A Modern Guide to Understanding and Conducting Research in Psychology

Chapter 3 experimental research.

In the late 1960s social psychologists John Darley and Bibb Latané proposed a counterintuitive hypothesis. The more witnesses there are to an accident or a crime, the less likely any of them is to help the victim ( Darley & Latané, 1968 ) . They also suggested the theory that this happens because each witness feels less responsible for helping—a process referred to as the “diffusion of responsibility.” Darley and Latané noted that their ideas were consistent with many real-world cases. For example, a New York woman named Kitty Genovese was assaulted and murdered while several witnesses failed to help. But Darley and Latané also understood that such isolated cases did not provide convincing evidence for their hypothesized “bystander effect.” There was no way to know, for example, whether any of the witnesses to Kitty Genovese’s murder would have helped had there been fewer of them.

So to test their hypothesis, Darley and Latané created a simulated emergency situation in a laboratory. Each of their college student participants was isolated in a small room and told that he or she would be having a discussion about college life with other students via an intercom system. Early in the discussion, however, one of the students began having what seemed to be an epileptic seizure. Over the intercom came the following: “I could really-er-use some help so if somebody would-er-give me a little h-help-uh-er-er-er-er-er c-could somebody-er-er-help-er-uh-uh-uh (choking sounds)…I’m gonna die-er-er-I’m…gonna die-er-help-er-er-seizure-er- [chokes, then quiet]” ( Darley & Latané, 1968, p. 379 ) .

In actuality, there were no other students. These comments had been prerecorded and were played back to create the appearance of a real emergency. The key to the study was that some participants were told that the discussion involved only one other student (the victim), others were told that it involved two other students, and still others were told that it included five other students. Because this was the only difference between these three groups of participants, any difference in their tendency to help the victim would have to have been caused by it. And sure enough, the likelihood that the participant left the room to seek help for the “victim” decreased from 85% to 62% to 31% as the number of “witnesses” increased.

The Parable of the 38 Witnesses

The story of Kitty Genovese has been told and retold in numerous psychology textbooks. The standard version is that there were 38 witnesses to the crime, that all of them watched (or listened) for an extended period of time, and that none of them did anything to help. However, recent scholarship suggests that the standard story is inaccurate in many ways ( Manning et al., 2007 ) . For example, only six eyewitnesses testified at the trial, none of them was aware that he or she was witnessing a lethal assault, and there have been several reports of witnesses calling the police or even coming to the aid of Kitty Genovese. Although the standard story inspired a long line of research on the bystander effect and the diffusion of responsibility, it may also have directed researchers’ and students’ attention away from other equally interesting and important issues in the psychology of helping—including the conditions in which people do in fact respond collectively to emergency situations.

The study that Darley and Latané conducted was a particular kind of study called an experiment. Experiments are used to determine not only whether there is a statistical relationship between two variables but also whether the relationship is a causal one. For this reason, experiments are one of the most common and useful tools in the psychological researcher’s toolbox. In this chapter, we look at experiments in detail. We consider first what sets experiments apart from other kinds of studies and why they support causal conclusions while other kinds of studies do not. We then look at two basic ways of designing an experiment—between-subjects designs and within-subjects designs—and discuss their pros and cons. Finally, we consider several important practical issues that arise when conducting experiments.

3.1 Experiment Basics

Learning objectives.

  • Explain what an experiment is and recognize examples of studies that are experiments and studies that are not experiments.
  • Explain what internal validity is and why experiments are considered to be high in internal validity.
  • Explain what external validity is and evaluate studies in terms of their external validity.
  • Distinguish between the manipulation of the independent variable and control of extraneous variables and explain the importance of each.
  • Recognize examples of confounding variables and explain how they affect the internal validity of a study.

What Is an Experiment?

As we saw earlier in the book, an experiment is a type of study designed specifically to answer the question of whether there is a causal relationship between two variables. Do changes in an independent variable cause changes in a dependent variable? Experiments have two fundamental features. The first is that the researchers manipulate, or systematically vary, the level of the independent variable. The different levels of the independent variable are called conditions. For example, in Darley and Latané’s experiment, the independent variable was the number of witnesses that participants believed to be present. The researchers manipulated this independent variable by telling participants that there were either one, two, or five other students involved in the discussion, thereby creating three conditions. The second fundamental feature of an experiment is that the researcher controls, or minimizes the variability in, variables other than the independent and dependent variable. These other variables are called extraneous variables. Darley and Latané tested all their participants in the same room, exposed them to the same emergency situation, and so on. They also randomly assigned their participants to conditions so that the three groups would be similar to each other to begin with. Notice that although the words manipulation and control have similar meanings in everyday language, researchers make a clear distinction between them. They manipulate the independent variable by systematically changing its levels and control other variables by holding them constant.

Internal and External Validity

Internal validity.

Recall that the fact that two variables are statistically related does not necessarily mean that one causes the other. “Correlation does not imply causation.” For example, if it were the case that people who exercise regularly are happier than people who do not exercise regularly, this would not necessarily mean that exercising increases people’s happiness. It could mean instead that greater happiness causes people to exercise (the directionality problem) or that something like better physical health causes people to exercise and be happier (the third-variable problem).

The purpose of an experiment, however, is to show that two variables are statistically related and to do so in a way that supports the conclusion that the independent variable caused any observed differences in the dependent variable. The basic logic is this: If the researcher creates two or more highly similar conditions and then manipulates the independent variable to produce just one difference between them, then any later difference between the conditions must have been caused by the independent variable. For example, because the only difference between Darley and Latané’s conditions was the number of students that participants believed to be involved in the discussion, this must have been responsible for differences in helping between the conditions.

An empirical study is said to be high in internal validity if the way it was conducted supports the conclusion that the independent variable caused any observed differences in the dependent variable. Thus experiments are high in internal validity because the way they are conducted—with the manipulation of the independent variable and the control of extraneous variables—provides strong support for causal conclusions.

External Validity

At the same time, the way that experiments are conducted sometimes leads to a different kind of criticism. Specifically, the need to manipulate the independent variable and control extraneous variables means that experiments are often conducted under conditions that seem artificial or unlike “real life” ( Stanovich, 2013 ) . In many psychology experiments, the participants are all college undergraduates and come to a classroom or laboratory to fill out a series of paper-and-pencil questionnaires or to perform a carefully designed computerized task. Consider, for example, an experiment in which researcher Barbara Fredrickson and her colleagues had college students come to a laboratory on campus and complete a math test while wearing a swimsuit ( Fredrickson et al., 1998 ) . At first, this might seem silly. When will college students ever have to complete math tests in their swimsuits outside of this experiment?

