug. Discuss the treatment hypothesis in the context of clinical equipoise.
3. Distinguish between case control prospective and case control retrospective studies and the kinds of inferences that can be made.

Quiz Chapter 5.4

Clinical trials

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Chapter 5 contents

• The basics explained
• Experiments
• Experimental and Sampling units
• Replication, Bias, and Nuisance variables
• Clinical trials
• Importance of randomization in experimental design
• Sampling from Populations
• References and suggested readings

5 – Experimental design

Beyond numbers.

During this course, you will learn about statistics, yes, but my hope and goal for your experience in this class is much more than that: statistical reasoning. To have statistical reasoning skills, you need to be comfortable with the context of how data are acquired, ie, data acquisition. It’s not just about knowing how an instrument performs, eg, under or over the limits of quantification characteristics of the instrument lead to censored missing values, missing not at random (MNAR). In a broad stoke view, data are obtained from two kinds of studies: observational studies and experimental (manipulative) studies. what a correctly designed experiment can tell you about the world, and how a poorly designed experiment works against you. At the end of the semester, you should be familiar with the issues of Randomization, Control, Independence, and Replication.

The basics explained.

Experimental design is a discipline within statistics concerned with the analysis and design of experiments. Design is intended to help research create experiments such that cause and effect can be established from tests of the hypothesis. We introduced elements of experimental design in Chapter 2.4. I recommend a quick re-read: We talk about the different types of bias that can affect research. We also point out parts of the problem you’ll need to think about when planning a project, so you can avoid or reduce bias from the start.

Here, we expand our discussion of experimental design. We begin with review of definitions and an outline of an important concept in statistics. First, we need to be clear about why we measure or conduct experiments. We do so to collect data (datum is the singular) about a characteristic or trait from a population. Data are observations: they include observations and measurements from instruments. At their best, data are the “facts” of science.

Measurement, Observation, Variables, Values.

Measurement is how we as scientists acquire our data (Chapter 3.4). The process of measuring involves the assignment of numbers, codes, or labels to observations according to rules established prior to any data collection (Stevens 1946, Houle et al 2011). Observations refer to the units of measurement, whereas variables are the characteristics or traits that are measured. A value refers to the particular number, score, or label assigned to a particular sample for a variable. Variables are generic, the thing being measured, values are specific to the subject or sample being measured for the variable. Each discipline in biology has its own set of variables and samples may or may not have different values for each variable measured. Variables are summarized as a statistic (eg, the sample mean), which is a number taken to estimate a parameter, which pertains to the population. Variables and parameters in statistics were discussed in Chapter 3.4. Because numbers or scores or labels can be assigned according to different rules, this means that variables may be measured on different kinds of scales or data types. The different kinds of data types were presented in Chapter 3.1.

Missing values.

A missing value refers to lack of a value for an observation or variable (Chapter 3.5).  Censored values, a type of missing value, include observations for which limited or partial information is available, eg, range, while a missing value lacks any information about the true value.

Missing values can affect analysis and many R algorithms are sensitive or may fail to run in the presence of missing values. Missing data may be of three kinds, and one of them, missing not at random (MNAR), can substantially influence the analysis. MNAR implies some observations are missing because of a systematic bias. Instrument limits of quantification are an example of systematic bias — for example, spectrophotometric absorbance readings of zero for a colorimetric assay (eg, Bradford protein assay) may not represent complete absence of the target, but rather, the lower detection limits of the instrument or the assay method (0.1 mg protein/mL in this case).

The other kinds of missing values are missing completely at random (MCAR) and missing at random (MAR). MCAR implies there is no association between any element of the experiment and the absence of a value. Analysis on MCAR data sets may support unbiased conclusions. MAR includes the random errors that occur during data acquisition: data may be lost because of operator error or power outage (shudder). Unlike MNAR, analysis of MAR, like MCAR data sets may still result in unbiased conclusions.

One consequence of missing values — a decision how best to handle the lost information. The options are either pairwise deletion or listwise deletion. Listwise means the entire row, all variables, are lost for any record with one or more missing values. You recorded root length, stem length, numbers of secondary roots, time to germinate, but the SPAD meter failed and there is no chlorophyl reading for seedling #212? Sorry, the entire row is deleted. Optionally, the missing data is deleted pairwise — only chlorophyl reading for #212 is lost, all other variables remain.

