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 (e.g., 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.
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 will bias your results and can lead to incorrect interpretation of results. 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 (e.g., 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, e.g., 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.
The graphic below shows the transmission grid in the continental United States (Fig. 4). 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 4. 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 (e.g., report on a cluster of breast cancer in men working in office adjacent to high EMF, Milham 2004).
1. I claimed that Graph B in Figure 8 was generated by a random process while Graph B was not. The results are: Graph A, each cell in the grid has a point; In graph B, ten cells have at least one point, six cells are empty. Which probability _____ distribution applies? A. beta B. binomial C. normal D. poisson
2. True or False. If sample with replacement is used, a subject may be included more than once.
3. Use the sample() with and without replacement on the object (see help with R below)
a) set of 3
b) set of 4
4. Confirm the claim by calculating the probability of Graph A result vs Graph B result (see R script below).
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 (i.e., no need for you tp type them).
First, create some variables. Vectors aa and bb contain my two age sequences.
Second, append vector bb to the end of vector aa
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!).
Fourth, start building a data frame, then sort it by age. Will be adding additional variables to this data frame
Fifth, divide the variable again into two subsets of 30 and get the averages
Sixth, create an index variable, random order without replacement
Add the new variable to our existing data frame, then print it to check that all is well
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.
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.
Eighth, create our new treatment groups, again of n = 30 each, then get the means ages for each group.
Get the minimum and maximum values for the groups
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
The second group called dd
Create a new variable called BMI by joining cc and dd
Add the BMI variable to our data frame.
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.
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
Get the means of the new groups
That’s all of the work!
Design of Experiments > Randomization
Randomization in an experiment is where you choose your experimental participants randomly . For example, you might use simple random sampling , where participants names are drawn randomly from a pool where everyone has an even probability of being chosen. You can also assign treatments randomly to participants, by assigning random numbers from a random number table.
If you use randomization in your experiments, you guard against bias . For example, selection bias (where some groups are underrepresented) is eliminated and accidental bias (where chance imbalances happen) is minimized. You can also run a variety of statistical tests on your data (to test your hypotheses) if your sample is random.
The word “random” has a very specific meaning in statistics. Arbitrarily choosing names from a list might seem random, but it actually isn’t. Hidden biases (like a subconscious preference for English names, names that sound like friends, or names that roll off the tongue) means that what you think is a random selection probably isn’t. Because these biases are often hidden, or overlooked, specific randomization techniques have been developed for researchers:
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Most, if not all, guidelines, recommendations, and other texts on Good Research Practice emphasize the importance of blinding and randomization. There is, however, very limited specific guidance on when and how to apply blinding and randomization. This chapter aims to disambiguate these two terms by discussing what they mean, why they are applied, and how to conduct the acts of randomization and blinding. We discuss the use of blinding and randomization as the means against existing and potential risks of bias rather than a mandatory practice that is to be followed under all circumstances and at any cost. We argue that, in general, experiments should be blinded and randomized if (a) this is a confirmatory research that has a major impact on decision-making and that cannot be readily repeated (for ethical or resource-related reasons) and/or (b) no other measures can be applied to protect against existing and potential risks of bias.
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‘When I use a word,’ Humpty Dumpty said in rather a scornful tone, ‘it means just what I choose it to mean – neither more nor less.’
Lewis Carroll ( 1871 )
Through the Looking-Glass, and What Alice Found There
In various fields of science, outcome of the experiments can be intentionally or unintentionally distorted if potential sources of bias are not properly controlled. There is a number of recognized risks of bias such as selection bias, performance bias, detection bias, attrition bias, etc. (Hooijmans et al. 2014 ). Some sources of bias can be efficiently controlled through research rigor measures such as randomization and blinding.
Existing guidelines and recommendations assign a significant value to adequate control over various factors that can bias the outcome of scientific experiments (chapter “Guidelines and Initiatives for Good Research Practice”). Among internal validity criteria, randomization and blinding are two commonly recognized bias-reducing instruments that need to be considered when planning a study and are to be reported when the study results are disclosed in a scientific publication.
For example, editorial policy of the Nature journals requires authors in the life sciences field to submit a checklist along with the manuscripts to be reviewed. This checklist has a list of items including questions on randomization and blinding. More specifically, for randomization, the checklist is asking for the following information: “If a method of randomization was used to determine how samples/animals were allocated to experimental groups and processed, describe it.” Recent analysis by the NPQIP Collaborative group indicated that only 11.2% of analyzed publications disclosed which method of randomization was used to determine how samples or animals were allocated to experimental groups (Macleod, The NPQIP Collaborative Group 2017 ). Meanwhile, the proportion of studies mentioning randomization was much higher – 64.2%. Do these numbers suggest that authors strongly motivated to have their work published in a highly prestigious scientific journal ignore the instructions? It is more likely that, for many scientists (authors, editors, reviewers), a statement such as “subjects were randomly assigned to one of the N treatment conditions” is considered to be sufficient to describe the randomization procedure.
For the field of life sciences, and drug discovery in particular, the discussion of sources of bias, their impact, and protective measures, to a large extent, follows the examples from the clinical research (chapter “Learning from Principles of Evidence-Based Medicine to Optimize Nonclinical Research Practices”). However, clinical research is typically conducted by research teams that are larger than those involved in basic and applied preclinical work. In the clinical research teams, there are professionals (including statisticians) trained to design the experiments and apply bias-reducing measures such as randomization and blinding. In contrast, preclinical experiments are often designed, conducted, analyzed, and reported by scientists lacking training or access to information and specialized resources necessary for proper administration of bias-reducing measures.
As a result, researchers may design and apply procedures that reflect their understanding of what randomization and blinding are. These may or may not be the correct procedures. For example, driven by a good intention to randomize 4 different treatment conditions (A, B, C, and D) applied a group of 16 mice, a scientist may design the experiment in the following way (Table 1 ).
The above example is a fairly common practice to conduct “randomization” in a simple and convenient way. Another example of common practice is, upon animals’ arrival, to pick them haphazardly up from the supplier’s transport box and place into two (or more) cages which then constitute the control and experimental group(s). However, both methods of assigning subjects to experimental treatment conditions violate the randomness principle (see below) and, therefore, should not be reported as randomization.
Similarly, the use of blinding in experimental work typically cannot be described solely by stating that “experimenters were blinded to the treatment conditions.” For both randomization and blinding, it is essential to provide details on what exactly was applied and how.
The purpose of this chapter is to disambiguate these two terms by discussing what they mean, why they are applied, and how to conduct the acts of randomization and blinding. We discuss the use of blinding and randomization as the means against existing and potential risks of bias rather than a mandatory practice that is to be followed under all circumstances and at any cost.
Randomization can serve several purposes that need to be recognized individually as one or more of them may become critical when considering study designs and conditions exempt from the randomization recommendation.
First, randomization permits the use of probability theory to express the likelihood of chance as a source for the difference between outcomes. In other words, randomization enables the application of statistical tests that are common in biology and pharmacology research. For example, the central limit theorem states that the sampling distribution of the mean of any independent, random variable will be normal or close to normal, if the sample size is large enough. The central limit theorem assumes that the data are sampled randomly and that the sample values are independent of each other (i.e., occurrence of one event has no influence on the next event). Usually, if we know that subjects or items were selected randomly, we can assume that the independence assumption is met. If the study results are to be subjected to conventional statistical analyses dependent on such assumptions, adequate randomization method becomes a must.
Second, randomization helps to prevent a potential impact of the selection bias due to differing baseline or confounding characteristics of the subjects. In other words, randomization is expected to transform any systematic effects of an uncontrolled factor into a random, experimental noise. A random sample is one selected without bias: therefore, the characteristics of the sample should not differ in any systematic or consistent way from the population from which the sample was drawn. But random sampling does not guarantee that a particular sample will be exactly representative of a population. Some random samples will be more representative of the population than others. Random sampling does ensure, however, that, with a sufficiently large number of subjects, the sample becomes more representative of the population.
There are characteristics of the subjects that can be readily assessed and controlled (e.g., by using stratified randomization, see below). But there are certainly characteristics that are not known and for which randomization is the only way to control their potentially confounding influence. It should be noted, however, that the impact of randomization can be limited when the sample size is low. Footnote 1 This needs to be kept in mind given that most nonclinical studies are conducted using small sample sizes. Thus, when designing nonclinical studies, one should invest extra efforts into analysis of possible confounding factors or characteristics in order to judge whether or not experimental and control groups are similar before the start of the experiment.
Third, randomization interacts with other means to reduce risks of bias. Most importantly, randomization is used together with blinding to conceal the allocation sequence. Without an adequate randomization procedure, efforts to introduce and maintain blinding may not always be fully successful.
There are several randomization methods that can be applied to study designs of differing complexities. The tools used to apply these methods range from random number tables to specialized software. Irrespective of the tools used, reporting on the randomization schedule applied should also answer the following two questions:
Is the randomization schedule based on an algorithm or a principle that can be written down and, based on the description, be reapplied by anyone at a later time point resulting in the same group composition? If yes, we are most likely dealing with a “pseudo-randomization” (e.g., see below comments about the so-called Latin square design).