The issue we are confronting is that of external validity. An empirical study is high in external validity if the way it was conducted supports generalizing the results to people and situations beyond those actually studied. As a general rule, studies are higher in external validity when the participants and the situation studied are similar to those that the researchers want to generalize to. Imagine, for example, that a group of researchers is interested in how shoppers in large grocery stores are affected by whether breakfast cereal is packaged in yellow or purple boxes. Their study would be high in external validity if they studied the decisions of ordinary people doing their weekly shopping in a real grocery store. If the shoppers bought much more cereal in purple boxes, the researchers would be fairly confident that this would be true for other shoppers in other stores. Their study would be relatively low in external validity, however, if they studied a sample of college students in a laboratory at a selective college who merely judged the appeal of various colors presented on a computer screen. If the students judged purple to be more appealing than yellow, the researchers would not be very confident that this is relevant to grocery shoppers’ cereal-buying decisions.

We should be careful, however, not to draw the blanket conclusion that experiments are low in external validity. One reason is that experiments need not seem artificial. Consider that Darley and Latané’s experiment provided a reasonably good simulation of a real emergency situation. Or consider field experiments that are conducted entirely outside the laboratory. In one such experiment, Robert Cialdini and his colleagues studied whether hotel guests choose to reuse their towels for a second day as opposed to having them washed as a way of conserving water and energy ( Cialdini, 2005 ) . These researchers manipulated the message on a card left in a large sample of hotel rooms. One version of the message emphasized showing respect for the environment, another emphasized that the hotel would donate a portion of their savings to an environmental cause, and a third emphasized that most hotel guests choose to reuse their towels. The result was that guests who received the message that most hotel guests choose to reuse their towels reused their own towels substantially more often than guests receiving either of the other two messages. Given the way they conducted their study, it seems very likely that their result would hold true for other guests in other hotels.

A second reason not to draw the blanket conclusion that experiments are low in external validity is that they are often conducted to learn about psychological processes that are likely to operate in a variety of people and situations. Let us return to the experiment by Fredrickson and colleagues. They found that the women in their study, but not the men, performed worse on the math test when they were wearing swimsuits. They argued that this was due to women’s greater tendency to objectify themselves—to think about themselves from the perspective of an outside observer—which diverts their attention away from other tasks. They argued, furthermore, that this process of self-objectification and its effect on attention is likely to operate in a variety of women and situations—even if none of them ever finds herself taking a math test in her swimsuit.

Manipulation of the Independent Variable

Again, to manipulate an independent variable means to change its level systematically so that different groups of participants are exposed to different levels of that variable, or the same group of participants is exposed to different levels at different times. For example, to see whether expressive writing affects people’s health, a researcher might instruct some participants to write about traumatic experiences and others to write about neutral experiences. The different levels of the independent variable are referred to as conditions , and researchers often give the conditions short descriptive names to make it easy to talk and write about them. In this case, the conditions might be called the “traumatic condition” and the “neutral condition.”

Notice that the manipulation of an independent variable must involve the active intervention of the researcher. Comparing groups of people who differ on the independent variable before the study begins is not the same as manipulating that variable. For example, a researcher who compares the health of people who already keep a journal with the health of people who do not keep a journal has not manipulated this variable and therefore not conducted an experiment. This is important because groups that already differ in one way at the beginning of a study are likely to differ in other ways too. For example, people who choose to keep journals might also be more conscientious, more introverted, or less stressed than people who do not. Therefore, any observed difference between the two groups in terms of their health might have been caused by whether or not they keep a journal, or it might have been caused by any of the other differences between people who do and do not keep journals. Thus the active manipulation of the independent variable is crucial for eliminating the third-variable problem.

Of course, there are many situations in which the independent variable cannot be manipulated for practical or ethical reasons and therefore an experiment is not possible. For example, whether or not people have a significant early illness experience cannot be manipulated, making it impossible to do an experiment on the effect of early illness experiences on the development of hypochondriasis. This does not mean it is impossible to study the relationship between early illness experiences and hypochondriasis—only that it must be done using nonexperimental approaches. We will discuss this in detail later in the book.

In many experiments, the independent variable is a construct that can only be manipulated indirectly. For example, a researcher might try to manipulate participants’ stress levels indirectly by telling some of them that they have five minutes to prepare a short speech that they will then have to give to an audience of other participants. In such situations, researchers often include a manipulation check in their procedure. A manipulation check is a separate measure of the construct the researcher is trying to manipulate. For example, researchers trying to manipulate participants’ stress levels might give them a paper-and-pencil stress questionnaire or take their blood pressure—perhaps right after the manipulation or at the end of the procedure—to verify that they successfully manipulated this variable.

Control of Extraneous Variables

An extraneous variable is anything that varies in the context of a study other than the independent and dependent variables. In an experiment on the effect of expressive writing on health, for example, extraneous variables would include participant variables (individual differences) such as their writing ability, their diet, and their shoe size. They would also include situation or task variables such as the time of day when participants write, whether they write by hand or on a computer, and the weather. Extraneous variables pose a problem because many of them are likely to have some effect on the dependent variable. For example, participants’ health will be affected by many things other than whether or not they engage in expressive writing. This can make it difficult to separate the effect of the independent variable from the effects of the extraneous variables, which is why it is important to control extraneous variables by holding them constant.

Extraneous Variables as “Noise”

Extraneous variables make it difficult to detect the effect of the independent variable in two ways. One is by adding variability or “noise” to the data. Imagine a simple experiment on the effect of mood (happy vs. sad) on the number of happy childhood events people are able to recall. Participants are put into a negative or positive mood (by showing them a happy or sad video clip) and then asked to recall as many happy childhood events as they can. The two leftmost columns of Table 3.1 show what the data might look like if there were no extraneous variables and the number of happy childhood events participants recalled was affected only by their moods. Every participant in the happy mood condition recalled exactly four happy childhood events, and every participant in the sad mood condition recalled exactly three. The effect of mood here is quite obvious. In reality, however, the data would probably look more like those in the two rightmost columns of Table 3.1 . Even in the happy mood condition, some participants would recall fewer happy memories because they have fewer to draw on, use less effective strategies, or are less motivated. And even in the sad mood condition, some participants would recall more happy childhood memories because they have more happy memories to draw on, they use more effective recall strategies, or they are more motivated. Although the mean difference between the two groups is the same as in the idealized data, this difference is much less obvious in the context of the greater variability in the data. Thus one reason researchers try to control extraneous variables is so their data look more like the idealized data in Table 3.1 , which makes the effect of the independent variable is easier to detect (although real data never look quite that good).