Users of R will quickly learn some algorithms immediately fail to run if not instructed how to process missing values. In some cases, missing values can be replaced by imputed values.

Cause & Effect.

Observations or measurements gathered under controlled conditions (experiments) are essential if we are to answer questions about populations, to separate cause and effect, where one or more events is directly the result of another factor, as opposed to anecdote, a story about an event which, by itself, cannot be used to cause from association (eg, spurious correlations, see Ch 16.2). Recall that anecdotal evidence typically comes from personal experience, where observations may be obtained by non-systematic methods. Well designed experiments, in the classical sense, permit discrimination among competing hypotheses in large part because observations are collected according to strict rules. Well developed hypotheses tested by well-designed experiments permit ruling out alternative explanations (sensu Pratt [1964] strong inference). Observational studies, or epidemiology studies if we are talking about investigations of risk assessment, also may contribute to discussions of cause and effect (see history of smoking by Doll 1998).

Medicine is replete with stories about how a patient showed a particular set of symptoms, and how a physician applied a set of diagnostic protocols. An outcome was achieved, and the physician reports the outcome and circumstances related to the patient to her colleagues. This is an example of a case study, and the focus of investigation is the individual, the patient. The doctor’s report will sound like, “I tried the standard treatment given the diagnosis, and the patient’s symptoms diminished, but later returned. I tried a higher dose, but the patient’s symptoms persisted unabated.” No inferences are made to a wider set of individuals and the report is anecdotal. If observations are made on several patients, this may be a case series.

In ecology, a field biologist may notice a six-legged adult frog (Scott 1999, Alvarez et al 2021) — since frogs typically have four legs, the six-legged frog attracts the biologist’s eye and he jots down the circumstances in which the frog were found: relative humidity, air temperature, ground temperature, where the frogs was found (on lower leaf of a philodendron plant). A water source near where the frog was found is tested for pH with a meter the biologist carries, and a water sample is taken for later testing of herbicides. The frog is collected so that it can be checked for skin parasites. Upon further inspection, the frog did indeed have parasites known to cause deformities in other frog species. However, note that this example too, is a case study. Although the biologist makes additional observations, any conclusions about why the frog has six legs is anecdotal.

From these case studies, no conclusions can be drawn. We cannot say why the patient failed to respond to treatment, nor can we say why the frog has six legs. Why? Because these are singular events, and a variety of explanations can be given as to their causes — importantly, no controls are available, so there’s no way to distinguish among possibilities.

From such anecdotes, however, experiments can be designed. The physician may decide to recruit additional patients with the diagnosed illness and apply the standard treatment to see if her anecdote is a single, unique event, or more indicative of a problem with the treatment. The biologist may collect other frogs from the area near where he found the six-legged frog and check to see if they, too, have the parasites. If additional patients fail to respond to the treatment, then the singular even is more likely to be a phenomenon. If the normal frogs also have similar levels of the parasite then it is unlikely that these parasites caused the malformed frog. With this simple step (recruiting similar patients, finding additional frogs), we can begin to make inferences about cause and effect and in some cases, to generalize our findings.

This is the objective of most statistical procedures, the concept of sampling from a reference population and making distinctions between groups within the sample. The difference between observational and experimental studies then is how the subjects are selected with respect to the groups. In an experiment, the researcher controls and decides which subject receives the treatment, therefore, allocation to groups is manipulated by the researcher. In contrast, subjects included in an observational study have already been “assigned” to a group, but not by us. Assignment to groups, smokers or non smokers, Type II diabetes or no diabetes (etc.), is done by nature.

Now, I do not wish to imply that research that cannot be generalized back to a reference population are worthless. Far from it. In fact, there is a strong argument for specificity. For example, much basic biological research depends on work or model organisms, which in turn may be further partitioned into specific genetic lines (cf. discussion in Rothman et al 2013). And my goodness, what we have learned about the devastation to oceanic islands like Guam when the brown tree snake was introduced (Fritts and Rodda 1998).  Strictly speaking, what has happened to Guam is a case history. But no one would argue that what has happened to Guam cannot happen to Hawaii and other oceanic islands (eg, United States Federal law 384-108 “Brown Tree Snake Control and Eradication Act of 2004”). In other words, even from case histories, generalizations can sometimes be made.

