PART3-Prepare a 2-page outline of your Research Proposal. The outline should provide an overview of the main elements of your proposal. It should include:
- An introduction
- A brief statement of purpose
- The rationale for conducting the study
- Your hypotheses and research questions
- Methods (participants, procedures, materials, instruments), and appropriate statistical test(s) for data analysis
- List of at least three relevant articles for the proposal
Submit your assignment.
The purpose of this outline is to obtain feedback from your instructor on your progress and on the feasibility of your topic and design.
PART4- PLEASE SEE TEAM ATTACHMENT. I ONLY HAVE TO COMPLETE THE SECTION THAT SAYS “Example of Hawthorne Effect”
REFERENCE CHAPTER 11
- Describe single-case experimental designs and discuss reasons to use this design.
- Describe the one-group posttest-only design.
- Describe the one-group pretest-posttest design and the associated threats to internal validity that may occur: history, maturation, testing, instrument decay, and regression toward the mean.
- Describe the nonequivalent control group design and nonequivalent control group pretest-posttest design, and discuss the advantages of having a control group.
- Distinguish between the interrupted time series design and control series design.
- Describe cross-sectional, longitudinal, and sequential research designs, including the advantages and disadvantages of each design.
- Define cohort effect.
IN THE CLASSIC EXPERIMENTAL DESIGN DESCRIBED IN CHAPTER 8, PARTICIPANTS ARE RANDOMLY ASSIGNED TO THE INDEPENDENT VARIABLE CONDITIONS, AND A DEPENDENT VARIABLE IS MEASURED. The responses on the dependent measure are then compared to determine whether the independent variable had an effect. Because all other variables are held constant, differences on the dependent variable must be due to the effect of the independent variable. This design has high internal validity—we are very confident that the independent variable caused the observed responses on the dependent variable. You will frequently encounter this experimental design when you explore research in the behavioral sciences. However, other research designs have been devised to address special research problems.
This chapter focuses on three types of special research situations. The first is the instance in which the effect of an independent variable must be inferred from an experiment with only one participant—single-case experimental designs. Second, we will describe pre-experimental and quasi-experimental designs that may be considered if it is not possible to use one of the true experimental designs described in Chapter 8. Third, we consider research designs for studying changes that occur with age.
SINGLE-CASE EXPERIMENTAL DESIGNS
Single-case experimental designs have traditionally been called single-subject designs; an equivalent term you may see is small N designs. Much of the early interest in single-case designs in psychology came from research on operant conditioning pioneered by B. F. Skinner (e.g., Skinner, 1953). Today, research using single-case designs is often seen in applied behavior analysis in which operant conditioning techniques are used in clinical, counseling, educational, medical, and other applied settings (Kazdin, 2011, 2013).
Single-case experiments were developed from a need to determine whether an experimental manipulation had an effect on a single research participant. In a single-case design, the subject’s behavior is measured over time during a baseline control period. The manipulation is then introduced during a treatment period, and the subject’s behavior continues to be observed. A change in the subject’s behavior from baseline to treatment periods is evidence for the effectiveness of the manipulation. The problem, however, is that there could be many explanations for the change other than the experimental treatment (i.e., alternative explanations). For example, some other event may have coincided with the introduction of the treatment. The single-case designs described in the following sections address this problem.
As noted, the basic issue in single-case experiments is how to determine that the manipulation of the independent variable had an effect. One method is Page 222to demonstrate the reversibility of the manipulation. A simple reversal design takes the following form:
This basic reversal design is called an ABA design; it requires observation of behavior during the baseline control (A) period, again during the treatment (B) period, and also during a second baseline (A) period after the experimental treatment has been removed. (Sometimes this is called a withdrawal design, in recognition of the fact that the treatment is removed or withdrawn.) For example, the effect of a reinforcement procedure on a child’s academic performance could be assessed with an ABA design. The number of correct homework problems could be measured each day during the baseline. A reinforcement treatment procedure would then be introduced in which the child received stars for correct problems; the stars could be accumulated and exchanged for toys or candies. Later, this treatment would be discontinued during the second baseline (A) period. Hypothetical data from such an experiment are shown in Figure 11.1. The fact that behavior changed when the treatment was introduced and reversed when the treatment was withdrawn is evidence for its effectiveness.
Figure 11.1 depicts a treatment that had a relatively dramatic impact on behavior. Some treatments do produce an immediate change in behavior, but many other variables may require a longer time to show an impact.