One way to control extraneous variables is to hold them constant. This can mean holding situation or task variables constant by testing all participants in the same location, giving them identical instructions, treating them in the same way, and so on. It can also mean holding participant variables constant. For example, many studies of language limit participants to right-handed people, who generally have their language areas isolated in their left cerebral hemispheres. Left-handed people are more likely to have their language areas isolated in their right cerebral hemispheres or distributed across both hemispheres, which can change the way they process language and thereby add noise to the data.

In principle, researchers can control extraneous variables by limiting participants to one very specific category of person, such as 20-year-old, straight, female, right-handed, sophomore psychology majors. The obvious downside to this approach is that it would lower the external validity of the study—in particular, the extent to which the results can be generalized beyond the people actually studied. For example, it might be unclear whether results obtained with a sample of younger straight women would apply to older gay men. In many situations, the advantages of a diverse sample outweigh the reduction in noise achieved by a homogeneous one.

Extraneous Variables as Confounding Variables

The second way that extraneous variables can make it difficult to detect the effect of the independent variable is by becoming confounding variables . A confounding variable is an extraneous variable that differs on average across levels of the independent variable. For example, in almost all experiments, participants’ intelligence quotients (IQs) will be an extraneous variable. But as long as there are participants with lower and higher IQs at each level of the independent variable so that the average IQ is roughly equal, then this variation is probably acceptable (and may even be desirable). What would be bad, however, would be for participants at one level of the independent variable to have substantially lower IQs on average and participants at another level to have substantially higher IQs on average. In this case, IQ would be a confounding variable.

To confound means to confuse, and this is exactly what confounding variables do. Because they differ across conditions—just like the independent variable—they provide an alternative explanation for any observed difference in the dependent variable. Figure 3.1 shows the results of a hypothetical study, in which participants in a positive mood condition scored higher on a memory task than participants in a negative mood condition. But if IQ is a confounding variable—with participants in the positive mood condition having higher IQs on average than participants in the negative mood condition—then it is unclear whether it was the positive moods or the higher IQs that caused participants in the first condition to score higher. One way to avoid confounding variables is by holding extraneous variables constant. For example, one could prevent IQ from becoming a confounding variable by limiting participants only to those with IQs of exactly 100. But this approach is not always desirable for reasons we have already discussed. A second and much more general approach—random assignment to conditions—will be discussed in detail shortly.

Hypothetical results from a study on the effect of mood on memory. Because IQ also differs across conditions, it is a confounding variable.

Figure 3.1: Hypothetical results from a study on the effect of mood on memory. Because IQ also differs across conditions, it is a confounding variable.

KEY TAKEAWAYS

  • An experiment is a type of empirical study that features the manipulation of an independent variable, the measurement of a dependent variable, and control of extraneous variables.
  • Studies are high in internal validity to the extent that the way they are conducted supports the conclusion that the independent variable caused any observed differences in the dependent variable. Experiments are generally high in internal validity because of the manipulation of the independent variable and control of extraneous variables.
  • Studies are high in external validity to the extent that the result can be generalized to people and situations beyond those actually studied. Although experiments can seem “artificial”—and low in external validity—it is important to consider whether the psychological processes under study are likely to operate in other people and situations.
  • Practice: List five variables that can be manipulated by the researcher in an experiment. List five variables that cannot be manipulated by the researcher in an experiment.
  • Effect of parietal lobe damage on people’s ability to do basic arithmetic.
  • Effect of being clinically depressed on the number of close friendships people have.
  • Effect of group training on the social skills of teenagers with Asperger’s syndrome.
  • Effect of paying people to take an IQ test on their performance on that test.

3.2 Experimental Design

  • Explain the difference between between-subjects and within-subjects experiments, list some of the pros and cons of each approach, and decide which approach to use to answer a particular research question.
  • Define random assignment, distinguish it from random sampling, explain its purpose in experimental research, and use some simple strategies to implement it.
  • Define what a control condition is, explain its purpose in research on treatment effectiveness, and describe some alternative types of control conditions.
  • Define several types of carryover effect, give examples of each, and explain how counterbalancing helps to deal with them.

In this section, we look at some different ways to design an experiment. The primary distinction we will make is between approaches in which each participant experiences one level of the independent variable and approaches in which each participant experiences all levels of the independent variable. The former are called between-subjects experiments and the latter are called within-subjects experiments.

Between-Subjects Experiments

In a between-subjects experiment , each participant is tested in only one condition. For example, a researcher with a sample of 100 college students might assign half of them to write about a traumatic event and the other half write about a neutral event. Or a researcher with a sample of 60 people with severe agoraphobia (fear of open spaces) might assign 20 of them to receive each of three different treatments for that disorder. It is essential in a between-subjects experiment that the researcher assign participants to conditions so that the different groups are, on average, highly similar to each other. Those in a trauma condition and a neutral condition, for example, should include a similar proportion of men and women, and they should have similar average intelligence quotients (IQs), similar average levels of motivation, similar average numbers of health problems, and so on. This is a matter of controlling these extraneous participant variables across conditions so that they do not become confounding variables.

Random Assignment

The primary way that researchers accomplish this kind of control of extraneous variables across conditions is called random assignment , which means using a random process to decide which participants are tested in which conditions. Do not confuse random assignment with random sampling. Random sampling is a method for selecting a sample from a population, and it is rarely used in psychological research. Random assignment is a method for assigning participants in a sample to the different conditions, and it is an important element of all experimental research in psychology and other fields too.

In its strictest sense, random assignment should meet two criteria. One is that each participant has an equal chance of being assigned to each condition (e.g., a 50% chance of being assigned to each of two conditions). The second is that each participant is assigned to a condition independently of other participants. Thus one way to assign participants to two conditions would be to flip a coin for each one. If the coin lands heads, the participant is assigned to Condition A, and if it lands tails, the participant is assigned to Condition B. For three conditions, one could use a computer to generate a random integer from 1 to 3 for each participant. If the integer is 1, the participant is assigned to Condition A; if it is 2, the participant is assigned to Condition B; and if it is 3, the participant is assigned to Condition C. In practice, a full sequence of conditions—one for each participant expected to be in the experiment—is usually created ahead of time, and each new participant is assigned to the next condition in the sequence as he or she is tested. When the procedure is computerized, the computer program often handles the random assignment.