There can also be real reasons to ignore the issue of generality. One benefit of specificity is experimental control. Transgenic lines may differ by single gene knockout or by gene duplication, and clearly the aim of such studies is to evaluate the function (hence purpose) of the gene product (or its absence) on some phenotype. In this sense it may not seem important that an transgenic mouse is not representative of a wild outbred mouse population. However, this argument is fundamentally one of expedience — such studies do result in specific results, results that cannot be generalized beyond the strains involved. It ignores the issue of genetic background — all of the genes that affect a trait in addition to the candidate gene under study (Sigmund 2000; Lariviere et al 2001). Transgenic mice of different inbred strains or their hybrids may have very different alleles at other genes that may influence a phenotype, hence, the results of the gene knockdown or other engineering result in different outcomes. Results of genetic manipulations on inbred strains, no matter how sophisticated, the conclusions are strain- or hybrid cross-specific. Thus, although technically and financially difficult, conclusions are better, more generalizable, when conducted with many different inbred lines and verified in outbred mouse populations precisely because genetic background often influences function of single genes (Sigmund 2000; Lariviere et al 2001).

“Causal criteria:” Logic of causation in medicine.

This section is in progress. Just a list of key points and references

Throughout this text, emphasis on the power of experimentation is emphasized. Well designed experiments …

Henle-Koch’s postulates (1877, 1882), working on tuberculosis reported a set of causal criteria to establish link between a microorganism and a disease, are the following:

• The microorganism must be found in abundance in all organisms suffering from the disease, but should not be found in healthy organisms.
• The microorganism must be isolated from a diseased organism and grown in pure culture.
• The cultured microorganism should cause disease when introduced into a healthy organism.
• The microorganism must be reisolated from the inoculated, diseased experimental host and identified as being identical to the original specific causative agent.

Robert Koch wrote these more than 100 years ago, so, clearly, understanding of infectious disease has improved. Evan’s postulates, quoted from A Dictionary of Epidemiology, 5th edition (pp. 86-87).

1. Prevalence of the disease should be significantly higher in those exposed to the hypothesized cause than in controls not so exposed.
2. Exposure to the hypothesized cause should be more frequent among those with the disease than in controls without the disease—when all other risk factors are held constant.
3. Incidence of the disease should be significantly higher in those exposed to the hypothesized cause than in those not so exposed, as shown by prospective studies.
4. The disease should follow exposure to the hypothesized causative agent with a normal or log-normal distribution of incubation periods.
5. A spectrum of host responses should follow exposure to the hypothesized agent along a logical biological gradient from mild to severe.
6. A measurable host response following exposure to the hypothesized cause should have a high probability of appearing in those lacking this before exposure (eg, antibody, cancer cells) or should increase in magnitude if present before exposure. This response pattern should occur infrequently in persons not so exposed.
7. Experimental reproduction of the disease should occur more frequently in animals or humans appropriately exposed to the hypothesized cause than in those not so exposed; this exposure may be deliberate in volunteers, experimentally induced in the laboratory, or may represent a regulation of natural exposure.
8. Elimination or modification of the hypothesized cause should decrease the incidence of the disease (eg, attenuation of a virus, removal of tar from cigarettes).
9. Prevention or modification of the host’s response on exposure to the hypothesized cause should decrease or eliminate the disease (eg, immunization, drugs to lower cholesterol, specific lymphocyte transfer factor in cancer).
10. All of the relationships and findings should make biological and epidemiological sense.

Fredericks, D. N., & Relman, D. A. (1996). Sequence-based identification of microbial pathogens: a reconsideration of Koch’s postulates. Clinical microbiology reviews, 9(1), 18-33.

Correlation (association) does not imply causation, a well-worn truism in any application of critical thinking skills. Conversely, causation does imply association (correlation); If a change in one variable directly changes another variable, there will be a statistical association between the two variables. Thus, a correlation between two variables is necessary, but not sufficient evidence for cause and effect between two variables.

However, sometimes association does point to a cause. A familiar example is association between tobacco cigarette smoking causes lung cancer.  Surgeon General Luthar Terry’s 1964 report (link to document in National Library of Medicine), presented a strong case linking smoking to elevated risk of lung cancer and coronary artery disease.

