Observational Studies and Designed Experiments
Besides classifying statistical studies as either descriptive or inferential, we often need to classify them as either observational studies or designed experiments. In an observational study, researchers simply observe characteristics and take measurements, as in a sample survey. In a designed experiment, researchers impose treatments and controls and then observe characteristics and take measurements. Observational studies can reveal only association, whereas designed experiments can help establish causation.
Census, Sampling, and Experimentation
If the information you need is not already available from a previous study, you might acquire it by conducting a census – that is, by obtaining information for the entire population of interest. However, conducting a census may be time consuming, costly, impractical, or even impossible.
Two methods other than a census for obtaining information are sampling and experimentation. If sampling is appropriate, you must decide how to select the sample; that is, you must choose the method for obtaining a sample from the population. Because the sample will be used to draw conclusions about the entire population, it should be a representative sample – that is, it should reflect as closely as possible the relevant characteristics of the population under consideration.
Three basic principles of experimental design are: control, randomization, and replication. In a designed experiment, the individuals or items on which the experiment is performed are called experimental units. When the experimental units are humans, the term subject is often used in place of experimental unit. Generally, each experimental condition is called a treatment, of which there may be several.
Most modern sampling procedure involve the use of probability sampling. In probability sampling, a random device – such as tossing a coin, consulting a table of random numbers, or employing a random-number generator – is used to decide which members of the population will constitute the sample instead of leaving such decisions to human judgement. The use of probability sampling may still yield a non representative sample. However, probability sampling helps eliminate unintentional selection bias and permits the researcher to control the chance of obtaining a non representative sample. Furthermore, the use of probability sampling guarantees that the techniques of inferential statistics can be applied.
Simple Random Sampling
Simple random sampling is a sampling procedure for which each possible sample of a given size is equally likely to be the one obtained. There are two types of simple random sampling. One is simple random sampling with replacement (SRSWR), whereby a member of the population can be selected more than once; the other is simple random sampling without replacement (SRS), whereby a member of the population can be selected at most once.
Simple random sampling is the most natural and easily understood method of probability sampling – it corresponds to our intuitive notion of random selection by lot. However, simple random sampling does have drawbacks. For instance, it may fail to provide sufficient coverage when information about subpopulations is required and may be impractical when the members of the population are widely scattered geographically.
Systematic Random Sampling
One method that takes less effort to implement than simple random sampling is systematic random sampling.
Another sampling method is cluster sampling, which is particular useful when the members of the population are widely scattered geographically.
Another sampling method, known as stratified sampling, is often more reliable than cluster sampling. In stratified sampling, the population is first divided into subpopulations, called strata, and then sampling is done from each stratum. Ideally, the members of each stratum should be homogenous relative to the characteristic under consideration. In stratified sampling, the strata are often sampled in proportion to their size, which is called proportional allocation.
Basic Study Design
We discuss several major clinical trial designs here. Most trials use the so-called parallel design. That is, the intervention and control groups are followed simultaneously from the time of allocation to one or the other. Exceptions to the simultaneous follow-up are historical control studies. These compare a group of participants on a new intervention with a previous group of participants on standard or control therapy. A modification of the parallel design is the cross-over trial, which uses each participant at least twice, at least once as a member of the control group and at least once as a member of one or more intervention groups. Another modification is a withdrawal study, which starts with all participants on the active intervention and then, usually randomly, assigns a portion to be followed on the active intervention and the remainder to be followed off the intervention. Factorial design trials employ two or more independent assignments to intervention or control.
Randomized Control Trials
Randomized control trials are comparative studies with an intervention group and a control group; the assignment of the participant to a group is determined by the formal procedure of randomization. Randomization, in the simplest case, is a process by which all participants are equally likely to be assigned to either the intervention group or the control group. The features of this technique are discuss detail below. Not all clinical studies can use randomized controls. Occasionally, the prevalence of the disease is so rare that a large enough population cannot be readily obtained. In such an instance, only case-control studies might be possible. Such studies, are not clinical trials however.