The ABA design can be greatly improved by extending it to an ABAB design, in which the experimental treatment is introduced a second time, or even to an ABABAB design that allows the effect of the treatment to be tested a third time. This is done to address two problems with the ABA reversal design. First, a single reversal is not extremely powerful evidence for the effectiveness of the treatment. The observed reversal might have been due to a random fluctuation in the child’s behavior; perhaps the treatment happened to coincide with some other event, such as the child’s upcoming birthday, that caused the change (and the post-birthday reversal). These possibilities are much less likely if the treatment has been shown to have an effect two or more times; random or coincidental events are unlikely to be responsible for both reversals. The second problem is ethical. As Barlow, Nock, and Hersen (2009) point out, it does not seem right to end the design with the withdrawal of a treatment that may be very beneficial for the participant. Using an ABAB design provides the opportunity to observe a second reversal when the treatment is introduced again. The sequence ends with the treatment rather than the withdrawal of the treatment.
Hypothetical data from ABA reversal design
Page 223The logic of the reversal design can also be applied to behaviors observed in a single setting. For example, Kazbour and Bailey (2010) examined the effectiveness of a procedure designed to increase use of designated drivers in a bar. The percentage of bar patrons either serving as or being with a designated driver was recorded over a baseline period of 2 weeks. A procedure to increase the use of designated drivers was then implemented during the treatment phase. Designated drivers received a $5 gas card, and the driver and passengers received free pizza on their way out of the bar. The pizza and gas incentive was discontinued during the final phase of the study. The percentage of bar patrons engaged in designated driver arrangements increased substantially during the treatment phase but returned to baseline levels when the incentive was withdrawn.
Multiple Baseline Designs
It may have occurred to you that a reversal of some behaviors may be impossible or unethical. For example, it would be unethical to reverse treatment that reduces dangerous or illegal behaviors, such as indecent exposure or alcoholism, even if the possibility exists that a second introduction of the treatment might be effective. Other treatments might produce a long-lasting change in behavior that is not reversible. In such cases, multiple measures over time can be made before and after the manipulation. If the manipulation is effective, a change in behavior will be immediately observed, and the change will continue to be reflected in further measures of the behavior. In a multiple baseline design, the effectiveness of the treatment is demonstrated when a behavior changes only after the manipulation is introduced. To demonstrate the effectiveness of the treatment, such a change must be observed under multiple circumstances to rule out the possibility that other events were responsible.
There are several variations of the multiple baseline design (Barlow et al., 2009). In the multiple baseline across subjects, the behavior of several subjects is measured over time; for each subject, though, the manipulation is introduced at a different point in time. Figure 11.2 shows data from a hypothetical smoking reduction experiment with three subjects. Note that introduction of the manipulation was followed by a change in behavior for each subject. However, because this change occurred across all individuals and the manipulation was introduced at a different time for each subject, we can rule out explanations based on chance, historical events, and so on.
Hypothetical data from multiple baseline design across three subjects (S1, S2, and S3)
In a multiple baseline across behaviors, several different behaviors of a single subject are measured over time. At different times, the same manipulation is applied to each of the behaviors. For example, a reward system could be instituted to increase the socializing, grooming, and reading behaviors of a psychiatric patient. The reward system would be applied to each of these behaviors at different times. Demonstrating that each behavior increased when the reward system was applied would be evidence for the effectiveness of the manipulation.
The third variation is the multiple baseline across situations, in which the same behavior is measured in different settings, such as at home and at work. Again, a manipulation is introduced at a different time in each setting, with the expectation that a change in the behavior in each situation will occur only after the manipulation.
Replications in Single-Case Designs
The procedures for use with a single subject can, of course, be replicated with other subjects, greatly enhancing the generalizability of the results. Usually, reports of research that employs single-case experimental procedures do present Page 225the results from several subjects (and often in several settings). The tradition in single-case research has been to present the results from each subject individually rather than as group data with overall means. Sidman (1960), a leading spokesperson for this tradition, has pointed out that grouping the data from a number of subjects by using group means can sometimes give a misleading picture of individual responses to the manipulation. For example, the manipulation may be effective in changing the behavior of some subjects but not others. This was true in a study conducted by Ryan and Hemmes (2005) that investigated the impact of rewarding college students with course grade points for submitting homework. For half of the 10 chapters, students received points for submitting homework; however, there were no points given if they submitted homework for the other chapters (to control for chapter topic, some students had points for odd-numbered chapters only and others received points for the even-numbered chapters). Ryan and Hemmes found that on average students submitted more homework assignments and performed better on chapter-based quizzes that were directly associated with point rewards. However, some individual participants performed about the same regardless of condition. Because the emphasis of the study was on the individual subject, this pattern of results was quickly revealed.