Bradford Hill’s guidelines to evaluate causal effects based on epidemiology (Hill 1965, see also Sussar 1999, Fedak et al 2015). Set of necessary and sufficient conditions, inductive reasoning.

1. Strength of association
2. Consistency of observed association
3. Specificity of association
4. Temporal relationship of the association
5. Biological gradient, eg, a dose-response curve
6. Biological plausibility
7. Coherence, the cause and effect inference should not conflict with what is known about the etiology of a disease.

Follows and extends David Hume’s (1739) causation criteria: association (Hill #1), cause precedes effect (Hill #4), direction of connection.

Validity.

An obvious objective of research is to reach valid conclusions about fundamental questions. A helpful distinction between the specific and the generalizable experiment is to recognize there are two forms of validity in research: internal validity and external validity (Elwood 2013). Internal validity is the quality of a designed study that determines whether cause and effect can be determined. Random assignment of subjects to treatment groups enhances the internal validity of the study. External validity relates to how general the assessment of cause and effect can be to other populations. Thus, random sampling from a reference population has to do with whether or not the study has external validity.

Additional definitions.

We proceed now with definitions. We use the term population in a special and restrictive way in statistics. Our definition includes the one you are already familiar with, but it also means more than that.

Populations are the entire group of individuals that you want to investigate. In statistics, the entire groups is actually the entire class with the observation — so if we are referring to the average body weight of house mice, we’re actually referring to the body weight as the population — it’s a subtle distinction, not essential for our introduction to biostatistics. When we conduct experiments and apply statistical tests on collected data, we generally intend to make inferences (draw conclusions) from our results back to the population.

Population has a strict application in statistics, but the definition also includes our general understanding of the word population. For example, Examples of a population in the general sense one may refer to include: .… the entire human population existing today .… the entire collection of U.S. citizens. .… all the individuals in an entire species. .… all individuals in a population of a species (eg, house mice in a dairy barn in Hawai’i) .… all of us in this classroom (if we are ONLY interested in US) If you could measure the entire population then there would be no need to do (or learn) statistics! Populations usually are in the thousands, millions, or billions of individuals. Here, population is used in the everyday sense that we think of — a collection of individuals that share a characteristic.

A more formal definition of “population” in statistics reads as follows: A statistical population is the complete set of possible measurements on a trait or characteristic corresponding to the entire collection of sampling units for which conclusions are intended.

To conclude, in this class, when we talk about population, we will generally be using it in the everyday sense of the word. However, keep in mind that the definition is more restrictive than that and the key is to identify what sampling units are measured.

Conclusions.

This is only the beginning, the basics of experimental design. Beginning with RA Fisher‘s 1935 book, The Design of Experiments (nine editions, some freely accessible via internet search), which is still very much worth reading, entire books are written on the subject, as you can well imagine.

We will also return to the subject of Experimental Design throughout the book. We will return to random sampling in Chapter 5.5. Next we discuss distinctions between experiments and observational studies with respect to sampling of populations.

A bit of a disclaimer here before proceeding; while I cite several papers for examples in experimental design in Chapter 5, reader’s should not read into this that I am either criticizing or endorsing the published experiments. Experimental design will always have elements of compromise — the trick of course is knowing which choices influence validity (Thompson and Panacek 2006).

Questions.

1. Define in your own words the following terms

• reference population
• subjects
• specific versus general conclusions
• random sampling
• convenience sampling
• haphazard sampling
• research validity

2. Revisit our cell experiment, “What is the sampling unit in the following cell experiment?” How would you change this experiment so that there will be biological and not just technical replication?
3. Describe the type of sampling for each research scenario described?

• All African snails on a staircase at Chaminade University are collected on a Thursday evening.
• All African snails on a staircase at Chaminade University are collected every Thursday evening for six months.
• All African snails on all staircases at Chaminade University are collected.
• African snails are studied in the lab, then returned to the areas from which they were collected. Days later, the researcher collects snails from the same area.
• African snails are studied in the lab, then returned to the areas from which they were collected. Days later, the researcher collects snails from a different area.
• The Chaminade University campus is divided into grids. Grids that include stairwells are marked. Before collecting snails, the researcher randomly selects from the list of grids and searches for snails only in those grids selected from the list.
• 
  Figure 1. Giant African Snail (Lissachatina fulica, formerly Achatina fulica). Image by M. Dohm.