One problem with coin flipping and other strict procedures for random assignment is that they are likely to result in unequal sample sizes in the different conditions. Unequal sample sizes are generally not a serious problem, and you should never throw away data you have already collected to achieve equal sample sizes. However, for a fixed number of participants, it is statistically most efficient to divide them into equal-sized groups. It is standard practice, therefore, to use a kind of modified random assignment that keeps the number of participants in each group as similar as possible. One approach is block randomization . In block randomization, all the conditions occur once in the sequence before any of them is repeated. Then they all occur again before any of them is repeated again. Within each of these “blocks,” the conditions occur in a random order. Again, the sequence of conditions is usually generated before any participants are tested, and each new participant is assigned to the next condition in the sequence. Table 3.2 shows such a sequence for assigning nine participants to three conditions. The Research Randomizer website ( http://www.randomizer.org ) will generate block randomization sequences for any number of participants and conditions. Again, when the procedure is computerized, the computer program often handles the block randomization.

Random assignment is not guaranteed to control all extraneous variables across conditions. It is always possible that just by chance, the participants in one condition might turn out to be substantially older, less tired, more motivated, or less depressed on average than the participants in another condition. However, there are some reasons that this is not a major concern. One is that random assignment works better than one might expect, especially for large samples. Another is that the inferential statistics that researchers use to decide whether a difference between groups reflects a difference in the population takes the “fallibility” of random assignment into account. Yet another reason is that even if random assignment does result in a confounding variable and therefore produces misleading results, this is likely to be detected when the experiment is replicated. The upshot is that random assignment to conditions—although not infallible in terms of controlling extraneous variables—is always considered a strength of a research design.

Treatment and Control Conditions

Between-subjects experiments are often used to determine whether a treatment works. In psychological research, a treatment is any intervention meant to change people’s behavior for the better. This includes psychotherapies and medical treatments for psychological disorders but also interventions designed to improve learning, promote conservation, reduce prejudice, and so on. To determine whether a treatment works, participants are randomly assigned to either a treatment condition , in which they receive the treatment, or a control condition , in which they do not receive the treatment. If participants in the treatment condition end up better off than participants in the control condition—for example, they are less depressed, learn faster, conserve more, express less prejudice—then the researcher can conclude that the treatment works. In research on the effectiveness of psychotherapies and medical treatments, this type of experiment is often called a randomized clinical trial .

There are different types of control conditions. In a no-treatment control condition , participants receive no treatment whatsoever. One problem with this approach, however, is the existence of placebo effects. A placebo is a simulated treatment that lacks any active ingredient or element that should make it effective, and a placebo effect is a positive effect of such a treatment. Many folk remedies that seem to work—such as eating chicken soup for a cold or placing soap under the bedsheets to stop nighttime leg cramps—are probably nothing more than placebos. Although placebo effects are not well understood, they are probably driven primarily by people’s expectations that they will improve. Having the expectation to improve can result in reduced stress, anxiety, and depression, which can alter perceptions and even improve immune system functioning ( Price et al., 2008 ) .

Placebo effects are interesting in their own right (see box “The Powerful Placebo”), but they also pose a serious problem for researchers who want to determine whether a treatment works. Figure 3.2 shows some hypothetical results in which participants in a treatment condition improved more on average than participants in a no-treatment control condition. If these conditions (the two leftmost bars in 3.2 ) were the only conditions in this experiment, however, one could not conclude that the treatment worked. It could be instead that participants in the treatment group improved more because they expected to improve, while those in the no-treatment control condition did not.

Hypothetical results from a study including treatment, no-treatment, and placebo conditions.

Figure 3.2: Hypothetical results from a study including treatment, no-treatment, and placebo conditions.

Fortunately, there are several solutions to this problem. One is to include a placebo control condition , in which participants receive a placebo that looks much like the treatment but lacks the active ingredient or element thought to be responsible for the treatment’s effectiveness. When participants in a treatment condition take a pill, for example, then those in a placebo control condition would take an identical-looking pill that lacks the active ingredient in the treatment (a “sugar pill”). In research on psychotherapy effectiveness, the placebo might involve going to a psychotherapist and talking in an unstructured way about one’s problems. The idea is that if participants in both the treatment and the placebo control groups expect to improve, then any improvement in the treatment group over and above that in the placebo control group must have been caused by the treatment and not by participants’ expectations. This is what is shown by a comparison of the two outer bars in Figure 3.2 .

Of course, the principle of informed consent requires that participants be told that they will be assigned to either a treatment or a placebo control condition—even though they cannot be told which until the experiment ends. In many cases the participants who had been in the control condition are then offered an opportunity to have the real treatment. An alternative approach is to use a waitlist control condition , in which participants are told that they will receive the treatment but must wait until the participants in the treatment condition have already received it. This allows researchers to compare participants who have received the treatment with participants who are not currently receiving it but who still expect to improve (eventually). A final solution to the problem of placebo effects is to leave out the control condition completely and compare any new treatment with the best available alternative treatment. For example, a new treatment for simple phobia could be compared with standard exposure therapy. Because participants in both conditions receive a treatment, their expectations about improvement should be similar. This approach also makes sense because once there is an effective treatment, the interesting question about a new treatment is not simply “Does it work?” but “Does it work better than what is already available?”

The Powerful Placebo

Many people are not surprised that placebos can have a positive effect on disorders that seem fundamentally psychological, including depression, anxiety, and insomnia. However, placebos can also have a positive effect on disorders that most people think of as fundamentally physiological. These include asthma, ulcers, and warts ( Shapiro & Shapiro, 2000 ) . There is even evidence that placebo surgery—also called “sham surgery”—can be as effective as actual surgery.

Medical researcher J. Bruce Moseley and his colleagues conducted a study on the effectiveness of two arthroscopic surgery procedures for osteoarthritis of the knee ( Moseley et al., 2002 ) . The control participants in this study were prepped for surgery, received a tranquilizer, and even received three small incisions in their knees. But they did not receive the actual arthroscopic surgical procedure. The surprising result was that all participants improved in terms of both knee pain and function, and the sham surgery group improved just as much as the treatment groups. According to the researchers, “This study provides strong evidence that arthroscopic lavage with or without débridement [the surgical procedures used] is not better than and appears to be equivalent to a placebo procedure in improving knee pain and self-reported function” (p. 85).

Research has shown that patients with osteoarthritis of the knee who receive a “sham surgery” experience reductions in pain and improvement in knee function similar to those of patients who receive a real surgery. *Photo by Piron Guillaume on Unsplash.*

Figure 3.3: Research has shown that patients with osteoarthritis of the knee who receive a “sham surgery” experience reductions in pain and improvement in knee function similar to those of patients who receive a real surgery. Photo by Piron Guillaume on Unsplash.

