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Some popular experimental designs are summarized in  Table 9.4 . The second column (schematic diagram) depicts design notation from a classic monograph (Campbell & Stanley, 1963). In this notation, R means random assignment, O represents observations (i.e., data collected on the outcome), and X stands for exposure to the intervention. Each row designates a different group, and time is portrayed moving from left to right. Thus, in Row 2 (a basic pretest–posttest design), the top line represents the group that was randomly assigned (R) to an intervention (X) and from which data were collected prior to (O1) and after (O2) the intervention. The second row is the control group, which differs from the experimental group only by absence of the treatment (no X). (Some entries in the “drawbacks” column of  Table 9.4  are not discussed until  Chapter 10 .)

TABLE 9.4: Design Alternatives: Selected Experimental (Randomized) Designs

TYPE OF DESIGN SCHEMATIC DIAGRAM SITUATIONS THAT ARE BEST SUITED TO THIS DESIGN DRAWBACKS OF THIS DESIGN
· 1. Basic posttest-only design When the outcome is not relevant until after the intervention is complete (e.g., length of stay in hospital) Does not permit an evaluation of whether the two groups were comparable at the outset on the outcome of interest
· 2. Basic pretest-posttest design (with optional repeated follow-ups) · a. When the focus of the intervention is on change (e.g., behaviors, attitudes)

· b. When the researcher wants to assess both group differences (experimental comparison), and change within groups (quasi-experimental)

Sometimes the pretest itself can affect the outcomes of interest
· 3. Multiple intervention design Can be used to disentangle effects of different components of a complex intervention, or to test competing interventions · a. Requires largersample than basic designs

· b. May be at risk to threats to statistical conclusion validity *  if A and B are not very different (small effects)

· 4. Wait-list (delay of treatment) design · a. Attractive when there is patient preference for the innovative treatment

· b. Can strengthen inferences by virtue of replication aspect for the second group

· a. Controls may drop out of study before they get deferred treatment

· b. Not suitable if key outcomes are measured long after treatment (e.g., mortality) or if there is an interest in assessing long-term effects (wait-list period is then too long)

· 5. Crossover design—participants serve as their own controls · a. Appropriate only if there is no expectation of carryover effects from one period to the next (effects should have rapid onset, short half-life)

· b. Useful when recruitment is difficult—smaller sample is needed; excellent for controlling confounding variables

· a. Often cannot be assumed that there are no carryover effects

· b. If the first treatment received “fixes” a problem for participants, they may not remain in the study for the second one

· c. History threat *  to intemal validity a possibility

· 6. Factorial design · a. Efficient for testing two interventions simultaneously

· b. Can be useful in illuminating interaction effects, but most useful when strong synergistic/additive effects (or no interaction effects) are expected

Power needed to detect interactions could require larger sample size than when testing each intervention separately
KEY: R = Randomization

X = Intervention (XA = one treatment, XB = alternative treatment, dose, etc.)

O = Observation or measurement of the dependent variable/outcome

*Validity threats are discussed in  Chapter 10 .

Basic Experimental Designs

Earlier in this chapter, we described a study that tested the effect of gentle massage on pain in nursing home residents. This example illustrates a simple design that is sometimes called a  posttest-only design (or  after-only design ) because data on the dependent variable are collected only once—after randomization and completion of the intervention.

A second basic design involves the collection of baseline data, as shown in the flowchart,  Figure 9.1 . Suppose we hypothesized that convective airflow blankets are more effective than conductive water-flow blankets in cooling critically ill febrile patients. Our design involves assigning patients to the two blanket types (the independent variable) and measuring the outcome (body temperature) twice, before and after the intervention. This design allows us to examine whether one blanket type is more effective than the other in reducing fever—that is, with this design researchers can examine change. This design is a  pretest–posttest design  or a  before–after design . Many pretest–posttest designs include data collection at multiple postintervention points (sometimes called repeated measures designs, as noted in  Chapter 8 ). Designs that involve collecting data multiple times from two groups are mixed designs: Analyses can examine both differences between groups and changes within groups over time.

These basic designs can be “tweaked” in various ways—for example, the design could involve comparison of three or more groups or could have a wait-listed control group. These designs are included in  Table 9.4 .

Example of a Pretest–Posttest Experimental Design: Zhu and co-researchers (2014) tested the effects of a transtheoretical model-based exercise intervention on exercise behavior and self-efficacy in patients with coronary heart disease. The outcomes were measured at baseline and at a 3-month and 6-month follow-up.