4. This next scenario may be evaluated by you for potential sources of bias. Review the list of bias listed above. A researcher wants to do a population count of feral cats on campus. Feral cats are active at night, so he decides to set up a feeding station near a light post. The researcher sits all night in a parked car yards away and watches the feeding station for visits by cats. The researcher repeats these observations over the course of a week, moving the feeding station to different campus locations each night, and reports the total number of cats seen during the week as an estimate of the population size. Be able to discuss this study in terms of potential and actual bias.

Quiz

Including the quiz on this page, a total of 65 questions among the several subchapters, a mix of true or false and multiple choice question format.

Quiz Chapter 5

Experimental design

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Chapter 5 contents

• The basics explained
• Experiments
• Experimental and Sampling units
• Replication, Bias, and Nuisance Variables
• Clinical trials
• Importance of randomization in experimental design
• Sampling from Populations
• References and suggested readings

2.4 – Experimental Design and rise of statistics in medical research

Experiments and observations: Finding answers.

.

How to identify cause and effect, and the kinds of evidence that can be inferred from the various approaches to study causes of  disease has became a major source of disagreement in the news. In a fascinating study, Pew Research Center reported “half of U.S. adults under 50 say they get health and wellness information from social media influencers or podcasts,” and, only about 17% of these influencers report “conventional medicine” training (Report, May 7 2026).  For our purposes, I made substantial updates to this page in the fifth month after WHO had declared the Covid-19 pandemic (CDC timeline), and continue to do so today. 

The pandemic left many life-lessons, for scientists and public-health supporters, but also for everyone who lived through those times. One of the lessons was how to deal with the challenges of finding treatments in real time. If you followed the news early in the pandemic, you know of the appeal from some (including Donald Trump, the then-President of the United States, Boseley 2020), for use of an anti-parasite drug, hydroxychloroquine, as prophylactic or treatment for active Covid-19 infection (cf. Liu et al 2020). The FDA as well as other institutions rapidly advised against use, in part because experimental design concerns were raised for early studies (Kupferschmidt, 2020). The issue remains contentious for some (eg, Health and Human Services Secretary Robert F. Kennedy Jr., CNN August 2, 2026 interview).

Thus, job number one for students of biostatistics is to learn how to weigh arguments for or against therapies or treatments offered. The purpose of this page is to introduce these issues — how to judge whether a treatment is effective or not. 

We will spend some time later on statistical aspects of experimental design (Chapter 5), but we begin with Randomized Control Trials, or RCT, as a model for our discussion of experimental studies. The RCT we recognize today owes its beginning to the 1948 studies on streptomycin use to treat tuberculosis (British Medical Research Council 1948), but of course, the foundations of RCT and experimental design in general, go back much earlier than that date (Chalmers 2011, Hairton and Locascio 2018). For a number of reasons the RCT — experimental, prospective, double-blind clinical trial with random selection of subjects from a reference population and random assignment of subjects to a treatment group or an appropriate placebo treatment control group — is considered the “gold standard” method for producing knowledge (Kaptchuk 2001, Hairton and Locascio 2018). 

Technically, RCT are intervention trials, a specific application of the more general definition of an experiment. That is, the researchers tests a potential drug or therapy in people to observe its effect while holding other variables constant.  Experimental studies imply that the researcher imposed treatments or controls onto subjects. The subjects are followed and outcomes are recorded. Thus, experiments by definition are also prospective studies — the outcome is recorded for subjects after some period of time. With a well-designed experiment, the researcher may have evidence to support the claim that, for example, Treatment A causes the outcome.

RCT applied to human health can have profound impact on lives.

The ALLHAT-LLT (JAMA, 2002) trial tested whether adding the cholesterol-lowering drug pravastatin to standard care would reduce heart attacks and deaths in people with high blood pressure and moderately high cholesterol. The study found no significant benefit compared to usual care, suggesting that statin therapy may not always provide extra protection in this group. Its results helped refine how doctors balance blood pressure and cholesterol treatment in heart disease prevention.

The Women’s Health Initiative (JAMA, 2002) trial tested the effects of combined estrogen and progestin therapy in healthy postmenopausal women. It found that while the therapy slightly reduced the risk of fractures and colon cancer, it increased the risk of heart disease, stroke, and breast cancer. These results transformed medical guidance by showing that hormone therapy should not be routinely used to prevent chronic disease in postmenopausal women.