3.3 Within-Subjects Experiments

In a within-subjects experiment , each participant is tested under all conditions. Consider an experiment on the effect of a defendant’s physical attractiveness on judgments of his guilt. Again, in a between-subjects experiment, one group of participants would be shown an attractive defendant and asked to judge his guilt, and another group of participants would be shown an unattractive defendant and asked to judge his guilt. In a within-subjects experiment, however, the same group of participants would judge the guilt of both an attractive and an unattractive defendant.

The primary advantage of this approach is that it provides maximum control of extraneous participant variables. Participants in all conditions have the same mean IQ, same socioeconomic status, same number of siblings, and so on—because they are the very same people. Within-subjects experiments also make it possible to use statistical procedures that remove the effect of these extraneous participant variables on the dependent variable and therefore make the data less “noisy” and the effect of the independent variable easier to detect. We will look more closely at this idea later in the book.

Carryover Effects and Counterbalancing

The primary disadvantage of within-subjects designs is that they can result in carryover effects. A carryover effect is an effect of being tested in one condition on participants’ behavior in later conditions. One type of carryover effect is a practice effect , where participants perform a task better in later conditions because they have had a chance to practice it. Another type is a fatigue effect , where participants perform a task worse in later conditions because they become tired or bored. Being tested in one condition can also change how participants perceive stimuli or interpret their task in later conditions. This is called a context effect . For example, an average-looking defendant might be judged more harshly when participants have just judged an attractive defendant than when they have just judged an unattractive defendant. Within-subjects experiments also make it easier for participants to guess the hypothesis. For example, a participant who is asked to judge the guilt of an attractive defendant and then is asked to judge the guilt of an unattractive defendant is likely to guess that the hypothesis is that defendant attractiveness affects judgments of guilt. This could lead the participant to judge the unattractive defendant more harshly because he thinks this is what he is expected to do. Or it could make participants judge the two defendants similarly in an effort to be “fair.”

Carryover effects can be interesting in their own right. (Does the attractiveness of one person depend on the attractiveness of other people that we have seen recently?) But when they are not the focus of the research, carryover effects can be problematic. Imagine, for example, that participants judge the guilt of an attractive defendant and then judge the guilt of an unattractive defendant. If they judge the unattractive defendant more harshly, this might be because of his unattractiveness. But it could be instead that they judge him more harshly because they are becoming bored or tired. In other words, the order of the conditions is a confounding variable. The attractive condition is always the first condition and the unattractive condition the second. Thus any difference between the conditions in terms of the dependent variable could be caused by the order of the conditions and not the independent variable itself.

There is a solution to the problem of order effects, however, that can be used in many situations. It is counterbalancing , which means testing different participants in different orders. For example, some participants would be tested in the attractive defendant condition followed by the unattractive defendant condition, and others would be tested in the unattractive condition followed by the attractive condition. With three conditions, there would be six different orders (ABC, ACB, BAC, BCA, CAB, and CBA), so some participants would be tested in each of the six orders. With counterbalancing, participants are assigned to orders randomly, using the techniques we have already discussed. Thus random assignment plays an important role in within-subjects designs just as in between-subjects designs. Here, instead of randomly assigning to conditions, they are randomly assigned to different orders of conditions. In fact, it can safely be said that if a study does not involve random assignment in one form or another, it is not an experiment.

There are two ways to think about what counterbalancing accomplishes. One is that it controls the order of conditions so that it is no longer a confounding variable. Instead of the attractive condition always being first and the unattractive condition always being second, the attractive condition comes first for some participants and second for others. Likewise, the unattractive condition comes first for some participants and second for others. Thus any overall difference in the dependent variable between the two conditions cannot have been caused by the order of conditions. A second way to think about what counterbalancing accomplishes is that if there are carryover effects, it makes it possible to detect them. One can analyze the data separately for each order to see whether it had an effect.

When 9 Is “Larger” Than 221

Researcher Michael Birnbaum has argued that the lack of context provided by between-subjects designs is often a bigger problem than the context effects created by within-subjects designs. To demonstrate this, he asked one group of participants to rate how large the number 9 was on a 1-to-10 rating scale and another group to rate how large the number 221 was on the same 1-to-10 rating scale ( Birnbaum, 1999 ) . Participants in this between-subjects design gave the number 9 a mean rating of 5.13 and the number 221 a mean rating of 3.10. In other words, they rated 9 as larger than 221! According to Birnbaum, this is because participants spontaneously compared 9 with other one-digit numbers (in which case it is relatively large) and compared 221 with other three-digit numbers (in which case it is relatively small).

Simultaneous Within-Subjects Designs

So far, we have discussed an approach to within-subjects designs in which participants are tested in one condition at a time. There is another approach, however, that is often used when participants make multiple responses in each condition. Imagine, for example, that participants judge the guilt of 10 attractive defendants and 10 unattractive defendants. Instead of having people make judgments about all 10 defendants of one type followed by all 10 defendants of the other type, the researcher could present all 20 defendants in a sequence that mixed the two types. The researcher could then compute each participant’s mean rating for each type of defendant. Or imagine an experiment designed to see whether people with social anxiety disorder remember negative adjectives (e.g., “stupid,” “incompetent”) better than positive ones (e.g., “happy,” “productive”). The researcher could have participants study a single list that includes both kinds of words and then have them try to recall as many words as possible. The researcher could then count the number of each type of word that was recalled. There are many ways to determine the order in which the stimuli are presented, but one common way is to generate a different random order for each participant.

Between-Subjects or Within-Subjects?

Almost every experiment can be conducted using either a between-subjects design or a within-subjects design. This means that researchers must choose between the two approaches based on their relative merits for the particular situation.

Between-subjects experiments have the advantage of being conceptually simpler and requiring less testing time per participant. They also avoid carryover effects without the need for counterbalancing. Within-subjects experiments have the advantage of controlling extraneous participant variables, which generally reduces noise in the data and makes it easier to detect a relationship between the independent and dependent variables.

A good rule of thumb, then, is that if it is possible to conduct a within-subjects experiment (with proper counterbalancing) in the time that is available per participant—and you have no serious concerns about carryover effects—this is probably the best option. If a within-subjects design would be difficult or impossible to carry out, then you should consider a between-subjects design instead. For example, if you were testing participants in a doctor’s waiting room or shoppers in line at a grocery store, you might not have enough time to test each participant in all conditions and therefore would opt for a between-subjects design. Or imagine you were trying to reduce people’s level of prejudice by having them interact with someone of another race. A within-subjects design with counterbalancing would require testing some participants in the treatment condition first and then in a control condition. But if the treatment works and reduces people’s level of prejudice, then they would no longer be suitable for testing in the control condition. This is true for many designs that involve a treatment meant to produce long-term change in participants’ behavior (e.g., studies testing the effectiveness of psychotherapy). Clearly, a between-subjects design would be necessary here.