Does the randomization schedule exclude any subjects and groups that belong to the experiment? If yes, one should be aware of the risks associated with excluding some groups or subjects such as a positive control group (see chapter “Out of Control? Managing Baseline Variability in Experimental Studies with Control Groups”).
An answer “yes” to either of the above questions does not automatically mean that something incorrect or inappropriate is being done. In fact, a scientist may take a decision well justified by their experience with and need of particular experimental situation. However, in any case, the answer “yes” to either or both of the questions above mandates the complete and transparent description of the study design with the subject allocation schedule.
One of the common randomization strategies used for between-subject study designs is called simple (or unrestricted) randomization. Simple random sampling is defined as the process of selecting subjects from a population such that just the following two criteria are satisfied:
The probability of assignment to any of the experimental groups is equal for each subject.
The assignment of one subject to a group does not affect the assignment of any other subject to that same group.
With simple randomization, a single sequence of random values is used to guide assignment of subjects to groups. Simple randomization is easy to perform and can be done by anyone without a need to involve professional statistical help. However, simple randomization can be problematic for studies with small sample sizes. In the example below, 16 subjects had to be allocated to 4 treatment conditions. Using Microsoft Excel’s function RANDBETWEEN (0.5;4.5), there were 16 random integer numbers from 1 to 4 generated. Obviously, this method has resulted in an unequal number of subjects among groups (e.g., there is only one subject assigned to group 2). This problem may occur irrespective of whether one uses machine-generated random numbers or simply tosses a coin.
Subject ID | 1 | 2 | 3 | 4 | 5 | 6 | 7 | 8 | 9 | 10 | 11 | 12 | 13 | 14 | 15 | 16 |
Group ID | 4 | 1 | 1 | 3 | 3 | 1 | 4 | 4 | 3 | 4 | 3 | 3 | 4 | 2 | 3 | 1 |
An alternative approach would be to generate a list of all treatments to be administered (top row in the table below) and generate a list of random numbers (as many as the total number of subjects in a study) using a Microsoft Excel’s function RAND() that returns random real numbers greater than or equal to 0 and less than 1 (this function requires no argument):
Treatment | 1 | 1 | 1 | 1 | 2 | 2 | 2 | 2 | 3 | 3 | 3 | 3 | 4 | 4 | 4 | 4 |
Random number | 0.76 | 0.59 | 0.51 | 0.90 | 0.64 | 0.10 | 0.50 | 0.48 | 0.22 | 0.37 | 0.05 | 0.09 | 0.73 | 0.83 | 0.50 | 0.43 |
The next step would be to sort the treatment row based on the values in the random number row (in an ascending or descending manner) and add a Subject ID row:
Subject ID | 1 | 2 | 3 | 4 | 5 | 6 | 7 | 8 | 9 | 10 | 11 | 12 | 13 | 14 | 15 | 16 |
Treatment | 3 | 3 | 2 | 3 | 3 | 4 | 2 | 2 | 4 | 1 | 1 | 2 | 4 | 1 | 4 | 1 |
Random number | 0.05 | 0.09 | 0.10 | 0.22 | 0.37 | 0.43 | 0.48 | 0.50 | 0.50 | 0.51 | 0.59 | 0.64 | 0.73 | 0.76 | 0.83 | 0.90 |
There is an equal number of subjects (four) assigned to each of the four treatment conditions, and the assignment is random. This method can also be used when group sizes are not equal (e.g., when a study is conducted with different numbers of genetically modified animals and animals of wild type).
However, such randomization schedule may still be problematic for some types of experiments. For example, if the subjects are tested one by one over the course of 1 day, the first few subjects could be tested in the morning hours while the last subjects – in the afternoon. In the example above, none of the first eight subjects is assigned to group 1, while the second half does not include any subject from group 3. To avoid such problems, block randomization may be applied.
Blocking is used to supplement randomization in situations such as the one described above – when one or more external factors change or may change during the period when the experiment is run. Blocks are balanced with predetermined group assignments, which keeps the numbers of subjects in each group similar at all times. All blocks of one experiment have equal size, and each block represents all independent variables that are being studied in the experiment.
The first step in block randomization is to define the block size. The minimum block size is the number obtained by multiplying numbers of levels of all independent variables. For example, an experiment may compare the effects of a vehicle and three doses of a drug in male and female rats. The minimum block size in such case would be eight rats per block (i.e., 4 drug dose levels × 2 sexes). All subjects can be divided into N blocks of size X∗Y, where X is a number of groups or treatment conditions (i.e., 8 for the example given) and Y – number of subjects per treatment condition per block. In other words, there may be one or more subjects per treatment condition per block so that the actual block size is multiple of a minimum block size (i.e., 8, 16, 24, and so for the example given above).
The second step is, after block size has been determined, to identify all possible combinations of assignment within the block. For instance, if the study is evaluating effects of a drug (group A) or its vehicle (group B), the minimum block size is equal to 2. Thus, there are just two possible treatment allocations within a block: (1) AB and (2) BA. If the block size is equal to 4, there is a greater number of possible treatment allocations: (1) AABB, (2) BBAA, (3) ABAB, (4) BABA, (5) ABBA, and (6) BAAB.
The third step is to randomize these blocks with varying treatment allocations:
Block number | 4 | 3 | 1 | 6 | 5 | 2 |
Random number | 0.015 | 0.379 | 0.392 | 0.444 | 0.720 | 0.901 |
And, finally, the randomized blocks can be used to determine the subjects’ assignment to the groups. In the example above, there are 6 blocks with 4 treatment conditions in each block, but this does not mean that the experiment must include 24 subjects. This random sequence of blocks can be applied to experiments with a total number of subjects smaller or greater than 24. Further, the total number of subjects does not have to be a multiple of 4 (block size) as in the example below with a total of 15 subjects:
Block number | 4 | 3 | 1 | 6 | ||||||||||||
Random number | 0.015 | 0.379 | 0.392 | 0.444 | ||||||||||||
Subject ID | 1 | 2 | 3 | 4 | 5 | 6 | 7 | 8 | 9 | 10 | 11 | 12 | 13 | 14 | 15 | – |
Treatment | B | A | B | A | A | B | A | B | A | A | B | B | B | A | A | – |
It is generally recommended to blind the block size to avoid any potential selection bias. Given the low sample sizes typical for preclinical research, this recommendation becomes a mandatory requirement at least for confirmatory experiments (see chapter “Resolving the Tension Between Exploration and Confirmation in Preclinical Biomedical Research”).
Simple and block randomization are well suited when the main objective is to balance the subjects’ assignment to the treatment groups defined by the independent variables whose impact is to be studied in an experiment. With sample sizes that are large enough, simple and block randomization may also balance the treatment groups in terms of the unknown characteristics of the subjects. However, in many experiments, there are baseline characteristics of the subjects that do get measured and that may have an impact on the dependent (measured) variables (e.g., subjects’ body weight). Potential impact of such characteristics may be addressed by specifying inclusion/exclusion criteria, by including them as covariates into a statistical analysis, and (or) may be minimized by applying stratified randomization schedules.
It is always up to a researcher to decide where there are such potentially impactful covariates that need to be controlled and what is the best way of dealing with them. In case of doubt, the rule of thumb is to avoid any risk, apply stratified randomization, and declare an intention to conduct a statistical analysis that will isolate a potential contribution of the covariate(s).
It is important to acknowledge that, in many cases, information about such covariates may not be available when a study is conceived and designed. Thus, a decision to take covariates into account often affects the timing of getting the randomization conducted. One common example of such a covariate is body weight. A study is planned, and sample size is estimated before the animals are ordered or bred, but the body weights will not be known until the animals are ready. Another example is the size of the tumors that are inoculated and grow at different rates for a pre-specified period of time before the subjects start to receive experimental treatments.
For most situations in preclinical research, an efficient way to conduct stratified randomization is to run simple (or block) randomization several times (e.g., 100 times) and, for each iteration, calculate means for the covariate per each group (e.g., body weights for groups A and B in the example in previous section). The randomization schedule that yields the lowest between-group difference for the covariate would then be chosen for the experiment. Running a large number of iterations does not mean saving excessively large volumes of data. In fact, several tools used to support randomization allow to save the seed for the random number generator and re-create the randomization schedule later using this seed value.
Although stratified randomization is a relatively simple technique that can be of great help, there are some limitations that need to be acknowledged. First, stratified randomization can be extended to two or more stratifying variables. However, given the typically small sample sizes of preclinical studies, it may become complicated to implement if many covariates must be controlled. Second, stratified randomization works only when all subjects have been identified before group assignment. While this is often not a problem in preclinical research, there may be situations when a large study sample is divided into smaller batches that are taken sequentially into the study. In such cases, more sophisticated procedures such as the covariate adaptive randomization may need to be applied similar to what is done in clinical research (Kalish and Begg 1985 ). With this method, subjects are assigned to treatment groups by taking into account the specific covariates and assignments of subjects that have already been allocated to treatment groups. We intentionally do not provide any further examples or guidance on such advanced randomization methods as they should preferably be developed and applied in consultation with or by biostatisticians.