Single-case designs are useful for studying many research problems and should be considered a powerful alternative to more traditional research designs. They can be especially valuable for someone who is applying some change technique in a natural environment—for example, a teacher who is trying a new technique in the classroom. In addition, complex statistical analyses are not required for single-case designs.
Quasi-experimental designs address the need to study the effect of an independent variable in settings in which the control features of true experimental designs cannot be achieved. Thus, a quasi-experimental design allows us to examine the impact of an independent variable on a dependent variable, but causal inference is much more difficult because quasi-experiments lack important features of true experiments such as random assignment to conditions. In this chapter, we will examine several quasi-experimental designs that might be used in situations in which a true experiment is not possible. This is most likely to occur in applied settings when an independent variable is manipulated in a natural setting such as a school, business, hospital, or an entire city or state.
There are many types of quasi-experimental designs—see Campbell (1968, 1969), Campbell and Stanley (1966), Cook and Campbell (1979), Shadish, Cook, and Campbell (2002). Only six designs will be described. As you read about each design, compare the design features and problems with the randomized true experimental designs described in Chapter 8. We start out with the simplest and most problematic of the designs. In fact, the first three designs Page 226we describe are sometimes called “pre-experimental” to distinguish them from other quasi-experimental designs. This is because of the problems associated with these designs. Nevertheless, all may be used in different circumstances, and it is important to recognize the internal validity issues raised by each design.
One-Group Posttest-Only Design
Suppose you want to investigate whether sitting close to a stranger will cause the stranger to move away. You might try sitting next to a number of strangers and measure the number of seconds that elapse before they leave. Your design would look like this:
Now suppose that the average amount of time before the people leave is 9.6 seconds. Unfortunately, this finding is not interpretable. You do not know whether they would have stayed longer if you had not sat down or whether they would have stayed for 9.6 seconds anyway. It is even possible that they would have left sooner if you had not sat down—perhaps they liked you!
This one-group posttest-only design—called a “one-shot case study” by Campbell and Stanley (1966)—lacks a crucial element of a true experiment: a control or comparison group. There must be some sort of comparison condition to enable you to interpret your results. The one-group posttest-only design with its missing comparison group has serious deficiencies in the context of designing an internally valid experiment that will allow us to draw causal inferences about the effect of an independent variable on a dependent variable.
You might wonder whether this design is ever used. In fact, you may see this type of design used as evidence for the effectiveness of a program. For example, employees in a company might participate in a 4-hour information session on emergency procedures. At the conclusion of the program, they complete a knowledge test on which their average score is 90%. This result is then used to conclude that the program is successfully educating employees. Such studies lack internal validity—our ability to conclude that the independent variable had an effect on the dependent variable. With this design, we do not even know if the score on the dependent variable would have been equal, lower, or even higher without the program. The reason why results such as these are sometimes accepted is because we may have an implicit idea of how a control group would perform. Unfortunately, we need that comparison data.
One-Group Pretest-Posttest Design
One way to obtain a comparison is to measure participants before the manipulation (a pretest) and again afterward (a posttest). An index of change from Page 227the pretest to the posttest could then be computed. Although this one-group pretest-posttest design sounds fine, there are some major problems with it.
To illustrate, suppose you wanted to test the hypothesis that a relaxation training program will result in a reduction in cigarette smoking. Using the one-group pretest-posttest design, you would select a group of people who smoke, administer a measure of smoking, have them go through relaxation training, and then re-administer the smoking measure. Your design would look like this:
If you did find a reduction in smoking, you could not assume that the result was due to the relaxation training program. This design has failed to take into account several alternative explanations. These alternative explanations are threats to the internal validity of studies using this design and include history, maturation, testing, instrument decay, and regression toward the mean.