Remember also that using one type of design does not preclude using the other type in a different study. There is no reason that a researcher could not use both a between-subjects design and a within-subjects design to answer the same research question. In fact, professional researchers often do exactly this.

  • Experiments can be conducted using either between-subjects or within-subjects designs. Deciding which to use in a particular situation requires careful consideration of the pros and cons of each approach.
  • Random assignment to conditions in between-subjects experiments or to orders of conditions in within-subjects experiments is a fundamental element of experimental research. Its purpose is to control extraneous variables so that they do not become confounding variables.
  • Experimental research on the effectiveness of a treatment requires both a treatment condition and a control condition, which can be a no-treatment control condition, a placebo control condition, or a waitlist control condition. Experimental treatments can also be compared with the best available alternative.
  • You want to test the relative effectiveness of two training programs for running a marathon.
  • Using photographs of people as stimuli, you want to see if smiling people are perceived as more intelligent than people who are not smiling.
  • In a field experiment, you want to see if the way a panhandler is dressed (neatly vs. sloppily) affects whether or not passersby give him any money.
  • You want to see if concrete nouns (e.g., dog ) are recalled better than abstract nouns (e.g., truth ).
  • Discussion: Imagine that an experiment shows that participants who receive psychodynamic therapy for a dog phobia improve more than participants in a no-treatment control group. Explain a fundamental problem with this research design and at least two ways that it might be corrected.

3.4 Conducting Experiments

  • Describe several strategies for recruiting participants for an experiment.
  • Explain why it is important to standardize the procedure of an experiment and several ways to do this.
  • Explain what pilot testing is and why it is important.

The information presented so far in this chapter is enough to design a basic experiment. When it comes time to conduct that experiment, however, several additional practical issues arise. In this section, we consider some of these issues and how to deal with them. Much of this information applies to nonexperimental studies as well as experimental ones.

Recruiting Participants

Of course, you should be thinking about how you will obtain your participants from the beginning of any research project. Unless you have access to people with schizophrenia or incarcerated juvenile offenders, for example, then there is no point designing a study that focuses on these populations. But even if you plan to use a convenience sample, you will have to recruit participants for your study.

There are several approaches to recruiting participants. One is to use participants from a formal subject pool —an established group of people who have agreed to be contacted about participating in research studies. For example, at many colleges and universities, there is a subject pool consisting of students enrolled in introductory psychology courses who must participate in a certain number of studies to meet a course requirement. Researchers post descriptions of their studies and students sign up to participate, usually via an online system. Participants who are not in subject pools can also be recruited by posting or publishing advertisements or making personal appeals to groups that represent the population of interest. For example, a researcher interested in studying older adults could arrange to speak at a meeting of the residents at a retirement community to explain the study and ask for volunteers.

The Volunteer Subject

Even if the participants in a study receive compensation in the form of course credit, a small amount of money, or a chance at being treated for a psychological problem, they are still essentially volunteers. This is worth considering because people who volunteer to participate in psychological research have been shown to differ in predictable ways from those who do not volunteer. Specifically, there is good evidence that on average, volunteers have the following characteristics compared with nonvolunteers ( Rosenthal, 1965 ) .

  • They are more interested in the topic of the research.
  • They are more educated.
  • They have a greater need for approval.
  • They have higher intelligence quotients (IQs).
  • They are more sociable.
  • They are higher in social class.

This can be an issue of external validity if there is reason to believe that participants with these characteristics are likely to behave differently than the general population. For example, in testing different methods of persuading people, a rational argument might work better on volunteers than it does on the general population because of their generally higher educational level and IQ.

In many field experiments, the task is not recruiting participants but selecting them. For example, researchers Nicolas Guéguen and Marie-Agnès de Gail conducted a field experiment on the effect of being smiled at on helping, in which the participants were shoppers at a supermarket. A confederate walking down a stairway gazed directly at a shopper walking up the stairway and either smiled or did not smile. Shortly afterward, the shopper encountered another confederate, who dropped some computer diskettes on the ground. The dependent variable was whether or not the shopper stopped to help pick up the diskettes ( Gueguen & De Gail, 2003 ) . Notice that these participants were not “recruited,” but the researchers still had to select them from among all the shoppers taking the stairs that day. It is extremely important that this kind of selection be done according to a well-defined set of rules that is established before the data collection begins and can be explained clearly afterward. In this case, with each trip down the stairs, the confederate was instructed to gaze at the first person he encountered who appeared to be between the ages of 20 and 50. Only if the person gazed back did he or she become a participant in the study. The point of having a well-defined selection rule is to avoid bias in the selection of participants. For example, if the confederate was free to choose which shoppers he would gaze at, he might choose friendly-looking shoppers when he was set to smile and unfriendly-looking ones when he was not set to smile. As we will see shortly, such biases can be entirely unintentional.

Standardizing the Procedure

It is surprisingly easy to introduce extraneous variables during the procedure. For example, the same experimenter might give clear instructions to one participant but vague instructions to another. Or one experimenter might greet participants warmly while another barely makes eye contact with them. To the extent that such variables affect participants’ behavior, they add noise to the data and make the effect of the independent variable more difficult to detect. If they vary across conditions, they become confounding variables and provide alternative explanations for the results. For example, if participants in a treatment group are tested by a warm and friendly experimenter and participants in a control group are tested by a cold and unfriendly one, then what appears to be an effect of the treatment might actually be an effect of experimenter demeanor.

Experimenter’s Sex as an Extraneous Variable

It is well known that whether research participants are male or female can affect the results of a study. But what about whether the experimenter is male or female? There is plenty of evidence that this matters too. Male and female experimenters have slightly different ways of interacting with their participants, and of course participants also respond differently to male and female experimenters ( Rosenthal, 1976 ) For example, in a study on pain perception, participants immersed their hands in icy water for as long as they could ( Kállai et al., 2004 ) . Male participants tolerated the pain longer when the experimenter was a woman, and female participants tolerated it longer when the experimenter was a man.

Researcher Robert Rosenthal has spent much of his career showing that this kind of unintended variation in the procedure does, in fact, affect participants’ behavior. Furthermore, one important source of such variation is the experimenter’s expectations about how participants “should” behave in the experiment. This is referred to as an experimenter expectancy effect ( Rosenthal, 1976 ) . For example, if an experimenter expects participants in a treatment group to perform better on a task than participants in a control group, then he or she might unintentionally give the treatment group participants clearer instructions or more encouragement or allow them more time to complete the task. In a striking example, Rosenthal and Kermit Fode had several students in a laboratory course in psychology train rats to run through a maze. Although the rats were genetically similar, some of the students were told that they were working with “maze-bright” rats that had been bred to be good learners, and other students were told that they were working with “maze-dull” rats that had been bred to be poor learners. Sure enough, over five days of training, the “maze-bright” rats made more correct responses, made the correct response more quickly, and improved more steadily than the “maze-dull” rats ( Rosenthal & Fode, 1963 ) . Clearly it had to have been the students’ expectations about how the rats would perform that made the difference. But how? Some clues come from data gathered at the end of the study, which showed that students who expected their rats to learn quickly felt more positively about their animals and reported behaving toward them in a more friendly manner (e.g., handling them more).