The above discussion on the randomization schedules referred to study designs known as between-subject. A different approach would be required if a study is designed as within-subject. In such study designs also known as the crossover, subjects may be given sequences of treatments with the intent of studying the differences between the effects produced by individual treatments. One should keep in mind that such sequence of testing always bears the danger that the first test might affect the following ones. If there are reasons to expect such interference, within-subjects designs should be avoided.
In the simplest case of a crossover design, there are only two treatments and only two possible sequences to administer these treatments (e.g., A-B and B-A). In nonclinical research and, particularly, in pharmacological studies, there is a strong trend to include at least three doses of a test drug and its vehicle. A Latin square design is commonly used to allocate subjects to treatment conditions. Latin square is a very simple technique, but it is often applied in a way that does not result in a proper randomization (Table 2 ).
In this example, each subject receives each of the four treatments over four consecutive study periods, and, for any given study period, each treatment is equally represented. If there are more than four subjects participating in a study, then the above schedule is copied as many times as need to cover all study subjects.
Despite its apparent convenience (such schedules can be generated without any tools), resulting allocation schedules are predictable and, what is even worse, are not balanced with respect to first-order carry-over effects (e.g., except for the first test period, D comes always after C). Therefore, such Latin square designs are not an example of properly conducted randomization.
One solution would be to create a complete set of orthogonal Latin Squares. For example, when the number of treatments equals three, there are six (i.e., 3!) possible sequences – ABC, ACB, BAC, BCA, CAB, and CBA. If the sample size is a multiple of six, then all six sequences would be applied. As the preclinical studies typically involve small sample sizes, this approach becomes problematic for larger numbers of treatments such as 4, where there are already 24 (i.e., 4!) possible sequences.
The Williams design is a special case of a Latin square where every treatment follows every other treatment the same number of times (Table 3 ).
The Williams design maintains all the advantages of the Latin square but is balanced (see Jones and Kenward 2003 for a detailed discussion on the Williams squares including the generation algorithms). There are six Williams squares possible in case of four treatments. Thus, if there are more than four subjects, more than one Williams square would be applied (e.g., two squares for eight subjects).
Constructing the Williams squares is not a randomization yet. In studies based on within-subject designs, subjects are not randomized to treatment in the same sense as they are in the between-subject design. For a within-subject design, the treatment sequences are randomized. In other words, after the Williams squares are constructed and selected, individual sequences are randomly assigned to the subjects.
The most common and basic method of simple randomization is flipping a coin. For example, with two treatment groups (control versus treatment), the side of the coin (i.e., heads, control; tails, treatment) determines the assignment of each subject. Other similar methods include using a shuffled deck of cards (e.g., even, control; odd, treatment), throwing a dice (e.g., below and equal to 3, control; over 3, treatment), or writing numbers of pieces of paper, folding them, mixing, and then drawing one by one. A random number table found in a statistics book, online random number generators ( random.org or randomizer.org ), or computer-generated random numbers (e.g., using Microsoft Excel) can also be used for simple randomization of subjects. As explained above, simple randomization may result in an unbalanced design, and, therefore, one should pay attention to the number of subjects assigned to each treatment group. But more advanced randomization techniques may require dedicated tools and, whenever possible, should be supported by professional biostatisticians.
Randomization tools are typically included in study design software, and, for in vivo research, the most noteworthy example is the NC3Rs’ Experimental Design Assistant ( www.eda.nc3rs.org.uk ). This freely available online resource allows to generate and share a spreadsheet with the randomized allocation report after the study has been designed (i.e., variables defined, sample size estimated, etc.). Similar functionality may be provided by Electronic Laboratory Notebooks that integrate study design support (see chapter “Electronic Lab Notebooks and Experimental Design Assistants”).
Randomization is certainly supported by many data analysis software packages commonly used in research. In some cases, there is even a free tool that allows to conduct certain types of randomization online (e.g., QuickCalcs at www.graphpad.com/quickcalcs/randMenu/ ).
Someone interested to have a nearly unlimited freedom in designing and executing different types of randomization will benefit from the resources generated by the R community (see https://paasp.net/resource-center/r-scripts/ ). Besides being free and supported by a large community of experts, R allows to save the scripts used to obtain randomization schedules (along with the seed numbers) that makes the overall process not only reproducible and verifiable but also maximally transparent.
Randomization is not and should never be seen as a goal per se. The goal is to minimize the risks of bias that may affect the design, conduct, and analysis of a study and to enable application of other research methods (e.g., certain statistical tests). Randomization is merely a tool to achieve this goal.
If not dictated by the needs of data analysis or the intention to implement blinding, in some cases, pseudo-randomizations such as the schedules described in Tables 1 and 2 may be sufficient. For example, animals delivered by a qualified animal supplier come from large batches where the breeding schemes themselves help to minimize the risk of systematic differences in baseline characteristics. This is in contrast to clinical research where human populations are generally much more heterogeneous than populations of animals typically used in research.
Randomization becomes mandatory in case animals are not received from major suppliers, are bred in-house, are not standard animals (i.e., transgenic), or when they are exposed to an intervention before the initiation of a treatment. Examples of intervention may be surgery, administration of a reagent substance inducing long-term effects, grafts, or infections. In these cases, animals should certainly be randomized after the intervention.
When planning a study, one should also consider the risk of between-subject cross-contamination that may affect the study outcome if animals receiving different treatment(s) are housed within the same cage. In such cases, the most optimal approach is to reduce the number of subjects per cage to a minimum that is acceptable from the animal care and use perspective and adjust the randomization schedule accordingly (i.e., so that all animals in the cage receive the same treatment).
There are situations when randomization becomes impractical or generates other significant risks that outweigh its benefits. In such cases, it is essential to recognize the reasons why randomization is applied (e.g., ability to apply certain statistical tests, prevention of selection bias, and support of blinding). For example, for an in vitro study with multi-well plates, randomization is usually technically possible, but one would need to recognize the risk of errors introduced during manual pipetting into a 96- or 384-well plate. With proper controls and machine-read experimental readout, the risk of bias in such case may not be seen as strong enough to accept the risk of a human error.
Another common example is provided by studies where incremental drug doses or concentrations are applied during the course of a single experiment involving just one subject. During cardiovascular safety studies, animals receive first an infusion of a vehicle (e.g., over a period of 30 min), followed by the two or three concentrations of the test drug, and the hemodynamics is being assessed along with the blood samples taken. As the goal of such studies is to establish concentration-effect relationships, one has no choice but to accept the lack of randomization. The only alternatives would be to give up on the within-subject design or conduct the study over many days to allow enough time to wash the drug out between the test days. Needless to say, neither of these options is perfect for a study where the baseline characteristics are a critical factor in keeping the sample size low. In this example, the desire to conduct a properly randomized study comes into a conflict with ethical considerations.
A similar design is often used in electrophysiological experiments (in vitro or ex vivo) where a test system needs to be equilibrated and baselined for extended periods of time (sometimes hours) to allow subsequent application of test drugs (at ascending concentrations). Because a washout cannot be easily controlled, such studies also do not follow randomized schedules of testing various drug doses.
The low-throughput studies such as in electrophysiology typically go over many days, and every day there is a small number of subjects or data points added. While one may accept the studies being not randomized in some cases, it is important to stress that there should be other measures in place that control potential sources of bias. It is a common but usually unacceptable practice to analyze the results each time a new data point has been added in order to decide whether a magic P value sank below 0.05 and the experiment can stop. For example, in one recent publication, it was stated: “For optogenetic activation experiments, cell-type-specific ablation experiments, and in vivo recordings (optrode recordings and calcium imaging), we continuously increased the number of animals until statistical significance was reached to support our conclusions.” Such an approach should be avoided by clear experimental planning and definition of study endpoints.
The above examples are provided only to illustrate that there may be special cases when randomization may not be done. This is usually not an easy decision to make and even more difficult to defend later. Therefore, one should always be advised to seek a professional advice (i.e., interaction with the biostatisticians or colleagues specializing in the risk assessment and study design issues). Needless to say, this advice should be obtained before the studies are conducted.
In the ideal case, once the randomization was applied to allocate subjects to treatment conditions, the randomization should be maintained through the study conduct and analysis to control against potential performance and outcome detection bias, respectively. In other words, it would not be appropriate first to assign the subjects, for example, to groups A and B and then do all experimental manipulations first with the group A and then with the group B.
In clinical research, blinding and randomization are recognized as the most important design techniques for avoiding bias (ICH Harmonised Tripartite Guideline 1998 ; see also chapter “Learning from Principles of Evidence-Based Medicine to Optimize Nonclinical Research Practices”). In the preclinical domain, there is a number of instruments assessing risks of bias, and the criteria most often included are randomization and blinding (83% and 77% of a total number of 30 instruments analyzed, Krauth et al. 2013 ).