The Du Toit et al. (NEJM, 2015) study showed that introducing peanut-containing foods early in life — rather than avoiding them — greatly reduced the risk of developing peanut allergies in high-risk infants. This landmark randomized trial changed how doctors think about food allergies, leading to new guidelines that encourage early introduction instead of avoidance.

And more recently, we have study reported by Deanfield et al (Lancet, 2025), which found that semaglutide reduced the risk of major adverse cardiovascular events (MACE) in adults with overweight or obesity and established cardiovascular disease—even if they did not lose much weight or had lower baseline adiposity.

In contrast, observational studies are those in which treatments arise by acts of nature. In both experiments and observational studies, there can be treatment and control groups; the distinction between the types of studies is how assignment of subjects to treatments were affected. Observational studies generally are retrospective studies — the outcome has already occurred, the researcher follows up to identify differences among the groups that may account for different outcomes. Examples of observational, retrospective study designs include cross-sectional and case control; cohort studies are prospective studies. Observational studies are discussed further in Chapter 5.4 – Clinical trials.

Compared to observational studies, in principle, experiments can establish cause and effect. Cause and effect refers to an explanation about relationship between two events or objects. In biology, Ernst Mayr (1904 – 2005) distinguished between two levels of explanation, proximate (how) explanations and ultimate (why) explanations (Mayr 1961, cf. Laland et al. 2011). As you know, our mechanism for identifying cause and effect is application of the Scientific Method (Chapter 2.5). Discussions of how to detect cause and effect are provided throughout this book, but emphasized in a few sections (Chapter 16.2 and 16.3).

Good experiments.

The principles of good experiments include many steps beyond simply choosing treatments and controls. In Chapter 5 we’ll go into more depth, but I wished to list for you some of the key principles of good experimental design. With respect to human-subject research, the researcher needs to protect against many sources of potential bias.

• Randomization of subjects assigned to treatment groups controls for individual differences.
• Controls (eg, Placebos) are a means to establish controls in a study so that effects may be attributed to the active treatment.
• Single-blind implies that the subject does not know what treatment was given. 
  • Double-blind implies that not only is the subject unaware of the treatment received, but, crucially, neither does the researcher.
• The double-blind design — neither the patient-subject nor the researchers know who received the placebo or the treatment — controls for subtle biases.

The experimenter may influence the outcome of the experiment if knowledge about who received the placebo or the new drug; the subject may respond differently with knowledge that they received the placebo and not the new drug. The key intent in this experimental design is to avoid systematic error, errors in studies that may occur because of our conscious and unconscious beliefs and biases. Placebos are used as treatments because people (and animals!) sometimes get better (or worse) with or without treatment; thus, to be effective, subjects receiving a new drug must get better more frequently than do subjects on placebo. Importantly, the well-designed placebo allows the researcher to gain insight into the mechanism of action by the new drug.

A case to consider: Comparing migraine treatments.

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Consider the following experiment (Diener et al 2006; see also Liu et al 2018): subjects who had several migraines per month were treated with acupuncture, sham-acupuncture, or standard treatments including beta blockers, calcium channel blockers, or antiepileptic drugs. After 26 weeks the reductions in reported migraines was compared. The authors reported that there was no difference in numbers of migraines among patients who received the different therapy treatments. The authors conclude that because acupuncture lacks side-effects that may occur with standard therapies acupuncture may be a good choice for patients seeking relief from migraine. This is a classic experiment — subjects were assigned to treatments by the researchers. At least in principle, if one treatment group showed better outcomes, the improvement could be attributed to the treatment. 

Another case to consider: When the cause isn’t clear.

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Consider the following example. My dad was diagnosed with lung cancer in his late 70s; his left lung showed many spots when imaged and biopsy confirmed. Surgeons removed half of the lung and after several years he was considered cancer free. Why did he develop cancer in the first place? If you immediately think, “He’s a smoker,” that’s not a good explanation — and shame on you, you’re first instinct was to blame the patient (see discussion in Huff 2013). Dad last smoked tobacco in his early thirties (latency smoking-lung cancer link about 20 years, Lipfert et al 2019).