Nonrandomized Concurrent Control Studies
Controls in this type of study are participants treated without the new intervention at approximately the same time as the intervention group is treated. Participants are allocated to one of the two groups, but by definition this is not a random process. An example of a nonrandomized concurrent control study would be a comparison of survival results of patients treated at two institutions, one institution using a new surgical procedure and the other using more traditional medical care. Another example is when patients are offered either of two treatments and the patient selects the one that he or she thinks is preferable. Comparisons between the two groups is then made, adjusting for any observed baseline imbalances.
To some investigators, the nonrandomized concurrent control design has advantages over the randomized control design. Those who object to the idea of ceding to chance the responsibility for selecting a person’s treatment may favor this design. It is also difficult for some investigators to convince potential participants of the need for randomization. They find it easier to offer the intervention to some and the control to others, hoping to match on key characteristics. The major weakness of the nonrandomized concurrent control study is the potential that the intervention group and control group are not strictly comparable. It is difficult to prove comparability because the investigator must assume that she has information on all the important prognostic factors. Selecting a control group by matching on more than a few factors is impractical and the comparability of a variety of other characteristics would still need to be evaluated. In small studies, an investigator is unlikely to find real differences which may exist between groups before the initiation of intervention since there is poor sensitivity statistically to detect such differences (e.g., high 𝛽 and not enough power). Even for large studies that could detect most differences of real clinical importance, the uncertainty about the unknown or unmeasured factors is still of concern.
Historical Controls and Databases
In historical control studies, a new intervention is used in a series of participants and the results are compared to the outcome in a previous series of comparable participants. Historical controls are thus, by this definition, nonrandomized and nonconcurrent. Typically, historical control data can be obtained from two sources. First, control group data may be available in the literature. These data are often undesirable because it is difficult, and perhaps impossible, to establish whether the control and intervention groups are comparable in key characteristics at the onset. Even if such characteristics were measured in the same way, the information may not be published and for all practical purposes it will be lost. Second, data may not have been published but may be available on computer files or in medical charts. Such data on control participants, for example, might be found in a large center which has several ongoing clinical investigations. When one study is finished, the participants in that study may be used as a control group for some future study. Centers which do successive studies, as in cancer research, will usually have a system for storing and retrieving the data from past studies for use at some future time. The advent of electronic medical records may also facilitate access to historical data from multiple sources, although it does not solve the problem of nonstandard and variable assessment or missing information.
Despite the time and cost benefits, as well as the ethical considerations, historical control studies have potential limitations which should be kept in mind. They are particularly vulnerable to bias. An improvement in outcome for a given disease may be attributed to a new intervention when, in fact, the improvement may stem from a change in the patient population or patient management. Shifts in patient population can be subtle and perhaps undetectable. In a Veterans Administration Urological Research Group study of prostate cancer, people were randomized to placebo or estrogen treatment groups over a 7-year period. For those enrolled during the last 2-3 years, no differences were found between the placebo and estrogen groups. However, those assigned to placebo entering in the first 2-3 years had a shorter survival time than those assigned to estrogen entering in the last 2-3 years of the study. The reason for the early apparent difference is probably that the people randomized earlier were older than the later group and thus were at higher risk of death during the period of observation.
Once we have chosen the treatments, we must decide how the experimental units are to be assigned to the treatments (or vice versa). In a completely randomized design, all the experimental units are assigned randomly among all the treatments. In a randomized block design, experimental units are similar in ways that are expected to affect the response variable are grouped in blocks. Then the random assignment of experimental units to the treatment is made block by block. Or, the experimental units are assigned randomly among all the treatments separately within each block.
Randomized Block Design and Randomized Block ANOVA
In this section we introduce a design that has its basic focus on a single factor, but uses an additional factor (called a blocking factor) to account for the effects of dissimilar groups of experimental units on the value of the response variable. Suppose we are interested in a single factor with k treatments (levels). Sometimes there is no much variation in the values of the response variable within each treatment that use of a completely randomized design will fail to detect differences among the treatment means when such difference exist. This is because it is often not possible to decide whether the variation among the sample means for the different treatments is due to differences among the treatment means or whether it is due to variation within the treatments (i.e., variation in the values of the response variable within each treatment).