While randomization and blinding are often discussed together and serve highly overlapping objectives, attitude towards these two research rigor measures is strikingly different. The reason for a higher acceptance of randomization compared to blinding is obvious – randomization can be implemented essentially at no cost, while blinding requires at least some investment of resources and may therefore have a negative impact on the research unit’s apparent capacity (measured by the number of completed studies, irrespective of quality).
Since the costs and resources are not an acceptable argument in discussions on ethical conduct of research, we often engage a defense mechanism, called rationalization, that helps to justify and explain why blinding should not be applied and do so in a seemingly rational or logical manner to avoid the true explanation. Arguments against the use of blinding can be divided into two groups.
One group comprises a range of factors that are essentially psychological barriers that can be effectively addressed. For example, one may believe that his/her research area or a specific research method has an innate immunity against any risk of bias. Or, alternatively, one may believe that his/her scientific excellence and the ability to supervise the activities in the lab make blinding unnecessary. There is a great example that can be used to illustrate that there is no place for beliefs and one should rather rely on empirical evidence. For decades, compared to male musicians, females have been underrepresented in major symphonic orchestras despite having equal access to high-quality education. The situation started to change in the mid-1970s when blind auditions were introduced and the proportion of female orchestrants went up (Goldin and Rouse 2000 ). In preclinical research, there are also examples of the impact of blinding (or a lack thereof). More specifically, there were studies that reveal substantially higher effect sizes reported in the experiments that were not randomized or blinded (Macleod et al. 2008 ).
Another potential barrier is related to the “trust” within the lab. Bench scientists need to be explained what the purpose of blinding is and, in the ideal case, be actively involved in development and implementation of blinding and other research rigor measures. With the proper explanation and engagement, blinding will not be seen as an unfriendly act whereby a PI or a lab head communicates a lack of trust.
The second group of arguments against the use of blinding is actually composed of legitimate questions that need to be addressed when designing an experiment. As mentioned above in the section on randomization, a decision to apply blinding should be justified by the needs of a specific experiment and correctly balanced against the existing and potential risks.
It requires no explanation that, in preclinical research, there are no double-blinded studies in a sense of how it is meant in the clinic. However, similar to clinical research, blinding in preclinical experiments serves to protect against two potential sources of bias: bias related to blinding of personnel involved in study conduct including application of treatments (performance bias) and bias related to blinding of personnel involved in the outcome assessment (detection bias).
Analysis of the risks of bias in a particular research environment or for a specific experiment allows to decide which type of blinding should be applied and whether blinding is an appropriate measure against the risks.
There are three types or levels of blinding, and each one of them has its use: assumed blinding, partial blinding, and full blinding. With each type of blinding, experimenters allocate subjects to groups, replace the group names with blind codes, save the coding information in a secure place, and do not access this information until a certain pre-defined time point (e.g., until the data are collected or the study is completed and analyzed).
In the assumed blinding, experimenters have access to the group or treatment codes at all times, but they do not know the correspondence between group and treatment before the end of the study. With the partial or full blinding, experimenters do not have access to the coding information until a certain pre-defined time point.
Main advantage of the assumed blinding is that an experiment can be conducted by one person who plans, performs, and analyzes the study. The risk of bias may be relatively low if the experiments are routine – e.g., lead optimization research in drug discovery or fee-for-service studies conducted using well-established standardized methods.
Efficiency of assumed blinding is enhanced if there is a sufficient time gap between application of a treatment and the outcome recording/assessment. It is also usually helpful if the access to the blinding codes is intentionally made more difficult (e.g., blinding codes are kept in the study design assistant or in a file on an office computer that is not too close to the lab where the outcomes will be recorded).
If introduced properly, assumed blinding can guard against certain unwanted practices such as remeasurement, removal, and reclassification of individual observations or data points (three evil Rs according to Shun-Shin and Francis 2013 ). In preclinical studies with small sample sizes, such practices have particularly deleterious consequences. In some cases, remeasurement even of a single subject may skew the results in a direction suggested by the knowledge of group allocation. One should emphasize that blinding is not necessarily an instrument against the remeasurement (it is often needed or unavoidable) but rather helps to avoid risks associated with it.
There are various situations where blinding (with no access to the blinding codes) is implemented not for the entire experiment but only for a certain part of it, e.g.:
No blinding during the application of experimental treatment (e.g., injection of a test drug) but proper blinding during the data collection and analysis
No blinding during the conduct of an experiment but proper blinding during analysis
For example, in behavioral pharmacology, there are experiments where subjects’ behavior is video recorded after a test drug is applied. In such cases, blinding is applied to analysis of the video recordings but not the drug application phase. Needless to say, blinded analysis has typically to be performed by someone who was not involved in the drug application phase.
A decision to apply partial blinding is based on (a) the confidence that the risks of bias are properly controlled during the unblinded parts of the experiment and/or (b) rationale assessment of the risks associated with maintaining blinding throughout the experiment. As an illustration of such decision-making process, one may imagine a study where the experiment is conducted in a small lab (two or three people) by adequately trained personnel that is not under pressure to deliver results of a certain pattern, data collection is automatic, and data integrity is maintained at every step. Supported by various risk reduction measures, such an experiment may deliver robust and reliable data even if not fully blinded.
Importantly, while partial blinding can adequately limit the risk of some forms of bias, it may be less effective against the performance bias.
For important decision-enabling studies (including confirmatory research, see chapter “Resolving the Tension Between Exploration and Confirmation in Preclinical Biomedical Research”), it is usually preferable to implement full blinding rather than to explain why it was not done and argue that all the risks were properly controlled.
It is particularly advisable to follow full blinding in the experiments that are for some reasons difficult to repeat. For example, these could be studies running over significant periods of time (e.g., many months) or studies using unique resources or studies that may not be repeated for ethical reasons. In such cases, it is more rational to apply full blinding rather than leave a chance that the results will be questioned on the ground of lacking research rigor.
As implied by the name, full blinding requires complete allocation concealment from the beginning until the end of the experiment. This requirement may translate into substantial costs of resources. In the ideal scenario, each study should be supported by at least three independent people responsible for:
(De)coding, randomization
Conduct of the experiment such as handling of the subjects and application of test drugs (outcome recording and assessment)
(Outcome recording and assessment), final analysis
The main reason for separating conduct of the experiment and the final analysis is to protect against potential unintended unblinding (see below). If there is no risk of unblinding or it is not possible to have three independent people to support the blinding of an experiment, one may consider a single person responsible for every step from the conduct of the experiment to the final analysis. In other words, the study would be supported by two independent people responsible for:
Conduct of the experiment such as handling of the subjects and application of test drugs, outcome recording and assessment, and final analysis
Successful blinding is related to adequate randomization. This does not mean that they should always be performed in this sequence: first randomization and then blinding. In fact, the order may be reversed. For example, one may work with an offspring of the female rats that received experimental and control treatments while pregnant. As the litter size may differ substantially between the dams, randomization may be conducted after the pups are born, and this does not require allocation concealment to be broken.
The blinding procedure has to be carefully thought through. There are several factors that are listed below and that can turn a well-minded intention into a waste of resources.
First, blinding should as far as possible cover the entire experimental setup – i.e., all groups and subjects. There is an unacceptable practice to exclude positive controls from blinding that is often not justified by anything other than an intention to introduce a detection bias in order to reduce the risk of running an invalid experiment (i.e., an experiment where a positive control failed).
In some cases, positive controls cannot be administered by the same route or using the same pretreatment time as other groups. Typically, such a situation would require a separate negative (vehicle) control treated in the same way as the positive control group. Thus, the study is only partially blinded as the experimenter is able to identify the groups needed to “validate” the study (negative control and positive control groups) but remains blind to the exact nature of the treatment received by each of these two groups. For a better control over the risk of unblinding, one may apply a “double-dummy” approach where all animals receive the same number of administrations via the same routes and pretreatment times.
Second, experiments may be unintentionally unblinded. For example, drugs may have specific, easy to observe physicochemical characteristics, or drug treatments may change the appearance of the subjects or produce obvious adverse effects. Perhaps, even more common is the unblinding due to the differences in the appearance of the drug solution or suspension dependent on the concentration. In such cases, there is not much that can be done but it is essential to take corresponding notes and acknowledge in the study report or publication. It is interesting to note that the unblinding is often cited as an argument against the use of blinding (Fitzpatrick et al. 2018 ); however, this argument reveals another problem – partial blinding schemes are often applied as a normative response without any proper risk of bias assessment.
Third, blinding codes should be kept in a secure place avoiding any risk that the codes are lost. For in vivo experiments, this is an ethical requirement as the study will be wasted if it cannot be unblinded at the end.