Factorial Design

Most experimental designs involve manipulating only one independent variable and randomizing participants to different treatment groups—these are sometimes called parallel-group designs. It is possible, however, to manipulate two or more variables simultaneously. Suppose we wanted to compare two therapies for premature infants: tactile stimulation versus auditory stimulation. We also want to learn if the daily amount of stimulation (15, 30, or 45 minutes) affects infants’ progress. The outcomes are measures of infant development (e.g., weight gain, cardiac responsiveness).  Figure 9.2  illustrates the structure of this RCT.

FIGURE 9.2

Example of a 2 × 3 factorial design.

This  factorial design  allows us to address three research questions:

· 1. Does auditory stimulation have a more beneficial effect on premature infants’ development than tactile stimulation, or vice versa?

· 2. Is the duration of stimulation (independent of type) related to infant development?

· 3. Is auditory stimulation most effective when linked to a certain dose and tactile stimulation most effective when coupled with a different dose?

The third question shows the strength of factorial designs: They permit us to test not only  main effects (effects from experimentally manipulated variables, as in questions 1 and 2) but also  interaction effects (effects from combining treatments). Our results may indicate that 30 minutes of auditory stimulation is the most beneficial treatment. We could not have learned this by conducting two separate studies that manipulated one independent variable and held the second one constant.

In factorial experiments, people are randomly assigned to a specific combination of conditions. In our example ( Figure 9.2 ), infants would be assigned randomly to one of six  cells —that is, six treatment conditions. The two independent variables in a factorial design are the factors. Type of stimulation is factor A, and amount of daily exposure is factor B. Level 1 of factor A is auditory, and level 2 of factor A is tactile. When describing the dimensions of the design, researchers refer to the number of levels. The design in  Figure 9.2  is a 2 × 3 design: two levels in factor A times three levels in factor B. Factorial experiments with more than two factors are rare.

Example of a Factorial Design: Mosleh and colleagues (2014) used a factorial design in their study of communications to improve attendance in cardiac rehabilitation. In their 2 × 2 design, one factor was a standard invitation letter versus a letter with wording based on the Theory of Planned Behavior. The second factor was the inclusion or noninclusion of a leaflet with motivational messages.

Crossover Design

Thus far, we have described RCTs in which different people are randomly assigned to different conditions. For instance, in the previous example, infants exposed to auditory stimulation were not the same infants as those exposed to tactile stimulation. A  crossover design  involves exposing the same people to more than one condition. This type of within-subjects design has the advantage of ensuring the highest possible equivalence among participants exposed to different conditions—the groups being compared are equal with respect to age, weight, health, and so on because they are composed of the same people.

Because randomization is a signature characteristic of an experiment, participants in a crossover design must be randomly assigned to different orderings of treatments. For example, if a crossover design were used to compare the effects of auditory and tactile stimulation on infant development, some infants would be randomly assigned to receive auditory stimulation first, and others would be assigned to receive tactile stimulation first. When there are three or more conditions to which participants will be exposed, the procedure of  counterbalancing  can be used to rule out ordering effects. For example, if there were three conditions (A, B, C), participants would be randomly assigned to one of six counterbalanced orderings:

A, B, C A, C, B
B, C, A B, A, C
C, A, B C, B, A

Although crossover designs are extremely powerful, they are inappropriate for certain research questions because of the problem of carryover effects. When people are exposed to two different treatments or conditions, they may be influenced in the second condition by their experience in the first condition. As one example, drug studies rarely use a crossover design because drug B administered after drug A is not necessarily the same treatment as drug B administered before drug A. When carryover effects are a potential concern, researchers often have a washout period in between the treatments (i.e., a period of no treatment exposure).

Example of a Crossover Design: Lippoldt and colleagues (2014) used a randomized crossover design with a sample of healthy adults to test the effects of different bedrest elevations and different types of mattresses on peak interface pressures.

Strengths and Limitations of Experiments

In this section, we explore the reasons why experimental designs are held in high esteem and examine some limitations.

Experimental Strengths

An experimental design is the gold standard for testing interventions because it yields strong evidence about intervention effectiveness. Experiments offer greater corroboration than any other approach that, if the independent variable (e.g., diet, drug, teaching approach) is varied, then certain consequences in the outcomes (e.g., weight loss, recovery, learning) are likely to ensue. The great strength of RCTs, then, lies in the confidence with which causal relationships can be inferred. Through the controls imposed by manipulation, comparison, and randomization, alternative explanations can be discredited. It is because of these strengths that meta-analyses of RCTs, which integrate evidence from multiple experimental studies, are at the pinnacle of evidence hierarchies for questions about treatment effects (see  Figure 2.1 ).