History History refers to any event that occurs between the first and second measurements but is not part of the manipulation. Any such event is confounded with the manipulation. For example, suppose that a famous person dies of lung cancer during the time between the first and second measures. This event, and not the relaxation training, could be responsible for a reduction in smoking. Admittedly, the celebrity death example is dramatic and perhaps unlikely. However, history effects can be caused by virtually any confounding event that occurs at the same time as the experimental manipulation.
Maturation People change over time. In a brief period they become bored, fatigued, perhaps wiser, and certainly hungrier; over a longer period, children become more coordinated and analytical. Any changes that occur systematically over time are called maturation effects. Maturation could be a problem in the smoking reduction example if people generally become more concerned about health as they get older. Any such time-related factor might result in a change from the pretest to the posttest. If this happens, you might mistakenly attribute the change to the treatment rather than to maturation.
Testing Testing becomes a problem if simply taking the pretest changes the participant’s behavior—the problem of testing effects. For example, the smoking measure might require people to keep a diary in which they note every cigarette smoked during the day. Simply keeping track of smoking might be sufficient to cause a reduction in the number of cigarettes a person smokes. Thus, the reduction found on the posttest could be the result of taking the Page 228pretest rather than of the program itself. In other contexts, taking a pretest may sensitize people to the purpose of the experiment or make them more adept at a skill being tested. Again, the experiment would not have internal validity.
Instrument decay Sometimes, the basic characteristics of the measuring instrument change over time; this is called instrument decay. Consider sources of instrument decay when human observers are used to measure behavior: Over time, an observer may gain skill, become fatigued, or change the standards on which observations are based. In our example on smoking, participants might be highly motivated to record all cigarettes smoked during the pretest when the task is new and interesting, but by the time the posttest is given they may be tired of the task and sometimes forget to record a cigarette. Such instrument decay would lead to an apparent reduction in cigarette smoking.
Regression toward the mean Sometimes called statistical regression, regression toward the mean is likely to occur whenever participants are selected because they score extremely high or low on some variable. When they are tested again, their scores tend to change in the direction of the mean. Extremely high scores are likely to become lower (closer to the mean), and extremely low scores are likely to become higher (again, closer to the mean).
Regression toward the mean would be a problem in the smoking experiment if participants were selected because they were initially found to be extremely heavy smokers. By choosing people for the program who scored highest on the pretest, the researcher may have selected many participants who were, for whatever reason, smoking much more than usual at the particular time the measure was administered. Those people who were smoking much more than usual will likely be smoking less when their smoking is measured again. If we then compare the overall amount of smoking before and after the program, it will appear that people are smoking less. The alternative explanation is that the smoking reduction is due to statistical regression rather than the effect of the program.
Regression toward the mean will occur whenever you gather a set of extreme scores taken at one time and compare them with scores taken at another point in time. The problem is actually rooted in the reliability of the measure. Recall from Chapter 5 that any given measure reflects a true score plus measurement error. If there is perfect reliability, the two measures will be the same (if nothing happens to lower or raise the scores). If the measure of smoking is perfectly reliable, a person who reports smoking 20 cigarettes today will report smoking 20 cigarettes 2 weeks from now. However, if the two measures are not perfectly reliable and there is measurement error, most scores will be close to the true score but some will be higher and some will be lower. Thus, one smoker with a true score of 20 cigarettes per day might sometimes smoke 5 and sometimes 35; however, most of the time, the number is closer to 20 than the extremes. Another smoker might have a true score of 35 but on occasion smokes as few as 20 and as many as 50; again, most of the time, the number is Page 229closer to the true score than to the extremes. Now suppose that you select two people who said they smoked 35 cigarettes on the previous day, and that both of these people are included in the group—you picked the first person on a very unusual day and the second person on a very ordinary day. When you measure these people 2 weeks later, the first person is probably going to report smoking close to 20 cigarettes and the second person close to 35. If you average the two, it will appear that there is an overall reduction in smoking.
What if the measure were perfectly reliable? In this case, the person with a true score of 20 cigarettes would always report this amount and therefore would not be included in the heavy smoker (35+) group at all. Only people with true scores of 35 or more would be in the group, and any reduction in smoking would be due to the treatment program. The point here is that regression toward the mean is a problem if there is measurement error.