Fourth, blinding can significantly increase the risk of mistakes. A particular situation that one should be prepared to avoid is related to lack of accessibility of blinding codes in case of emergency. There are situations when a scientist conducting a study falls ill and the treatment schedules or outcome assessment protocols are not available or a drug treatment is causing disturbing adverse effects and attending veterinarians or caregivers call for a decision in the absence of a scientist responsible for a study. It usually helps to make the right decision if it is known that an adverse effect is observed in a treatment group where it can be expected. Such situations should be foreseen and appropriate guidance made available to anyone directly or indirectly involved in an experiment. A proper study design should define a backup person with access to the blinding codes and include clear definition of endpoints.
Several practical tips can help to reduce the risk of human-made mistakes. For example, the study conduct can be greatly facilitated if each treatment group is assigned its own color. Then, this color coding would be applied to vials with the test drugs, syringes used to apply the drug, and the subjects (e.g., apply solution from a green-labeled vial using a green-labeled syringe to an animal from a green-labeled cage or with a green mark on its tail). When following such practice, one should not forget to randomly assign color codes to treatment conditions. Otherwise, for example, yellow color is always used for vehicle control, green for the lowest dose, and so forth.
To sum up, it is not always lacking resources that make full blinding not possible to apply. Further, similar to what was described above for randomization, there are clear exception cases where application of blinding is made problematic by the very nature of the experiment itself.
Most, if not all, guidelines, recommendations, and other texts on Good Research Practice emphasize the importance of blinding and randomization (chapters “Guidelines and Initiatives for Good Research Practice”, and “General Principles of Preclinical Study Design”). There is, however, very limited specific guidance on when and how to apply blinding and randomization. The present chapter aims to close this gap.
Generally speaking, experiments should be blinded and randomized if:
This is a confirmatory research (see chapter “Resolving the Tension Between Exploration and Confirmation in Preclinical Biomedical Research”) that has a major impact on decision-making and that cannot be readily repeated (for ethical or resource-related reasons).
No other measures can be applied to protect against existing and potential risks of bias.
There are various sources of bias that affect the outcome of experimental studies and these sources are unique and specific to each research unit. There is usually no one who knows these risks better than the scientists working in the research unit, and it is always up to the scientist to decide if, when, and how blinding and randomization should be implemented. However, there are several recommendations that can help to decide and act in the most effective way:
Conduct a risk assessment for your research environment, and, if you do not know how to do that, ask for a professional support or advice.
Involve your team in developing and implementing the blinding/randomization protocols, and seek the team members’ feedback regarding the performance of these protocols (and revise them, as needed).
Provide training not only on how to administer blinding and randomization but also to preempt any questions related to the rationale behind these measures (i.e., experiments are blinded not because of the suspected misconduct or lack of trust).
Describe blinding and randomization procedures in dedicated protocols with as many details as possible (including emergency plans and accident reporting, as discussed above).
Ensure maximal transparency when reporting blinding and randomization (e.g., in a publication). When deciding to apply blinding and randomization, be maximally clear about the details (Table 4 ). When deciding against, be open about the reasons for such decision. Transparency is also essential when conducting multi-laboratory collaborative projects or when a study is outsourced to another laboratory. To avoid any misunderstanding, collaborators should specify expectations and reach alignment on study design prior to the experiment and communicate all important details in study reports.
Blinding and randomization should always be a part of a more general effort to introduce and maintain research rigor. Just as the randomization increases the likelihood that blinding will not be omitted (van der Worp et al. 2010 ), other Good Research Practices such as proper documentation are also highly instrumental in making blinding and randomization effective.
To conclude, blinding and randomization may be associated with some effort and additional costs, but, under all circumstances, a decision to apply these research rigor techniques should not be based on general statements and arguments by those who do not want to leave their comfort zone. Instead, the decision should be based on the applicable risk assessment and careful review of potential implementation burden. In many cases, this leads to a relieving discovery that the devil is not so black as he is painted.
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The authors would like to thank Dr. Thomas Steckler (Janssen), Dr. Kim Wever (Radboud University), and Dr. Jan Vollert (Imperial College London) for reading the earlier version of the manuscript and providing comments and suggestions.
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Bespalov, A., Wicke, K., Castagné, V. (2019). Blinding and Randomization. In: Bespalov, A., Michel, M., Steckler, T. (eds) Good Research Practice in Non-Clinical Pharmacology and Biomedicine. Handbook of Experimental Pharmacology, vol 257. Springer, Cham. https://doi.org/10.1007/164_2019_279
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Minsoo kang.
1 Middle Tennessee State University, Murfreesboro, TN
2 University of Northern Iowa, Cedar Falls, IA
3 Korea National Sport University, Seoul, Korea
To review and describe randomization techniques used in clinical trials, including simple, block, stratified, and covariate adaptive techniques.
Clinical trials are required to establish treatment efficacy of many athletic training procedures. In the past, we have relied on evidence of questionable scientific merit to aid the determination of treatment choices. Interest in evidence-based practice is growing rapidly within the athletic training profession, placing greater emphasis on the importance of well-conducted clinical trials. One critical component of clinical trials that strengthens results is random assignment of participants to control and treatment groups. Although randomization appears to be a simple concept, issues of balancing sample sizes and controlling the influence of covariates a priori are important. Various techniques have been developed to account for these issues, including block, stratified randomization, and covariate adaptive techniques.
Athletic training researchers and scholarly clinicians can use the information presented in this article to better conduct and interpret the results of clinical trials. Implementing these techniques will increase the power and validity of findings of athletic medicine clinical trials, which will ultimately improve the quality of care provided.
Outcomes research is critical in the evidence-based health care environment because it addresses scientific questions concerning the efficacy of treatments. Clinical trials are considered the “gold standard” for outcomes in biomedical research. In athletic training, calls for more evidence-based medical research, specifically clinical trials, have been issued. 1 , 2
The strength of clinical trials is their superior ability to measure change over time from a treatment. Treatment differences identified from cross-sectional observational designs rather than experimental clinical trials have methodologic weaknesses, including confounding, cohort effects, and selection bias. 3 For example, using a nonrandomized trial to examine the effectiveness of prophylactic knee bracing to prevent medial collateral ligament injuries may suffer from confounders and jeopardize the results. One possible confounder is a history of knee injuries. Participants with a history of knee injuries may be more likely to wear braces than those with no such history. Participants with a history of injury are more likely to suffer additional knee injuries, unbalancing the groups and influencing the results of the study.
The primary goal of comparative clinical trials is to provide comparisons of treatments with maximum precision and validity. 4 One critical component of clinical trials is random assignment of participants into groups. Randomizing participants helps remove the effect of extraneous variables (eg, age, injury history) and minimizes bias associated with treatment assignment. Randomization is considered by most researchers to be the optimal approach for participant assignment in clinical trials because it strengthens the results and data interpretation. 4 – , 9
One potential problem with small clinical trials (n < 100) 7 is that conventional simple randomization methods, such as flipping a coin, may result in imbalanced sample size and baseline characteristics (ie, covariates) among treatment and control groups. 9 , 10 This imbalance of baseline characteristics can influence the comparison between treatment and control groups and introduce potential confounding factors. Many procedures have been proposed for random group assignment of participants in clinical trials. 11 Simple, block, stratified, and covariate adaptive randomizations are some examples. Each technique has advantages and disadvantages, which must be carefully considered before a method is selected. Our purpose is to introduce the concept and significance of randomization and to review several conventional and relatively new randomization techniques to aid in the design and implementation of valid clinical trials.
Randomization is the process of assigning participants to treatment and control groups, assuming that each participant has an equal chance of being assigned to any group. 12 Randomization has evolved into a fundamental aspect of scientific research methodology. Demands have increased for more randomized clinical trials in many areas of biomedical research, such as athletic training. 2 , 13 In fact, in the last 2 decades, internationally recognized major medical journals, such as the Journal of the American Medical Association and the BMJ , have been increasingly interested in publishing studies reporting results from randomized controlled trials. 5
Since Fisher 14 first introduced the idea of randomization in a 1926 agricultural study, the academic community has deemed randomization an essential tool for unbiased comparisons of treatment groups. Five years after Fisher's introductory paper, the first randomized clinical trial involving tuberculosis was conducted. 15 A total of 24 participants were paired (ie, 12 comparable pairs), and by a flip of a coin, each participant within the pair was assigned to either the control or treatment group. By employing randomization, researchers offer each participant an equal chance of being assigned to groups, which makes the groups comparable on the dependent variable by eliminating potential bias. Indeed, randomization of treatments in clinical trials is the only means of avoiding systematic characteristic bias of participants assigned to different treatments. Although randomization may be accomplished with a simple coin toss, more appropriate and better methods are often needed, especially in small clinical trials. These other methods will be discussed in this review.