Experimental Limitations

Despite the benefits of experiments, this type of design also has limitations. First, there are often constraints that make an experimental approach impractical or impossible. These constraints are discussed later in this chapter.

TIP: Shadish and colleagues (2002) described 10 situations that are especially conducive to randomized experiments; these are summarized in a table in the Toolkit.

Experiments are sometimes criticized for their artificiality, which partly stems from the requirements for comparable treatment within randomized groups, with strict adherence to protocols. In ordinary life, by contrast, we interact with people in non-formulaic ways. Another criticism is the focus on only a handful of variables while holding all else constant—a requirement that has been criticized as artificially constraining human experience. Experiments that are undertaken without a guiding theoretical framework are sometimes criticized for suggesting causal connections without any explanation for whythe intervention might affect outcomes.

A problem with RCTs conducted in clinical settings is that it is often clinical staff, rather than researchers, who administer an intervention, and therefore, it can sometimes be difficult to ascertain whether those in the intervention group actually received the treatment as specified and if those in the control group did not. Clinical studies are conducted in environments over which researchers may have little control—and control is a critical factor in RCTs. McGuire and colleagues (2000) have described some issues relating to the challenges of testing interventions in clinical settings.

Sometimes problems emerge when participants can “opt out” of the intervention. Suppose, for example, that we randomly assigned patients with HIV infection to a special support group intervention or to a control group. Intervention subjects who elect not to participate in the support groups, or who participate infrequently, actually are in a “condition” that looks more like the control condition than the experimental one. The treatment is diluted through nonparticipation, and it may become difficult to detect any treatment effects, no matter how effective it might otherwise have been. We discuss this at greater length in the next chapter.

Another potential problem is the  Hawthorne effect , a placebo-type effect caused by people’s expectations. The term is derived from a series of experiments conducted at the Hawthorne plant of the Western Electric Corporation in which various environmental conditions, such as light and working hours, were varied to test their effects on worker productivity. Regardless of what change was introduced, that is, whether the light was made better or worse, productivity increased. Knowledge of being included in the study (not just knowledge of being in a particular group) appears to have affected people’s behavior, obscuring the effect of the treatments.

In sum, despite the superiority of RCTs for testing causal hypotheses, they are subject to a number of limitations, some of which may make them difficult to apply to real-world problems. Nevertheless, with the growing demand for evidence-based practice, true experimental designs are increasingly being used to test the effects of nursing interventions.

QUASI-EXPERIMENTS

Quasi-experiments, often called controlled trials without randomization in the medical literature, involve an intervention but they lack randomization, the signature of a true experiment. Some quasi-experiments even lack a control group. The signature of a quasi-experimental design, then, is an intervention in the absence of randomization.

Quasi-Experimental Designs

The most widely used quasi-experimental designs are summarized in  Table 9.5 , which depicts designs using the schematic notation we introduced earlier.

TABLE 9.5: Design Alternatives: Selected Quasi-Experimental Designs

TYPE OF DESIGN SCHEMATIC DIAGRAM SITUATIONS THAT ARE BEST SUITED DRAWBACKS
· 1.Nonequivalent control group, pretest-posttest design Attractive when an entire unit must get the intervention and a similar unit not getting the intervention is available · a. Selection threat * remains a nearly intractable problem, but less so than when there is no pretest

· b. History threat *  also a possibility

· 2.Nonequivalent control group, posttest-only design A reasonable choice only when there is some a priori knowledge about comparability of groups with regard to key outcomes Extremely vulnerable to selection threat, * possibility of other threats as well, especially history threat *
· 3. One-group pretest-posttest design A reasonable choice only when intervention impact is expected to be dramatic and other potential causes have little credibility Typically provides very weak support for causal inference—vulnerable to many internal validity threats (maturation, history, etc.) *
· 4. Time series design · a. Good option when there are abundant data on key outcome in existing records

· b. Addresses maturation threat and change from secular trends and random fluctuation

· a. Complex statistical analysis that is most appropriate with very large number of data points (100+)

· b. History threat *  remains, and (sometimes) selection threat *  if the population changes over time

· 5. Time series nonequivalent control group design Attractive when an entire unit/institution adopts the intervention and a similar unit not adopting it is available, and if comparable data are readily available in records of both · a. Selection threat * remains, as two units or institutions are rarely identical

· b. Analyses may be very complex

· 6. Time series with withdrawn and reinstituted treatment * Attractive if effects of an intervention are short-term · a. May be untenable to assume that there are no carryover effects

· b. May be difficult ethically to withdraw treatment if it is efficacious

KEY: X = Intervention

O = Observation or measurement of the dependent variable/outcome

*Validity threats are discussed in  Chapter 10 .