If a large portion of the variation within the treatments is due to one extraneous variable, then it is often appropriate to use a randomized block design instead of a completely randomized design. In a randomized block design, the extraneous source of variation is isolated and removed so that it is easier to detect differences among the treatment means when such differences exist. Although a randomized block design is not always appropriate or feasible, it is often a viable alternative to a completely randomized design in the presence of a single extraneous source of variability. In a randomized block design, the experimental units within each block should be randomly assigned among all the treatments. Compared with two-way ANOVA:
- The blocking factor is not a factor of interest to the experimenter; only one factor is of real interest to the experimenter, namely, the treatment factor.
- There is a restriction in the way the randomization is performed in assigning the experimental units to the treatments. The experimental units are not assigned to the treatments completely at random; rather the experimental units within each block are assigned randomly to the treatments so that each treatment occurs once and only once within each block.
It is important to remember that including a blocking factor in our design is meant to account for another source of variation in the values of the response variable and thus reduce the variation that is due to “experimental error.” A properly selected blocking factor will make the test for the treatment effect more sensitive by reducing the error sum of squares.
Sample Size for Estimating 𝜇
Sample Size for Estimating p
Sample Size Calculation for Continuous Response Variables
where 2N = total sample size (N participants / group), 𝜎 = the pooled population standard deviation, 𝛿 = 𝜇1 – 𝜇2
Sample Size Calculation for Proportions
where 2N = total sample size (N participants / group), pbar = (pc + pi) / 2
Sample Size Calculation for Survival Functions
where 2N = total sample size (N participants / group), 𝜆 = population hazard function
One-Mean z-Interal Procedure
One-Mean t-Interval Procedure
Wilcoxon Signed-Rank Test
Note: The following points may be relevant when performing a Wilcoxon signed-rank test:
- If an observation equals 𝜇0 (the value for the mean in the null hypothesis), that observation should be removed and the sample size reduced by 1.
- If two or more absolute differences are tied, each should be assigned the mean of the ranks they would have had if there were no ties.
Pooled t-Interval Procedure
Nonpooled t-Interval Procedure
Mann-Whitney Test (Wilcoxon rank-sum test, Mann-Whitney-Wilcoxon test)
Note: When there are ties in the sample data, ranks are assigned in the same way as in the Wilcoxon signed-rank test. Namely, if two or more observations are tied, each is assigned the mean of the ranks they would have had if there had been no ties.
Paired t-Interval Procedure
Paired Wilcoxon Signed-Rank Test
One-Proportion z-Interval Procedure
Two-Proportions z-Interval Procedure
Chi-Square Goodness-of-Fit Test
Chi-Square Independence Test
Chi-Square Homogeneity Test
One-Standard-Deviation Chi-Square Test
One-Standard-Deviation Chi-Square Interval Procedure
Two-Standard-Deviations F-Interval Procedure
Turkey Multiple-Comparison Method
Simple Linear Regression
Coefficient of Determination
The coefficient of determination is a descriptive measure of the utility of the regression equation for making predictions. The coefficient of determination always lies between 0 and 1. A value of r^2 near 0 suggests that the regression equation is not very useful for making predictions, whereas a value of r^2 near 1 suggests that the regression equation is quite useful for making predictions.
- r reflects the slope o the scatterplot
- The magnitude of r indicates the strength of the linear relationship
- The sign of r suggests the type of linear relationship
- The sign of r and the sign of the slop of the regression line are identical
Assumption Before Linear Regression
Standard Error of the Estimate
Regression t-Interval Procedure
Conditional Mean t-Interval Procedure
Meta-Analysis: Which Model Should We Use?
Fix effect model
It makes sense to use the fixed-effect model if two conditions are met. First, we believe that all the studies included in the analysis are functionally identical. Second, our goal is to compute the common effect size for the identified population, and not to generalize to other populations. For example, suppose that a pharmaceutical company will use a thousand patients to compare a drug versus placebo. Because the staff can work with only 100 patients at a time, the company will run a series of ten trials with 100 patients in each. The studies are identical in the sense that any variable which can have an impact on the outcome are the same across the ten studies. Specifically, the studies draw patients from a common pool, using the same researchers, dose, measure, and so on.