Researchers demand randomization for several reasons. First, participants in various groups should not differ in any systematic way. In a clinical trial, if treatment groups are systematically different, trial results will be biased. Suppose that participants are assigned to control and treatment groups in a study examining the efficacy of a walking intervention. If a greater proportion of older adults is assigned to the treatment group, then the outcome of the walking intervention may be influenced by this imbalance. The effects of the treatment would be indistinguishable from the influence of the imbalance of covariates, thereby requiring the researcher to control for the covariates in the analysis to obtain an unbiased result. 16
Second, proper randomization ensures no a priori knowledge of group assignment (ie, allocation concealment). That is, researchers, participants, and others should not know to which group the participant will be assigned. Knowledge of group assignment creates a layer of potential selection bias that may taint the data. Schulz and Grimes 17 stated that trials with inadequate or unclear randomization tended to overestimate treatment effects up to 40% compared with those that used proper randomization. The outcome of the trial can be negatively influenced by this inadequate randomization.
Statistical techniques such as analysis of covariance (ANCOVA), multivariate ANCOVA, or both, are often used to adjust for covariate imbalance in the analysis stage of the clinical trial. However, the interpretation of this postadjustment approach is often difficult because imbalance of covariates frequently leads to unanticipated interaction effects, such as unequal slopes among subgroups of covariates. 18 , 19 One of the critical assumptions in ANCOVA is that the slopes of regression lines are the same for each group of covariates (ie, homogeneity of regression slopes). The adjustment needed for each covariate group may vary, which is problematic because ANCOVA uses the average slope across the groups to adjust the outcome variable. Thus, the ideal way of balancing covariates among groups is to apply sound randomization in the design stage of a clinical trial (before the adjustment procedure) instead of after data collection. In such instances, random assignment is necessary and guarantees validity for statistical tests of significance that are used to compare treatments.
Many procedures have been proposed for the random assignment of participants to treatment groups in clinical trials. In this article, common randomization techniques, including simple randomization, block randomization, stratified randomization, and covariate adaptive randomization, are reviewed. Each method is described along with its advantages and disadvantages. It is very important to select a method that will produce interpretable, valid results for your study.
Randomization based on a single sequence of random assignments is known as simple randomization. 10 This technique maintains complete randomness of the assignment of a person to a particular group. The most common and basic method of simple randomization is flipping a coin. For example, with 2 treatment groups (control versus treatment), the side of the coin (ie, heads = control, tails = treatment) determines the assignment of each participant. Other methods include using a shuffled deck of cards (eg, even = control, odd = treatment) or throwing a die (eg, below and equal to 3 = control, over 3 = treatment). A random number table found in a statistics book or computer-generated random numbers can also be used for simple randomization of participants.
This randomization approach is simple and easy to implement in a clinical trial. In large trials (n > 200), simple randomization can be trusted to generate similar numbers of participants among groups. However, randomization results could be problematic in relatively small sample size clinical trials (n < 100), resulting in an unequal number of participants among groups. For example, using a coin toss with a small sample size (n = 10) may result in an imbalance such that 7 participants are assigned to the control group and 3 to the treatment group ( Figure 1 ).
The block randomization method is designed to randomize participants into groups that result in equal sample sizes. This method is used to ensure a balance in sample size across groups over time. Blocks are small and balanced with predetermined group assignments, which keeps the numbers of participants in each group similar at all times. According to Altman and Bland, 10 the block size is determined by the researcher and should be a multiple of the number of groups (ie, with 2 treatment groups, block size of either 4 or 6). Blocks are best used in smaller increments as researchers can more easily control balance. 7 After block size has been determined, all possible balanced combinations of assignment within the block (ie, equal number for all groups within the block) must be calculated. Blocks are then randomly chosen to determine the participants' assignment into the groups.
For a clinical trial with control and treatment groups involving 40 participants, a randomized block procedure would be as follows: (1) a block size of 4 is chosen, (2) possible balanced combinations with 2 C (control) and 2 T (treatment) subjects are calculated as 6 (TTCC, TCTC, TCCT, CTTC, CTCT, CCTT), and (3) blocks are randomly chosen to determine the assignment of all 40 participants (eg, one random sequence would be [TTCC / TCCT / CTTC / CTTC / TCCT / CCTT / TTCC / TCTC / CTCT / TCTC]). This procedure results in 20 participants in both the control and treatment groups ( Figure 2 ).
Although balance in sample size may be achieved with this method, groups may be generated that are rarely comparable in terms of certain covariates. 6 For example, one group may have more participants with secondary diseases (eg, diabetes, multiple sclerosis, cancer) that could confound the data and may negatively influence the results of the clinical trial. Pocock and Simon 11 stressed the importance of controlling for these covariates because of serious consequences to the interpretation of the results. Such an imbalance could introduce bias in the statistical analysis and reduce the power of the study. 4 , 6 , 8 Hence, sample size and covariates must be balanced in small clinical trials.
The stratified randomization method addresses the need to control and balance the influence of covariates. This method can be used to achieve balance among groups in terms of participants' baseline characteristics (covariates). Specific covariates must be identified by the researcher who understands the potential influence each covariate has on the dependent variable. Stratified randomization is achieved by generating a separate block for each combination of covariates, and participants are assigned to the appropriate block of covariates. After all participants have been identified and assigned into blocks, simple randomization occurs within each block to assign participants to one of the groups.
The stratified randomization method controls for the possible influence of covariates that would jeopardize the conclusions of the clinical trial. For example, a clinical trial of different rehabilitation techniques after a surgical procedure will have a number of covariates. It is well known that the age of the patient affects the rate of healing. Thus, age could be a confounding variable and influence the outcome of the clinical trial. Stratified randomization can balance the control and treatment groups for age or other identified covariates.
For example, with 2 groups involving 40 participants, the stratified randomization method might be used to control the covariates of sex (2 levels: male, female) and body mass index (3 levels: underweight, normal, overweight) between study arms. With these 2 covariates, possible block combinations total 6 (eg, male, underweight). A simple randomization procedure, such as flipping a coin, is used to assign the participants within each block to one of the treatment groups ( Figure 3 ).
Although stratified randomization is a relatively simple and useful technique, especially for smaller clinical trials, it becomes complicated to implement if many covariates must be controlled. 20 For example, too many block combinations may lead to imbalances in overall treatment allocations because a large number of blocks can generate small participant numbers within the block. Therneau 21 purported that a balance in covariates begins to fail when the number of blocks approaches half the sample size. If another 4-level covariate was added to the example, the number of block combinations would increase from 6 to 24 (2 × 3 × 4), for an average of fewer than 2 (40 / 24 = 1.7) participants per block, reducing the usefulness of the procedure to balance the covariates and jeopardizing the validity of the clinical trial. In small studies, it may not be feasible to stratify more than 1 or 2 covariates because the number of blocks can quickly approach the number of participants. 10
Stratified randomization has another limitation: it works only when all participants have been identified before group assignment. This method is rarely applicable, however, because clinical trial participants are often enrolled one at a time on a continuous basis. When baseline characteristics of all participants are not available before assignment, using stratified randomization is difficult. 7
Covariate adaptive randomization has been recommended by many researchers as a valid alternative randomization method for clinical trials. 9 , 22 In covariate adaptive randomization, a new participant is sequentially assigned to a particular treatment group by taking into account the specific covariates and previous assignments of participants. 9 , 12 , 18 , 23 , 24 Covariate adaptive randomization uses the method of minimization by assessing the imbalance of sample size among several covariates. This covariate adaptive approach was first described by Taves. 23
The Taves covariate adaptive randomization method allows for the examination of previous participant group assignments to make a case-by-case decision on group assignment for each individual who enrolls in the study. Consider again the example of 2 groups involving 40 participants, with sex (2 levels: male, female) and body mass index (3 levels: underweight, normal, overweight) as covariates. Assume the first 9 participants have already been randomly assigned to groups by flipping a coin. The 9 participants' group assignments are broken down by covariate level in Figure 4 . Now the 10th participant, who is male and underweight, needs to be assigned to a group (ie, control versus treatment). Based on the characteristics of the 10th participant, the Taves method adds marginal totals of the corresponding covariate categories for each group and compares the totals. The participant is assigned to the group with the lower covariate total to minimize imbalance. In this example, the appropriate categories are male and underweight, which results in the total of 3 (2 for male category + 1 for underweight category) for the control group and a total of 5 (3 for male category + 2 for underweight category) for the treatment group. Because the sum of marginal totals is lower for the control group (3 < 5), the 10th participant is assigned to the control group ( Figure 5 ).
The Pocock and Simon method 11 of covariate adaptive randomization is similar to the method Taves 23 described. The difference in this approach is the temporary assignment of participants to both groups. This method uses the absolute difference between groups to determine group assignment. To minimize imbalance, the participant is assigned to the group determined by the lowest sum of the absolute differences among the covariates between the groups. For example, using the previous situation in assigning the 10th participant to a group, the Pocock and Simon method would (1) assign the 10th participant temporarily to the control group, resulting in marginal totals of 3 for male category and 2 for underweight category; (2) calculate the absolute difference between control and treatment group (males: 3 control – 3 treatment = 0; underweight: 2 control – 2 treatment = 0) and sum (0 + 0 = 0); (3) temporarily assign the 10th participant to the treatment group, resulting in marginal totals of 4 for male category and 3 for underweight category; (4) calculate the absolute difference between control and treatment group (males: 2 control – 4 treatment = 2; underweight: 1 control – 3 treatment = 2) and sum (2 + 2 = 4); and (5) assign the 10th participant to the control group because of the lowest sum of absolute differences (0 < 4).