Statistical regression occurs when we try to explain events in the “real world” as well. Sports columnists often refer to the hex that awaits an athlete who appears on the cover of Sports Illustrated. The performances of a number of athletes have dropped considerably after they were the subjects of Sports Illustrated cover stories. Although these cover stories might cause the lower performance (perhaps the notoriety results in nervousness and reduced concentration), statistical regression is also a likely explanation. An athlete is selected for the cover of the magazine because he or she is performing at an exceptionally high level; the principle of regression toward the mean states that very high performance is likely to deteriorate. We would know this for sure if Sports Illustrated also did cover stories on athletes who were in a slump and this became a good omen for them!
All these problems can be eliminated by the use of an appropriate control group. A group that does not receive the experimental treatment provides an adequate control for the effects of history, statistical regression, and so on. For example, outside historical events would have the same effect on both the experimental and the control groups. If the experimental group differs from the control group on the dependent measure administered after the manipulation, the difference between the two groups can be attributed to the effect of the experimental manipulation.
Given these problems, is the one-group pretest-posttest design ever used? This design may in fact be used in many applied settings. Recall the example of the evaluation of a program to teach emergency procedures to employees. With a one group pretest-posttest design, the knowledge test would be given before and after the training session. The ability to observe a change from the pretest to the posttest does represent an improvement over the posttest-only design, even with the threats to internal validity that we identified. In addition, the ability to use data from this design can be enhanced if the study is replicated at other times with other participants. However, formation of a control group is always the best way to strengthen this design.
In any control group, the participants in the experimental condition and the control condition must be equivalent. If participants in the two groups Page 230differ before the manipulation, they will probably differ after the manipulation as well. The next design illustrates this problem.
Nonequivalent Control Group Design
The nonequivalent control group design employs a separate control group, but the participants in the two conditions—the experimental group and the control group—are not equivalent. In other words, the two groups are not the result of random assignment. The differences become a confounding variable that provides an alternative explanation for the results. This problem, called selection differences or selection bias, usually occurs when participants who form the two groups in the experiment are chosen from existing natural groups. If the relaxation training program is studied with the nonequivalent control group design, the design will look like this:
The participants in the first group are given the smoking frequency measure after completing the relaxation training. The people in the second group do not participate in any program. In this design, the researcher does not have any control over which participants are in each group. Suppose, for example, that the study is conducted in a division of a large company. All of the employees who smoke are identified and recruited to participate in the training program. The people who volunteer for the program are in the experimental group, and the people in the control group are simply the smokers who did not sign up for the training. The problem of selection differences arises because smokers who choose to participate may differ in some important way from those who do not. For instance, they may already be light smokers compared with the others and more confident that a program can help them. If so, any difference between the groups on the smoking measure would reflect preexisting differences rather than the effect of the relaxation training. Such a preexisting difference is what we have previously described as a confound (see Chapter 4).
It is important to note that the problem of selection differences arises in this design even when the researcher apparently has successfully manipulated the independent variable using two similar groups. For example, a researcher might have all smokers in the engineering division of a company participate in the relaxation training program and smokers who work in the marketing division serve as a control group. The problem here, of course, is that the smokers in the two divisions may have differed in smoking patterns prior to the relaxation program.
Nonequivalent Control Group Pretest-Posttest Design
The nonequivalent control group posttest-only design can be greatly improved if a pretest is given. When this is done, we have a nonequivalent control group pretest-posttest design, one of the most useful quasi-experimental designs. It can be diagrammed as follows:
This design is similar to the pretest-posttest design described in Chapter 8. However, this is not a true experimental design because assignment to groups is not random; the two groups may not be equivalent. We have the advantage, however, of knowing the pretest scores. Thus, we can see whether the groups were the same on the pretest. Even if the groups are not equivalent, we can look at changes in scores from the pretest to the posttest. If the independent variable has an effect, the experimental group should show a greater change than the control group (see Kenny, 1979).
An evaluation of National Alcohol Screening Day (NASD) provides an example of the use of a nonequivalent control group pretest-posttest design (Aseltine, Schilling, James, Murray, & Jacobs, 2008). NASD is a community-based program that provides free access to alcohol screening, a private meeting with a health professional to review the results, educational materials, and referral information if necessary. For the evaluation, NASD attendees at five community locations completed a baseline (pretest) measure of their recent alcohol consumption. This measure was administered as a posttest 3 months later. A control group was formed 1 week following NASD at the same locations using displays that invited people to take part in a health survey. These individuals completed the same pretest measure and were contacted in 3 months for the posttest. The data analysis focused on participants identified as at-risk drinkers; the NASD participants showed a significant decrease in alcohol consumption from pretest to posttest when compared with similar individuals in the control group.