By contrast, when the researcher is accumulating data from a series of studies that had been performed by researchers operating independently, it would be unlikely that all the studies were functionally equivalent. Typically, the subjects or interventions in these studies would have differed in ways that would have impacted on the results, and therefore we should not assume a common effect size. Therefore, in these cases the random-effects model is more easily justified than the fixed-effect model. Additionally, the goal of this analysis is usually to generalize to a range of scenarios. Therefore, if one did make the argument that all the studies used an identical, narrowly defined population, then it would not be possible to extrapolate from this population to others’ nd the utility of the analysis would be severely limited.
To understand the problem, suppose for a moment that all studies in the analysis shared the same true effect size, so that the (true) heterogeneity is zero. Under this assumption, we would not expect the observed effect to be identical to each other. Rather, because of within-study error, we would expect each to fall within some range of the common effect. Now, assume that the true effect size does vary from one study to the next. In this case, the observed effects vary from one another for two reasons. One is the real heterogeneity in effect size, and the other is the within-study error. If we want to quantify the heterogeneity we need to partition the observed variation into these two components, and then focus on the former.
The mechanism that we use to extract the true between-studies variation from the observed variation is as follows:
- We compute the total amount of study-to-study variation actually observed.
- We estimate how much the observed effects would be expected to vary from each other if the true effect was actually the same in all studies.
- The excess variation (if any) is assumed to reflect real differences in effect size (that is, the heterogeneity)
The function of randomization include:
- Randomization removes the potential of bias in the allocation of participants to the intervention group or to the control group. Such selection bias could easily occur, and cannot be necessarily prevented, in the non-randomziared concurrent or historical control study because the investigator or the participant may influence the choice of intervention. The direction of the allocation bias may go either way and can easily invalidate the comparison. This advantage of randomization assumes that the procedure is performed in a valid manner and that the assignment cannot be predicted.
- Some what related to the first, is that randomization tends to produce comparable groups; that is, measured as well as unknown or unmeasured prognostic factors and other characteristics of the participants at the time of randomization will be, on the average, evenly balanced between the intervention and control groups. This dose not mean that in any single experiment all such characteristics, sometimes called baseline variables or covariates, will be perfectly balanced between the two groups. However, it does mean that for independent covariates, whatever the detected or undetected differences that exist between the groups, the overall magnitude and direction of the differences will tend to be equally divided between the two groups. Of course, many covariates are strongly associated; thus, any imbalance in one would tend to produce imbalances in the others.
- The validity of statistical tests of significance is guaranteed. The process of randomization makes it possible to ascribe a probability distribution to the difference in outcome between treatment groups receiving equally effective treatments and thus to assign significance levels to observed differences. The validity of the statistical tests of significance is not dependent on the balance of the prognostic factors between the randomized groups. The chi-square test for two-by-two tables and Student’s t-test for comparing two means can be justified on the basis of randomization alone without making further assumptions concerning the distribution of baseline variables. If randomization is not used, further assumptions conceding the comparability of the groups and the appropriateness fo the statistical models must be made before the comparisons will be valid. Establishing the validity of these assumptions may be difficult.
In the simplest case, randomization is a process by which each participant has the same chance of being assigned to either intervention or control. An example would be the toss of a coin, in which heads indicates intervention group and tails indicates control group. Even in the more complex randomization strategies, the element of chance underlies the allocation process. Of course, neither trial participant nor investigator should know what the assignment will be before the participant’s decision to enter the study. Otherwise, the benefits of randomization can be lost.
The Randomization Process
Two forms of experimental bias are of concern. The first, selection bias, occurs if the allocation process is predictable. In this case, the decision to enter a participant into a trial may be influenced by the anticipated treatment assignment. If any bias exists as to what treatment particular types of participants should receive, then a selection bias might occur. A second bias, accidental bias, can arise if the randomization procedure does not achieve balance on risk factors or prognostic covariates. Some of the allocation procedures are more vulnerable to accidental bias, especially for small studies. For large studies, however, the chance of accidental bias is negligible.