Pocock and Simon 11 also suggested using a variance approach. Instead of calculating absolute difference among groups, this approach calculates the variance among treatment groups. Although the variance method performs similarly to the absolute difference method, both approaches suffer from the limitation of handling only categorical covariates. 25
Frane 18 introduced a covariate adaptive randomization for both continuous and categorical types. Frane used P values to identify imbalance among treatment groups: a smaller P value represents more imbalance among treatment groups.
The Frane method for assigning participants to either the control or treatment group would include (1) temporarily assigning the participant to both the control and treatment groups; (2) calculating P values for each of the covariates using a t test and analysis of variance (ANOVA) for continuous variables and goodness-of-fit χ 2 test for categorical variables; (3) determining the minimum P value for each control or treatment group, which indicates more imbalance among treatment groups; and (4) assigning the participant to the group with the larger minimum P value (ie, try to avoid more imbalance in groups).
Going back to the previous example of assigning the 10th participant (male and underweight) to a group, the Frane method would result in the assignment to the control group. The steps used to make this decision were calculating P values for each of the covariates using the χ 2 goodness-of-fit test represented in the Table . The t tests and ANOVAs were not used because the covariates in this example were categorical. Based on the Table , the lowest minimum P values were 1.0 for the control group and 0.317 for the treatment group. The 10th participant was assigned to the control group because of the higher minimum P value, which indicates better balance in the control group (1.0 > 0.317).
Probabilities From χ 2 Goodness-of-Fit Tests for the Example Shown in Figure 5 (Frane 18 Method)
Covariate adaptive randomization produces less imbalance than other conventional randomization methods and can be used successfully to balance important covariates among control and treatment groups. 6 Although the balance of covariates among groups using the stratified randomization method begins to fail when the number of blocks approaches half the sample size, covariate adaptive randomization can better handle the problem of increasing numbers of covariates (ie, increased block combinations). 9
One concern of these covariate adaptive randomization methods is that treatment assignments sometimes become highly predictable. Investigators using covariate adaptive randomization sometimes come to believe that group assignment for the next participant can be readily predicted, going against the basic concept of randomization. 12 , 26 , 27 This predictability stems from the ongoing assignment of participants to groups wherein the current allocation of participants may suggest future participant group assignment. In their review, Scott et al 9 argued that this predictability is also true of other methods, including stratified randomization, and it should not be overly penalized. Zielhuis et al 28 and Frane 18 suggested a practical approach to prevent predictability: a small number of participants should be randomly assigned into the groups before the covariate adaptive randomization technique being applied.
The complicated computation process of covariate adaptive randomization increases the administrative burden, thereby limiting its use in practice. A user-friendly computer program for covariate adaptive randomization is available (free of charge) upon request from the authors (M.K., B.G.R., or J.H.P.). 29
Our purpose was to introduce randomization, including its concept and significance, and to review several randomization techniques to guide athletic training researchers and practitioners to better design their randomized clinical trials. Many factors can affect the results of clinical research, but randomization is considered the gold standard in most clinical trials. It eliminates selection bias, ensures balance of sample size and baseline characteristics, and is an important step in guaranteeing the validity of statistical tests of significance used to compare treatment groups.
Before choosing a randomization method, several factors need to be considered, including the size of the clinical trial; the need for balance in sample size, covariates, or both; and participant enrollment. 16 Figure 6 depicts a flowchart designed to help select an appropriate randomization technique. For example, a power analysis for a clinical trial of different rehabilitation techniques after a surgical procedure indicated a sample size of 80. A well-known covariate for this study is age, which must be balanced among groups. Because of the nature of the study with postsurgical patients, participant recruitment and enrollment will be continuous. Using the flowchart, the appropriate randomization technique is covariate adaptive randomization technique.
Simple randomization works well for a large trial (eg, n > 200) but not for a small trial (n < 100). 7 To achieve balance in sample size, block randomization is desirable. To achieve balance in baseline characteristics, stratified randomization is widely used. Covariate adaptive randomization, however, can achieve better balance than other randomization methods and can be successfully used for clinical trials in an effective manner.
This study was partially supported by a Faculty Grant (FRCAC) from the College of Graduate Studies, at Middle Tennessee State University, Murfreesboro, TN.
Minsoo Kang, PhD; Brian G. Ragan, PhD, ATC; and Jae-Hyeon Park, PhD, contributed to conception and design; acquisition and analysis and interpretation of the data; and drafting, critical revision, and final approval of the article.
Since school days’ students perform scientific experiments that provide results that define and prove the laws and theorems in science. These experiments are laid on a strong foundation of experimental research designs.
An experimental research design helps researchers execute their research objectives with more clarity and transparency.
In this article, we will not only discuss the key aspects of experimental research designs but also the issues to avoid and problems to resolve while designing your research study.
Table of Contents
Experimental research design is a framework of protocols and procedures created to conduct experimental research with a scientific approach using two sets of variables. Herein, the first set of variables acts as a constant, used to measure the differences of the second set. The best example of experimental research methods is quantitative research .
Experimental research helps a researcher gather the necessary data for making better research decisions and determining the facts of a research study.
A researcher can conduct experimental research in the following situations —
To publish significant results, choosing a quality research design forms the foundation to build the research study. Moreover, effective research design helps establish quality decision-making procedures, structures the research to lead to easier data analysis, and addresses the main research question. Therefore, it is essential to cater undivided attention and time to create an experimental research design before beginning the practical experiment.
By creating a research design, a researcher is also giving oneself time to organize the research, set up relevant boundaries for the study, and increase the reliability of the results. Through all these efforts, one could also avoid inconclusive results. If any part of the research design is flawed, it will reflect on the quality of the results derived.
Based on the methods used to collect data in experimental studies, the experimental research designs are of three primary types:
A research study could conduct pre-experimental research design when a group or many groups are under observation after implementing factors of cause and effect of the research. The pre-experimental design will help researchers understand whether further investigation is necessary for the groups under observation.
Pre-experimental research is of three types —
A true experimental research design relies on statistical analysis to prove or disprove a researcher’s hypothesis. It is one of the most accurate forms of research because it provides specific scientific evidence. Furthermore, out of all the types of experimental designs, only a true experimental design can establish a cause-effect relationship within a group. However, in a true experiment, a researcher must satisfy these three factors —
This type of experimental research is commonly observed in the physical sciences.
The word “Quasi” means similarity. A quasi-experimental design is similar to a true experimental design. However, the difference between the two is the assignment of the control group. In this research design, an independent variable is manipulated, but the participants of a group are not randomly assigned. This type of research design is used in field settings where random assignment is either irrelevant or not required.
The classification of the research subjects, conditions, or groups determines the type of research design to be used.
Experimental research allows you to test your idea in a controlled environment before taking the research to clinical trials. Moreover, it provides the best method to test your theory because of the following advantages:
There is no order to this list, and any one of these issues can seriously compromise the quality of your research. You could refer to the list as a checklist of what to avoid while designing your research.
Usually, researchers miss out on checking if their hypothesis is logical to be tested. If your research design does not have basic assumptions or postulates, then it is fundamentally flawed and you need to rework on your research framework.
Without a comprehensive research literature review , it is difficult to identify and fill the knowledge and information gaps. Furthermore, you need to clearly state how your research will contribute to the research field, either by adding value to the pertinent literature or challenging previous findings and assumptions.
Statistical results are one of the most trusted scientific evidence. The ultimate goal of a research experiment is to gain valid and sustainable evidence. Therefore, incorrect statistical analysis could affect the quality of any quantitative research.
This is one of the most basic aspects of research design. The research problem statement must be clear and to do that, you must set the framework for the development of research questions that address the core problems.
Every study has some type of limitations . You should anticipate and incorporate those limitations into your conclusion, as well as the basic research design. Include a statement in your manuscript about any perceived limitations, and how you considered them while designing your experiment and drawing the conclusion.
The most important yet less talked about topic is the ethical issue. Your research design must include ways to minimize any risk for your participants and also address the research problem or question at hand. If you cannot manage the ethical norms along with your research study, your research objectives and validity could be questioned.
In an experimental design, a researcher gathers plant samples and then randomly assigns half the samples to photosynthesize in sunlight and the other half to be kept in a dark box without sunlight, while controlling all the other variables (nutrients, water, soil, etc.)
By comparing their outcomes in biochemical tests, the researcher can confirm that the changes in the plants were due to the sunlight and not the other variables.
Experimental research is often the final form of a study conducted in the research process which is considered to provide conclusive and specific results. But it is not meant for every research. It involves a lot of resources, time, and money and is not easy to conduct, unless a foundation of research is built. Yet it is widely used in research institutes and commercial industries, for its most conclusive results in the scientific approach.
Have you worked on research designs? How was your experience creating an experimental design? What difficulties did you face? Do write to us or comment below and share your insights on experimental research designs!