Nonequivalent Control Group Designs

The  nonequivalent control group pretest–posttest design  involves two groups of participants, for whom outcomes are measured before and after the intervention. For example, suppose we wished to study the effect of a new chair yoga intervention for older people. The intervention is being offered to everyone at a community senior center, and randomization is not possible. For comparative purposes, we collect outcome data in a different community senior center that is not instituting the intervention. Data on quality of life are collected from both groups at baseline and again 10 weeks after its implementation in one of the centers.

The first row of  Table 9.5  depicts this study. The top line represents those receiving the intervention at the experimental site and the second row represents the elders at the comparison site. This diagram is identical to the experimental pretest–posttest design (second row of  Table 9.4 except there is no “R”—participants have not been randomized to groups. The design in  Table 9.5  is weaker because it cannot be assumed that the experimental and comparison groups are initially equivalent. Because there is no randomization, quasi-experimental comparisons are farther from an ideal counterfactual than experimental comparisons. The design is nevertheless strong because baseline data allow us to assess whether patients in the two centers had similar levels of quality of life at the outset. If the two groups are similar, on average, at baseline, we could be relatively confident inferring that any posttest difference in outcomes was the result of the yoga intervention. If quality of life scores are different initially, however, it will be difficult to interpret posttest differences. Note that in quasi-experiments, the term  comparison group  is often used in lieu of control group to refer to the group against which treatment group outcomes are evaluated.

Now suppose we had been unable to collect baseline data. This design, diagrammed in Row 2 of  Table 9.5 , has a major flaw. We no longer have information about initial equivalence of people in the two centers. If quality of life in the experimental senior center is higher than that in the comparison site at posttest, can we conclude that the intervention caused improved quality of life? An alternative explanation for posttest differences is that the elders in the two centers differed at the outset. Campbell and Stanley (1963) called this nonequivalent control group posttest-only design preexperimental rather than quasi-experimental because of its fundamental weakness—although Shadish and colleagues (2002), in their more recent book on causal inference, simply called this a weaker quasi-experimental design.

Example of a Nonequivalent Control Group Pretest–Posttest Design: Wang and co-researchers (2014) assessed the efficacy of narrowband ultraviolet B phototherapy in reducing renal pruritus in patients undergoing hemodialysis. Two groups were compared based on dates of receiving hemodialysis. One nonrandomized group received the intervention three times per week for 2 weeks, and the control group received usual care. Pruritus intensity was measured at baseline and on six subsequent occasions.

Sometimes researchers use matching in a pretest–posttest nonequivalent control group design to ensure that the groups are, in fact, equivalent on at least some key variables related to the outcomes. For example, if an intervention was designed to reduce patient anxiety, then it might be desirable to not only measure preintervention anxiety in the intervention and comparison group, but to take steps to ensure that the groups’ anxiety levels were comparable by matching participants’ initial anxiety. Because matching on more than one or two variables is unwieldy, a more sophisticated method of matching, called propensity matching, can be used by researchers with statistical sophistication. This method involves the creation of a single  propensity score  that captures the conditional probability of exposure to a treatment given various pre-intervention characteristics. Experimental and comparison group members can then be matched on this score (Qin et al., 2008). Both conventional and propensity matching are most easily implemented when there is a large pool of potential comparison group participants from which good matches to treatment group members can be selected.

In lieu of using a contemporaneous comparison group, researchers sometimes use a  historical comparison group . That is, comparison data are gathered before implementing the intervention. Even when the people are from the same institutional setting, however, it is risky to assume that the two groups are comparable, or that the environments are comparable in all respects except for the new intervention. There remains the possibility that something other than the intervention could account for observed differences in outcomes.

Example of a Historical Comparison Group: Cutler and Sluman (2014) assessed the effect of new oral hygiene protocols on the rates of ventilator-associated pneumonia (VAP) in a critical care unit. The incidence of VAP in 559 patients after the practice change was compared to that for 528 patients before the change.

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