Propensity Score Matching of Nonequivalent Treatment and Control Groups
The nonequivalent control group designs lack random assignment to conditions and so the groups may in fact differ in important ways. For example, people who decide to attend an alcohol screening event may differ from those who Page 232are interested in a health screening. Perhaps the people at the health screening are in fact healthier than the alcohol screening participants.
One approach to making the groups equivalent on a variable such as health is to match participants in the conditions on a measure of health (this is similar to matched pairs designs, covered in Chapter 8). The health measure can be administered to everyone in the treatment condition and all individuals who are included in the control condition. Now, each person in the treatment condition would be matched with a control individual who possesses an identical or highly similar health score. Once this has been done, the analysis of the dependent measure can take place. This procedure is most effective when the measure used for the matching is highly reliable and the individuals in the two conditions are known to be very similar. Nonetheless, it is still possible that the two groups are different on other variables that were not measured.
Advances in statistical methods have made it possible to simultaneously match individuals on multiple variables. Instead of matching on just one variable such as health, the researcher can obtain measures of other variables thought to be important when comparing the groups. The scores on these variables are combined to produce what is called a propensity score (the statistical procedure is beyond the scope of the book). Individuals in the treatment and control groups can then be matched on propensity scores—this process is called propensity score matching (Guo & Fraser, 2010; Shadish, Cook, & Campbell, 2002).
Interrupted Time Series Design and Control Series Design
Campbell (1969) discusses at length the evaluation of one specific legal reform: the 1955 crackdown on speeding in Connecticut. Although seemingly an event in the distant past, the example is still a good illustration of an important methodological issue. The crackdown was instituted after a record high number of traffic fatalities occurred in 1955. The easiest way to evaluate this reform is to compare the number of traffic fatalities in 1955 (before the crackdown) with the number of fatalities in 1956 (after the crackdown). Indeed, the number of traffic deaths fell from 324 in 1955 to 284 in 1956. This single comparison is really a one-group pretest-posttest design with all of that design’s problems of internal validity; there are many other reasons that traffic deaths might have declined. One alternative is to use an interrupted time series design that would examine the traffic fatality rates over an extended period of time, both before and after the reform was instituted. Figure 11.3 shows this information for the years 1951–1959. Campbell (1969) argues that the drop from 1955 to 1956 does not look particularly impressive, given the great fluctuations in previous years, but there is a steady downward trend in fatalities after the crackdown. Even here, however, Campbell sees a problem in interpretation. The drop could be due to statistical regression: Because 1955 was a record high year, the probability is that there would have been a drop anyway. Still, the data for the years extending before and after the crackdown allow for a less ambiguous interpretation than would be possible with data for only 1955 and 1956.
Connecticut traffic fatalities, 1951–1959
One way to improve the interrupted time series design is to find some kind of control group—a control series design. In the Connecticut speeding crackdown, this was possible because other states had not instituted the reform. Figure 11.4 shows the same data on traffic fatalities in Connecticut plus the fatality figures of four comparable states during the same years. The fact that the fatality rates in the control states remained relatively constant while those in Connecticut consistently declined led Campbell to conclude that the crackdown did indeed have some effect.
Control series design comparing Connecticut traffic fatality rate (solid color line) with the fatality rate of four comparable states (dotted black line)
DEVELOPMENTAL RESEARCH DESIGNS
Developmental psychologists often study the ways that individuals change as a function of age. A researcher might test a theory concerning changes in reasoning ability as children grow older, the age at which self-awareness develops in young children, or the global values people have as they move from adolescence through old age. In all cases, the major variable is age. Developmental researchers face an interesting choice in designing their studies because there are two general methods for studying individuals of different ages: the cross-sectional method and the longitudinal method. You will see that the cross-sectional method shares similarities with the independent groups design whereas the longitudinal method is similar to the repeated measures design. We will also examine a hybrid approach called the sequential method. The three approaches are illustrated in Figure 11.5.
In a study using the cross-sectional method, persons of different ages are studied at only one point in time. Suppose you are interested in examining how the ability to learn a computer application changes as people grow older. Using the cross-sectional method, you might study people who are currently 20, 30, 40, and 50 years of age. The participants in your study would be given the same computer learning task, and you would compare the groups on their performance.