Randomization is important in an experimental research because it ensures unbiased results of the experiment. It also measures the cause-effect relationship on a particular group of interest.
Experimental research design lay the foundation of a research and structures the research to establish quality decision making process.
There are 3 types of experimental research designs. These are pre-experimental research design, true experimental research design, and quasi experimental research design.
The difference between an experimental and a quasi-experimental design are: 1. The assignment of the control group in quasi experimental research is non-random, unlike true experimental design, which is randomly assigned. 2. Experimental research group always has a control group; on the other hand, it may not be always present in quasi experimental research.
Experimental research establishes a cause-effect relationship by testing a theory or hypothesis using experimental groups or control variables. In contrast, descriptive research describes a study or a topic by defining the variables under it and answering the questions related to the same.
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Randomization in an experiment refers to a random assignment of participants to the treatment in an experiment. OR, for instance we can say that randomization is assignment of treatment to the participants randomly.
For example : a teacher decides to take a viva in the class and randomly starts asking the students.
Here, all the participants have equal chance of getting into the experiment. Like with our example, every student has equal chance of getting a question asked by the teacher. Randomization helps you stand a chance against biases. It can be a case when you select a group using some category, there can be personal biases or accidental biases. But when the selection is random, you don’t get a chance to look into each participant and hence the groups are fairly divided.
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As mentioned earlier, randomization minimizes the biases. But apart from that it also provides various benefits when adopted as a selection method in experiments.
Randomization can be subject to errors when it comes to “randomly” selecting the participants. As for our example, the teacher surely said she will ask questions to random students, but it is possible that she might subconsciously target mischievous students. This means we think the selection is random, but most of the times it isn’t.
Hence, to avoid these unintended biases, there are three techniques that researchers use commonly:
In simple random sampling. The selection of the participants is completely luck and probability based. Every participant has an equal chance of getting into the sample.
This method is theoretically easy to understand and works best against a sample size of 100 or more. The main factor here is that every participants gets an equal chance of being included in a treatment, and this is why it is also called the method of chances.
Methods of simple random sampling:
Example : A teacher wants to know how good her class is in mathematics. So she will give each student a number and will draw numbers from a bunch of chits. This will include a randomly selected sample size and It won’t have any biases depending on teachers interference.
It is a method of randomly assigning participants to the treatment groups. A block is a group is randomly ordered treatment group. All the blocks have a fair balance of treatment assignment throughout.
Example : A teacher wants to enroll student in two treatments A and B. and she plans to enroll 6 students per week. The blocks would look like this:
Week 1- AABABA
Week 2- BABAAB
Week 3- BBABAB
Each block has 9 A and 9 B. both treatments have been balanced even though their ordering is random.
There are two types of block assignment in permuted block randomization:
Generate a random number for each treatment that is assign in the block. In our example, the block “Week 1” would look like- A(4), A(5), B(56), A(33), B(40), A(10)
Then arrange these treatments according to their number is ascending order, the new treatment could be- AAABB
This includes listing the permutations for the block. Simply, writing down all possible variations.
The formula is b! / ((b/2)! (b/2)!)
For our example, the block sixe is 6, so the possible arrangements would be:
6! / ((6/2)! (6/2)!)
6! / (3)! x (3)!
6x5x4x3x2x1 / (3x2x1) x (3x2x1)
20 possible arrangements.
The word “strata” refers to characteristics. Every population has characteristics like gender, cast, age, background etc. Stratified random sampling helps you consider these stratum while sampling the population. The stratum can be pre-defined or you can define them yourself any way you think is best suitable for your study.
Example: you want to categorize population of a state depending on literacy. Your categories would be- (1) Literate (2) Intermediate (3) Illiterate.
Steps to conduct stratified random sampling:
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Random assignment is an important part of control in experimental research, because it helps strengthen the internal validity of an experiment and avoid biases. ... a randomized block design involves placing participants into blocks based on a shared characteristic (e.g., college students versus graduates), and then using random assignment ...
Background. Various research designs can be used to acquire scientific medical evidence. The randomized controlled trial (RCT) has been recognized as the most credible research design for investigations of the clinical effectiveness of new medical interventions [1, 2].Evidence from RCTs is widely used as a basis for submissions of regulatory dossiers in request of marketing authorization for ...
The idea sounds so simple that defining it becomes almost a joke: randomisation is "putting participants into the treatment groups randomly". If only it were that simple. Randomisation can be a minefield, and not everyone understands what exactly it is or why they are doing it. A key feature of a randomised controlled trial is that it is ...
Single-case experimental designs (SCEDs) involve repeat measurements of the dependent variable under different experimental conditions within a single case, for example, a patient or a classroom 1 ...
Background Randomization is the foundation of any clinical trial involving treatment comparison. It helps mitigate selection bias, promotes similarity of treatment groups with respect to important known and unknown confounders, and contributes to the validity of statistical tests. Various restricted randomization procedures with different probabilistic structures and different statistical ...
Single-case experimental designs are rapidly growing in popularity. This popularity needs to be accompanied by transparent and well-justified methodological and statistical decisions. Appropriate ...
In performing randomization, it is important to consider the choice of methodology in the specific context of the trial/experiment. Sample size, population characteristics, longevity of treatment effect, number of treatment arms, and study design all factor into determining an applicable randomization schedule.
treatment must involve two experimental units. Important to have replication to insure you have power to detect differences Randomization helps to make fair or unbiased comparisons, but only in the sense of being fair or unbiased when averaged over a whole sequence of experiments. Beware of pseudo-replication (sub-sampling)
Four basic tenets or pillars of experimental design— replication, randomization, blocking, and size of experimental units— can be used creatively, intelligently, and consciously to solve both real and perceived problems in comparative experiments. Because research is expensive, both in terms of grant funds and the emotional costs invested ...
1 Introduction. Randomization is one of the oldest and most important ideas in statistics, playing several roles in experimental designs and inference (Cox Citation 2009).Randomization tests were introduced by (Fisher Citation 1935, chap. 21) Footnote 1 to substitute Student's t-tests when normality does not hold, and to restore randomization as "the physical basis of the validity of ...
Randomization in experimental design can address how tasks and stimuli are presented. As a theme, randomization in research is a major topic in experimental design and creation. Balancing is a related, equally important concept. Balancing ensures that each condition is equally replicated, ie. any number of measurements or observations from each ...
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.
Randomization-based inference is especially important in experimental design and in survey sampling. Overview. In the statistical theory of design of experiments, randomization involves randomly allocating the experimental units across the treatment groups. For example, if an experiment compares a new drug against a standard drug, then the ...
Randomized controlled trial is widely accepted as the best design for evaluating the efficacy of a new treatment because of the advantages of randomization (random allocation). Randomization eliminates accidental bias, including selection bias, and provides a base for allowing the use of probability theory.
Randomization is a statistical process in which a random mechanism is employed to select a sample from a population or assign subjects to different groups. The process is crucial in ensuring the random allocation of experimental units or treatment protocols, thereby minimizing selection bias and enhancing the statistical validity. It facilitates the objective comparison of treatment effects in ...
Permuted block randomization is a way to randomly allocate a participant to a treatment group, while keeping a balance across treatment groups. Each "block" has a specified number of randomly ordered treatment assignments. 3. Stratified Random Sampling. Stratified random sampling is useful when you can subdivide areas.
Randomized experimental design yields the most accurate analysis of the effect of an intervention (e.g., a voter mobilization phone drive or a visit from a GOTV canvasser, on voter behavior). ... This is because there are, no doubt, qualities about those volunteers that make them different from students who do not volunteer. And, most important ...
Randomization tools are typically included in study design software, and, for in vivo research, the most noteworthy example is the NC3Rs' Experimental Design Assistant (www.eda.nc3rs.org.uk). This freely available online resource allows to generate and share a spreadsheet with the randomized allocation report after the study has been designed ...
Objective: To review and describe randomization techniques used in clinical trials, including simple, block, stratified, and covariate adaptive techniques. Background: Clinical trials are required to establish treatment efficacy of many athletic training procedures. In the past, we have relied on evidence of questionable scientific merit to aid ...
Randomization is important in an experimental research because it ensures unbiased results of the experiment. It also measures the cause-effect relationship on a particular group of interest. ... The assignment of the control group in quasi experimental research is non-random, unlike true experimental design, which is randomly assigned. 2 ...
The approximate randomization theory associated with analysis of covariance is outlined and conditionality considerations are used to explain the limited role of randomization in experiments with very small numbers of experimental units. The relation between the so-called design-based and model-based analyses is discussed.
Randomization in an experiment refers to a random assignment of participants to the treatment in an experiment. OR, for instance we can say that randomization is assignment of treatment to the participants randomly. For example: a teacher decides to take a viva in the class and randomly starts asking the students.
Randomization is a crucial component of experimental design, and it's important for several reasons: Prevents bias: Randomization ensures that each participant has an equal chance of being assigned to any condition, minimizing the potential for bias in the assignment process. Controls for confounding variables: Randomization helps to ...