Tobacco smoking is not the only environmental trigger for lung cancer. Cancer of the lung in non-smokers is the seventh leading cause of cancer mortality worldwide (Field and Withers 2012). Long term exposure to radon gas, a naturally occurring, radioactive noble gas has been linked to lung cancer (EPA). I grew up on Vashon Island, Washington, in a non-smoking home environment. Radon levels on Vashon Island and other areas around Puget Sound are low (source: Washington State Department of Health). Radon is out as an explanation.

What other environmental sources may be linked to cancer? Vashon Island is rural, but, as it turned out, within range of effluent from a copper smelter located in nearby Ruston, Pierce County (Fig 1; my home was 17 km distance from the smelter). 

Figure 1. Left: ASARCO smelter, Ruston, Washington, image from Department of Ecology, State of Washington. Direction of smoke from the stack is north, toward Vashon Island. Right: Voronoi map of arsenic and lead affected areas. image from kingcounty.gov. Darker regions correspond to heavier arsenic and lead contamination of soils.

The smelter was last in operation in 1986 and was torn down in 1993 (EPA publication number 910R94001). The smelter stack rose more than 500 feet dispersing smoke laden with heavy metals, notably inorganic arsenic and lead, into the air (Bromenshenk et al. 1985). Over the smelter’s 68 years of service, winds carried away the smoke to my island and to other areas known now as the “Ruston-Vashon Island Exposure Pathway” (Kalman et al 1990). The former smelter site was among the first listed Superfund sites (1983) in the United States by the EPA. Thus, tens of thousands of people were (and continue to be) exposed to the heavy metals deposited into the soils, forming a distinct exposure group (Milham & Strong 1974; Kalman et al 1990; EPA 2000). Arsenic exposure can be via inhalation, skin, or in drinking water — areas of Vashon-Maury island continue to have high levels of arsenic in both the soil and in  any domestic water wells (PublicationNo. 14-09-044, Department of Ecology State of Washington).

Is arsenic exposure by inhalation a plausible mechanism for my Dad’s lung cancer? As shown in Fig 1, the soils on Vashon near my home were heavily impacted by the smelter. Exposure could have come about from exposure during routine yard work — I have memories of clouds of dust kicked up by the lawn mower during spring and summers. Thus, an exposure route is possible. What evidence can we come up with?

Figure 2A shows negative association between lung and bronchial cancer incidence rates per 100L persons, adjusted for age, for several Washington state counties between 2000 and 2020 and distance from the smelter in Ruston. For comparison, Figure 2B shows no association between bladder cancer incidence rates per 100K for the same counties and time period and distance from the smelter. Workers exposed to arsenic have higher rates of lung cancer (Sullivan 2007, Wei et al 2019; see Enterline et al 1987 for a study a study based on cancer of workers at the smelter). Cultured lung cells exposed to arsenic associated with changes in gene expression (Clancy et al 2012). Coincidently, two of the family dogs developed and died of cancer as did one female goat. Perhaps my dad’s lung cancer was attributed to long exposure to arsenic (a decade after the cancer, and long after he stopped with yard work, his blood readings for arsenic were in the range of a modest 11 μg/L).  

Figure 2. County cancer rates (A, lung and bronchial; B, bladder) from 2000 – 2020 vs distance in kilometers from ASARCO smelter, Ruston, WA. Data compiled from Washington Tracking Network (WTN). The counties were King (55 km), Kitsap (39.28 km), Pierce (38.48 km), San Juan ( 141.43 km), Snohomish (100.73 km), and Spokane (385.34 km).

If this scenario seems plausible, I hope you immediately recognize it as a case of confirmation bias (see Chapter 2.6). Putting aside for a moment the different arsenic species, each with different LD₅₀ (the lethal dose needed to kill half the population — see Chapter 20.10), the difficulty ascribing arsenic as a causal agent for my Dad’s cancer is that many other exposures happened simultaneously. For example, indoor carpets are a primary source of several volatile organic compounds (Haines et al 2020). Prior to 1980 carpets may have included formaldehyde and other known carcinogenic agents. Dad commuted by car between work and home — with a ferry ride between — for decades (until the early 1990s), routinely traveling heavily congested roadways, this during the years prior to and the early years of the Clean Air Act of Environmental Protection Agency of the United States (it wasn’t until 1981 that new cars met EPA emission standards: Clean Air Act timeline here). Thus, all commuters including my Dad were exposed to gasoline combustion emissions, many known to be carcinogenic (Parent et al 2007). Moreover, a limited study by Public Health of Seattle and King County (2001) found rates of cancer on Vashon between 1980 and 1988 were similar to other areas in King County.