Fixed Allocation Randomization
Fixed allocation procedures assign the interventions to participants with a respecified probability, usually equal (e.g., 50% for two arms, 33% for 3, or 25% for 4, etc.) and that allocation probability is not altered as the study progresses. Three methods of randomization belong to the fixed allocation, including: simple, blacked, and stratified randomization. The most elementary form of randomization is referred to as simple or complete randomization. One simple method is to toss an unbiased coin each time a participant is eligible to be randomized (for two treatment combinations). Using this procedure, approximately one half of the participants will be in group A and one half in group B. In practice, for small studies, instead of tossing a coin to generate a randomization schedule, a random digit table on which the equally likely digits 0 to 9 are arranged by tows and columns is usually used to accomplish simple randomization. For large studies, a more convenient method for producing a randomization schedule is to use a random number producing algorithm, available on most computer systems. Another simple randomization is to use a uniform random number algorithm to produce random numbers in the interval from 0.0 to 1.0. Using a uniform random number generator, a random number can be produced for each participant. If the random number is between 0 and p, the participant would be assigned to group A; otherwise to group B. For equal allocation, the probability cut point, p, is one-half (i.e., p = 0.50). If equal allocation between A and B is not desired, then p can be set to the desired proportion in the algorithm and the study will have, on the average, a proportion p of the participants in group A. In addition, this strategy could be adapted easily to more than two groups.
Blocked randomization, sometimes called permuted block randomization, avoids serious imbalance in the number of participants assigned to each group, an imbalance which could occur in the simple randomization procedure. More importantly, blocked randomization guarantees that at no time during randomization will the imbalance be large and that at certain points the number of participants in each group will be equal. This protects against temporal trends during enrollment, which is often a concern for larger trials with long enrollment phases. If participants are randomly assigned with equal probability to groups A or B, then for each block of even size (for example, 4, 6, or 8) one half of the participants will be assigned to A and the other half to B. The order in which the interventions are assigned in each block is randomized, and this process is repeated for consecutive blocks of participants until all participants are randomized.
Many researchers consider survival data analysis to be merely the application of two conventional statistical methods to a special type of problem: parametric if the distribution of survival times is known to be normal and nonparametric if the distribution is unknown. This assumption would be true if the survival times of all the subjects were exact and known; however, some survival times are not. Further, the survival distribution is often skewed, or far from being normal. Thus there is a need for new statistical techniques. One of the most important developments is due to a special feature of survival data in the life sciences that occurs when some subjects in the study or time of analysis. For example, some patients may still be alive or disease-free at the end of the study period. The exact survival times of these subjects are unknown. These are called censored observations or censored times and can also occur when people are lost to follow-up after a period of study. When these are not censored observation, the set of survival times is complete.
Type I Censoring
Animal studies usually start with a fixed number of animals, to which the treatment or treatments is given. Because of time and/or cost limitations, the researcher often cannot wait for the death of all the animals. One option is to observe for a fixed period of time, say six months, after which the surviving animals are sacrificed. Survival times recorded for the animals that died during the study period are the times from the start of the experiment to their death. These are called exact or uncensored observations. The survival times of the sacrificed animals are not known exactly but are recored as at east the length of the study period. These are called censored observations. Some animals could be lost or die accidentally. Their survival times, from the start of experiment to loss or death, are also censored observations. In type I censoring, if there are no accidental losses, all censored observations equal the length of the study period.
Type II Censoring
Another option in animal studies is to wait until a fixed portion of the animals have died, say 80 to 100, after which the surviving animals are sacrificed. In this case, type II censoring, if there are no accidental losses, the censored observations equal the largest uncensored observation.
Type III Censoring
In most clinical and epidemiological studies
There are generally three reasons why censoring may occur:
- A person does not experience the event before the study ends;
- A person is lost to follow-up during the study period;
- A person withdraws from the study because of death or some other reason.