Three designs for developmental research
Page 235In a recent study by Tymula, Belmaker, Ruderman, and Levy (2013), subjects in four age groups (12–17; 21–25; 30–50; 65–90) completed the same financial decision-making task. The task involved choosing among options with varying levels of risk and reward that led to an expected financial outcome for each subject. Individuals in the oldest age group made the poorest financial decisions with more inconsistent decisions and lower financial outcomes.
In the longitudinal method, the same group of people is observed at different points in time as they grow older. Perhaps the most famous longitudinal study is the Terman Life Cycle Study that was begun by Stanford psychologist Lewis Terman in 1921. Terman studied 1,528 California schoolchildren who had intelligence test scores of at least 135. The participants, who called themselves “Termites,” were initially measured on numerous aspects of their cognitive and social development in 1921 and 1922. Terman and his colleagues continued studying the Termites during their childhood and adolescence and throughout their adult lives (cf. Terman, 1925; Terman & Oden, 1947, 1959).
Terman’s successors at Stanford continue to track the Termites until each one dies. The study has provided a rich description of the lives of highly intelligent individuals and disconfirmed many negative stereotypes of high intelligence—for example, the Termites were very well adjusted both socially and emotionally. The data have now been archived for use by other researchers such as Friedman and Martin (2011), who used the Terman data to study whether personality and other factors are related to health and longevity. To complete their investigations, Friedman and Martin obtained death certificates of Terman participants to have precise data on both how long they lived and the causes of death. One strong pattern that emerged was that the personality dimension of “conscientiousness” (being self-disciplined, organized) that was measured in childhood was related to longevity. Of interest is that changes in personality qualities also affected longevity. Participants who had become less conscientious as adults had a reduction in longevity; those who became more conscientious as adults experienced longer lives. Another interesting finding concerned interacting with pets. Questions about animals were asked when participants were in their sixties; contrary to common beliefs, having or playing with pets was not related to longevity.
A unique longitudinal study on aging and Alzheimer’s disease called the Nun Study illustrates a different approach (Snowden, 1997). In 1991, all members of a particular religious order born prior to 1917 were asked to participate by providing access to their archived records as well as various annual medical and psychological measures taken over the course of the study. The Page 236sample consisted of 678 women with a mean age of 83. One fascinating finding from this study was based on autobiographies that all sisters wrote in 1930 (Danner, Snowden, & Friesen, 2001). The researchers devised a coding system to measure positive emotional content in the autobiographies. Greater positive emotions were strongly related to actual survival rate during the course of the study. Other longitudinal studies may study individuals over only a few years. For example, a 9-year study of U.S. children found a variety of impacts—positive and negative—of early non-maternal child care (NICHD Early Child Care Research Network, 2005).
Comparison of Longitudinal and Cross-Sectional Methods
The cross-sectional method is much more common than the longitudinal method primarily because it is less expensive and immediately yields results. Note that, with a longitudinal design, it would take 30 years to study the same group of individuals from age 20 to 50, but with a cross-sectional design, comparisons of different age groups can be obtained relatively quickly.
There are, however, some disadvantages to cross-sectional designs. Most important, the researcher must infer that differences among age groups are due to the developmental variable of age. The developmental change is not observed directly among the same group of people, but rather is based on comparisons among different cohorts of individuals. You can think of a cohort as a group of people born at about the same time, exposed to the same events in a society, and influenced by the same demographic trends such as divorce rates and family size. If you think about the hairstyles of people you know who are in their 30s, 40s, 50s, and 60s, you will immediately recognize the importance of cohort effects! More crucially, differences among cohorts reflect different economic and political conditions in society, different music and arts, different educational systems, and different child-rearing practices. In a cross-sectional study, a difference among groups of different ages may reflect developmental age changes; however, the differences may result from cohort effects (Schaie, 1986).
To illustrate this issue, let’s return to our hypothetical study on learning to use computers. Suppose you found that age is associated with a decrease in ability such that the people in the 50-year-old group score lower on the learning measure than the 40-year-olds, and so on. Should you conclude that the ability to learn to use a computer application decreases with age? That may be an accurate conclusion; alternatively, the differences could be due to a cohort effect: The older people had less experience with computers while growing up. The key point here is that the cross-sectional method confounds age and cohort effects. (Review the discussion of confounding and internal validity at the beginning of Chapter 8.) Finally, you should note that cohort effects are most likely to be a problem when the researcher is examining age effects across a wide range of ages (e.g., adolescents through older adults).