Summary.

It’s easy to fall into the trap that experiments — and by extension meta-analysis and systematic reviews — are the best tools offered by science for developing knowledge about the world, and other approaches suffer by comparison. But after even a bit of reflection, we should recognize that it can’t be that simple. While we now “know” tobacco cigarette smoking increases lung cancer risk, and many experiments with animal models convincingly show the link (eg, Hutt et al 2005), no human experiment in the strict sense, ie, prospective, randomized control trial, has ever been conducted (hint: it would be unethical, see discussion in Allmark and Tod 2016). Instead, the accumulated evidence from observational studies on exposures of different populations over the years overwhelmingly points to smoking as a leading risk factor (cause) of lung and other cancers — an example of Hill’s guidelines of causality.  We end with a quote:

RCTs can play a role in building scientific knowledge and useful predictions but they can only do so as part of a cumulative program, combining with other methods, including conceptual and theoretical development, to discover not ‘what works’, but ‘why things work’ (p 2, Deaton and Cartwright 2017).

Questions.

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1. Write up three learning outcomes for this page. Hint: Point your favorite generative AI to this page and ask for help.
2. Was my Dad’s lung cancer attributable to his 40 years plus exposure to soil arsenic (he’s a non-smoker)? How should we approach this question?
3. In Diener et al (2006), the authors concluded that because acupuncture lacks side-effects that may occur with standard therapies acupuncture may be a good choice for patients seeking relief from migraine. Do you agree with the authors?
4. Ethical standards evolve with time. An ongoing debate in research is whether and how placebos are to be used in human subjects research. Placebos are a means to establish controls in a study so that effects may be attributed to the active treatment. The “gold standard” of clinical trials is considered to be the randomized double-blind design — neither the patient-subject nor the researchers know who receives the placebo or the treatment. Following review of the WHO report on Use of Placebos in Vaccine Trials, pick one study and evaluate whether or not the decision to use placebos was warranted in your opinion.
5. I searched PUBMED for “double-blind” by decade and found the following results (August 2018) (Table 1). Open R and/or R Commander and create two variables, then generate a scatter plot. Describe the shape of the relationship between number of publications citing “double-blind” and time (eg, 1950 – 1959, 1960 – 1969, and so on).

5. Here’s one way to enter this data into R. At the R prompt (or in the R Script window of R Commander), create two variables, Decade and Pubs Decade <- c(seq(1950, 2020, by=10)) Pubs <- c(59,995,7161,24728,39670,54011,57043) Make an XY scatter plot plot(Decade,Pubs)
6. Repeat the PUBMED search as above but search for “placebo”. Make a table like the one above and provide a scatterplot of your results.
7. Is the concept of a placebo relevant if the subjects in your experiment are yeast cells, not humans?
   • Similarly, if your subjects are yeast cells, how does the concept of performing experiments “blind” apply?
8. Ethical standards change with time. An ongoing debate in research is whether and how placebos are to be used in human subjects research.
   • If placebos are so important, why is their use a concern in clinical trials?
   • Following review of the WHO report on Use of Placebos in Vaccine Trials (see Readings below), pick one study and evaluate whether or not the decision to use placebos was warranted in your opinion.

R notes for question 5:

• <- is an assignment operator (assignOP); everything to the right of <- is assigned to the object named to the left of the <- operator. You can instead use = in place of <- , but because = is also used in other contexts besides assignment, a quick look at blogs by data scientists will find a preference to use <- for clarity and consistency.
• c() “combines” arguments into a vector.
• seq() is used to generate a sequence of numbers between a lower and an upper limit; if by = n is included, the sequence will be increased by the value n. If omitted, then the sequence is increased by 1.

Quiz Chapter 2.4

Experimental Design and rise of statistics in medical research

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Chapter 2 contents.

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• Introduction
• Why biostatistics?
• Why do we use R Software?
• A brief history of (bio)statistics
• Experimental Design and rise of statistics in medical research
• Scientific method and where statistics fits
• Statistical reasoning
• Chapter 2 – References and suggested reading