The way to minimize unintended variation in the procedure is to standardize it as much as possible so that it is carried out in the same way for all participants regardless of the condition they are in. Here are several ways to do this:

  • Create a written protocol that specifies everything that the experimenters are to do and say from the time they greet participants to the time they dismiss them.
  • Create standard instructions that participants read themselves or that are read to them word for word by the experimenter.
  • Automate the rest of the procedure as much as possible by using software packages for this purpose or even simple computer slide shows.
  • Anticipate participants’ questions and either raise and answer them in the instructions or develop standard answers for them.
  • Train multiple experimenters on the protocol together and have them practice on each other.
  • Be sure that each experimenter tests participants in all conditions.

Another good practice is to arrange for the experimenters to be “blind” to the research question or to the condition that each participant is tested in. The idea is to minimize experimenter expectancy effects by minimizing the experimenters’ expectations. For example, in a drug study in which each participant receives the drug or a placebo, it is often the case that neither the participants nor the experimenter who interacts with the participants know which condition he or she has been assigned to. Because both the participants and the experimenters are blind to the condition, this is referred to as a double-blind study. (A single-blind study is one in which the participant, but not the experimenter, is blind to the condition.) Of course, there are many times this is not possible. For example, if you are both the investigator and the only experimenter, it is not possible for you to remain blind to the research question. Also, in many studies the experimenter must know the condition because he or she must carry out the procedure in a different way in the different conditions.

Record Keeping

It is essential to keep good records when you conduct an experiment. As discussed earlier, it is typical for experimenters to generate a written sequence of conditions before the study begins and then to test each new participant in the next condition in the sequence. As you test them, it is a good idea to add to this list basic demographic information; the date, time, and place of testing; and the name of the experimenter who did the testing. It is also a good idea to have a place for the experimenter to write down comments about unusual occurrences (e.g., a confused or uncooperative participant) or questions that come up. This kind of information can be useful later if you decide to analyze sex differences or effects of different experimenters, or if a question arises about a particular participant or testing session.

It can also be useful to assign an identification number to each participant as you test them. Simply numbering them consecutively beginning with 1 is usually sufficient. This number can then also be written on any response sheets or questionnaires that participants generate, making it easier to keep them together.

Pilot Testing

It is always a good idea to conduct a pilot test of your experiment. A pilot test is a small-scale study conducted to make sure that a new procedure works as planned. In a pilot test, you can recruit participants formally (e.g., from an established participant pool) or you can recruit them informally from among family, friends, classmates, and so on. The number of participants can be small, but it should be enough to give you confidence that your procedure works as planned. There are several important questions that you can answer by conducting a pilot test:

  • Do participants understand the instructions?
  • What kind of misunderstandings do participants have, what kind of mistakes do they make, and what kind of questions do they ask?
  • Do participants become bored or frustrated?
  • Is an indirect manipulation effective? (You will need to include a manipulation check.)
  • Can participants guess the research question or hypothesis?
  • How long does the procedure take?
  • Are computer programs or other automated procedures working properly?
  • Are data being recorded correctly?

Of course, to answer some of these questions you will need to observe participants carefully during the procedure and talk with them about it afterward. Participants are often hesitant to criticize a study in front of the researcher, so be sure they understand that this is a pilot test and you are genuinely interested in feedback that will help you improve the procedure. If the procedure works as planned, then you can proceed with the actual study. If there are problems to be solved, you can solve them, pilot test the new procedure, and continue with this process until you are ready to proceed.

  • There are several effective methods you can use to recruit research participants for your experiment, including through formal subject pools, advertisements, and personal appeals. Field experiments require well-defined participant selection procedures.
  • It is important to standardize experimental procedures to minimize extraneous variables, including experimenter expectancy effects.
  • It is important to conduct one or more small-scale pilot tests of an experiment to be sure that the procedure works as planned.
  • Practice: List two ways that you might recruit participants from each of the following populations: (a) elderly adults, (b) unemployed people, (c) regular exercisers, and (d) math majors.
  • Discussion: Imagine a study in which you will visually present participants with a list of 20 words, one at a time, wait for a short time, and then ask them to recall as many of the words as they can. In the stressed condition, they are told that they might also be chosen to give a short speech in front of a small audience. In the unstressed condition, they are not told that they might have to give a speech. What are several specific things that you could do to standardize the procedure?

3.5 Glossary

Between-subjects experiment.

An experiment in which each participant is tested in one condition.

block randomization

A method of randomly assigning participants that guarantees that the condition sample sizes are equal or almost equal. A random procedure is used to assign the first k participants into the k conditions, and then to assign the next k participants into the k conditions, and so on until all the participants have been assigned.

carryover effect

An effect of being tested in one condition on participants’ behavior in later conditions.

One level of the independent variable in an experiment.

confounding variable

An extraneous variable that differs across the levels of the independent variable.

context effect

An unintended effect of the context in which a response is made. In within-subjects experiments, this can be an effect of being tested in one condition on how participants perceive stimuli or interpret their task and therefore how they respond in later conditions. In survey research, this can be an effect of the surrounding items or the response scale on responses to a particular item.

Holding extraneous variables constant.

control condition

A condition in a study in which participants do not receive the treatment of interest.

counterbalancing

Systematically varying the order of conditions across participants.

double-blind

An experimental research design in which both the participants and the experimenters are unaware of which condition the participant has been assigned to.

A type of empirical study in which an independent variable is manipulated and a dependent variable is measured while extraneous variables are controlled.

experimenter expectancy effect

The effect of the researcher’s expectations on participants’ behavior.

external validity

The extent to which the results of a study can be generalized to people and situations beyond those actually studied.

extraneous variable

Any variable in the context of an experiment other than the independent and dependent variables.

fatigue effect

A carryover effect in which participants perform worse on a task in later conditions because they have become tired or bored.

field experiments

An experiment that is conducted outside the laboratory.

internal validity

The extent to which the design of a study supports the conclusion that differences in the independent variable caused any observed differences in the dependent variable.