The only way to conclusively study changes that occur as people grow older is to use a longitudinal design. Also, longitudinal research is the best way Page 237to study how scores on a variable at one age are related to another variable at a later age. For example, researchers at the National Children’s Study (http://www.nationalchildrensstudy.gov) began collecting data in 2009 at 105 study locations across the United States. In each of those study sites, participants (new parents) are being recruited to participate in the study that will run from the birth of their child until the child is 21 years of age. The goal of the study is to better understand the interactions of the environment and genetics and their effects on child health and well-being. The alternative in this case would be to study samples of children of various ages and ask them or their parents about the earlier home environment; this retrospective approach has its own problems when one considers the difficulty of remembering events in the distant past.
Thus, the longitudinal approach, despite being expensive and difficult, has definite advantages. However, there is one major problem: Over the course of a longitudinal study, people may move, die, or lose interest in the study. Researchers who conduct longitudinal studies become adept at convincing people to continue, often travel anywhere to collect more data, and compare test scores of people who drop out with those who stay to provide better analyses of their results. In sum, a researcher should not embark on a longitudinal study without considerable resources and a great deal of patience and energy!
A compromise between the longitudinal and cross-sectional methods is to use the sequential method. This method, along with the cross-sectional and longitudinal methods, is illustrated in Figure 11.5. In the figure, the goal of the study is to minimally compare 55- and 65-year-olds. The first phase of the sequential method begins with the cross-sectional method; for example, you could study groups of 55- and 65-year-olds. These individuals are then studied using the longitudinal method with each individual tested at least one more time.
Orth, Trzesniewski, and Robins (2010) studied the development of self-esteem over time using just such a sequential method. Using data from the Americans’ Changing Lives study, Orth and his colleagues identified six different age cohorts (25–34, 35–44, 45–54, 55–64, 65–74, 75+) and examined their self-esteem ratings from 1986, 1989, 1994, and 2002. Thus, they were interested in changes in self-esteem for participants at various ages, over time. Their findings provide an interesting picture of how self-esteem changes over time: They found that self-esteem gradually increases from age 25 to around age 60 and then declines in later years. If this were conducted as a full longitudinal study, it would require 100 years to complete!
Clearly, this method takes fewer years and less effort to complete than a longitudinal study, and the researcher reaps immediate rewards because data on the different age groups are available in the first year of the study. On the other hand, the participants are not followed over the entire time span as they would be in a full longitudinal investigation; that is, no one in the Orth study was followed from age 25 to 100.
Page 238We have now described most of the major approaches to designing research. In the next two chapters, we consider methods of analyzing research data.
ILLUSTRATIVE ARTICLE: A QUASI-EXPERIMENT
Sexual violence on college and university campuses has been and continues to be a widespread problem. Programs designed to prevent sexual violence on campuses have shown mixed results: Some evidence suggests that they can be effective, but other evidence shows that they are not.
Banyard, Moynihan, and Crossman (2009) implemented a prevention program that utilized specific sub groups of campus communities to “raise awareness about the problem of sexual violence and build skill that individuals can use to end it.” They exposed dormitory resident advisors to a program called “Bringing in the Bystander” and assessed change in attitudes as well as a set of six outcome measures (e.g., willingness to help).
First, acquire and read the article:
Banyard, V. L., Moynihan, M. M., & Crossman, M. T. (2009). Reducing sexual violence on campus: The role of student leaders as empowered bystanders. Journal of College Student Development, 50, 446–457. doi:10.1353/csd.0.0083
Then, after reading the article, consider the following:
1. This study was a quasi-experiment. What is the specific design?
2. What are the potential weaknesses of the design?
3. The discussion of this article begins with this statement: “The results of this study are promising.” Do you agree or disagree? Support your position.
4. How would you determine if there is a need to address the problem of sexual violence on your campus? If you discover that there is a need, would the program described here be appropriate? Why or why not?
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The post . How would you determine if there is a need to address the problem of sexual violence on your campus? If you discover that there is a need, would the program described here be appropriate? Why or why not? first appeared on nursing writers.
The post . How would you determine if there is a need to address the problem of sexual violence on your campus? If you discover that there is a need, would the program described here be appropriate? Why or why not? appeared first on nursing writers.