Systematically changing the level of the independent variable across groups or situations.

manipulation check

A measure of a manipulated independent variable—usually done at the end of the procedure—to confirm that the independent variable was successfully manipulated.

no-treatment control condition

A control condition in which participants receive no treatment whatsoever—not even a placebo.

A small-scale study conducted primarily to be sure that a procedure works as planned.

A treatment that lacks any active ingredient or element that should make it effective.

placebo control condition

A control condition in which participants receive a placebo.

placebo effect

The positive effect of a placebo.

practice effect

A carryover effect in which participants perform better on a task in later conditions because they have had a chance to practice.

random assignment

The assignment of participants to different conditions according to a random procedure, such as flipping a coin, rolling a die, or using a random number generator.

randomized clinical trial

An experiment designed to test the effectiveness of a psychological or medical treatment.

subject pool

A group of people who have agreed to be contacted about opportunities to be research participants. Many universities have subject pools that consist of introductory psychology students who participate to meet a course requirement.

An intervention intended to change people’s behavior for the better.

treatment condition

A condition in a study in which participants receive some treatment of interest.

waitlist control condition

A control condition in which participants are put on a waitlist to receive the treatment after the study is completed.

within-subjects experiment

An experiment in which each participant is tested in all conditions.

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Experimental Design

Learning objectives.

  • Explain the difference between between-subjects and within-subjects experiments, list some of the pros and cons of each approach, and decide which approach to use to answer a particular research question.
  • Define random assignment, distinguish it from random sampling, explain its purpose in experimental research, and use some simple strategies to implement it.
  • Define what a control condition is, explain its purpose in research on treatment effectiveness, and describe some alternative types of control conditions.
  • Define several types of carryover effect, give examples of each, and explain how counterbalancing helps to deal with them.

In this section, we look at some different ways to design an experiment. The primary distinction we will make is between approaches in which each participant experiences one level of the independent variable and approaches in which each participant experiences all levels of the independent variable. The former are called between-subjects experiments and the latter are called within-subjects experiments.

Between-Subjects Experiments

In a  between-subjects experiment , each participant is tested in only one condition. For example, a researcher with a sample of 100 university  students might assign half of them to write about a traumatic event and the other half write about a neutral event. Or a researcher with a sample of 60 people with severe agoraphobia (fear of open spaces) might assign 20 of them to receive each of three different treatments for that disorder. It is essential in a between-subjects experiment that the researcher assign participants to conditions so that the different groups are, on average, highly similar to each other. Those in a trauma condition and a neutral condition, for example, should include a similar proportion of men and women, and they should have similar average intelligence quotients (IQs), similar average levels of motivation, similar average numbers of health problems, and so on. This matching is a matter of controlling these extraneous participant variables across conditions so that they do not become confounding variables.

Random Assignment

The primary way that researchers accomplish this kind of control of extraneous variables across conditions is called  random assignment , which means using a random process to decide which participants are tested in which conditions. Do not confuse random assignment with random sampling. Random sampling is a method for selecting a sample from a population, and it is rarely used in psychological research. Random assignment is a method for assigning participants in a sample to the different conditions, and it is an important element of all experimental research in psychology and other fields too.

In its strictest sense, random assignment should meet two criteria. One is that each participant has an equal chance of being assigned to each condition (e.g., a 50% chance of being assigned to each of two conditions). The second is that each participant is assigned to a condition independently of other participants. Thus one way to assign participants to two conditions would be to flip a coin for each one. If the coin lands heads, the participant is assigned to Condition A, and if it lands tails, the participant is assigned to Condition B. For three conditions, one could use a computer to generate a random integer from 1 to 3 for each participant. If the integer is 1, the participant is assigned to Condition A; if it is 2, the participant is assigned to Condition B; and if it is 3, the participant is assigned to Condition C. In practice, a full sequence of conditions—one for each participant expected to be in the experiment—is usually created ahead of time, and each new participant is assigned to the next condition in the sequence as he or she is tested. When the procedure is computerized, the computer program often handles the random assignment.

One problem with coin flipping and other strict procedures for random assignment is that they are likely to result in unequal sample sizes in the different conditions. Unequal sample sizes are generally not a serious problem, and you should never throw away data you have already collected to achieve equal sample sizes. However, for a fixed number of participants, it is statistically most efficient to divide them into equal-sized groups. It is standard practice, therefore, to use a kind of modified random assignment that keeps the number of participants in each group as similar as possible. One approach is block randomization . In block randomization, all the conditions occur once in the sequence before any of them is repeated. Then they all occur again before any of them is repeated again. Within each of these “blocks,” the conditions occur in a random order. Again, the sequence of conditions is usually generated before any participants are tested, and each new participant is assigned to the next condition in the sequence.  Table 6.2  shows such a sequence for assigning nine participants to three conditions. The Research Randomizer website will generate block randomization sequences for any number of participants and conditions. Again, when the procedure is computerized, the computer program often handles the block randomization.

Random assignment is not guaranteed to control all extraneous variables across conditions. It is always possible that just by chance, the participants in one condition might turn out to be substantially older, less tired, more motivated, or less depressed on average than the participants in another condition. However, there are some reasons that this possibility is not a major concern. One is that random assignment works better than one might expect, especially for large samples. Another is that the inferential statistics that researchers use to decide whether a difference between groups reflects a difference in the population takes the “fallibility” of random assignment into account. Yet another reason is that even if random assignment does result in a confounding variable and therefore produces misleading results, this confound is likely to be detected when the experiment is replicated. The upshot is that random assignment to conditions—although not infallible in terms of controlling extraneous variables—is always considered a strength of a research design.

Treatment and Control Conditions

Between-subjects experiments are often used to determine whether a treatment works. In psychological research, a  treatment  is any intervention meant to change people’s behaviour for the better. This  intervention  includes psychotherapies and medical treatments for psychological disorders but also interventions designed to improve learning, promote conservation, reduce prejudice, and so on. To determine whether a treatment works, participants are randomly assigned to either a  treatment condition , in which they receive the treatment, or a control condition , in which they do not receive the treatment. If participants in the treatment condition end up better off than participants in the control condition—for example, they are less depressed, learn faster, conserve more, express less prejudice—then the researcher can conclude that the treatment works. In research on the effectiveness of psychotherapies and medical treatments, this type of experiment is often called a randomized clinical trial .

There are different types of control conditions. In a  no-treatment control condition , participants receive no treatment whatsoever. One problem with this approach, however, is the existence of placebo effects. A  placebo  is a simulated treatment that lacks any active ingredient or element that should make it effective, and a  placebo effect  is a positive effect of such a treatment. Many folk remedies that seem to work—such as eating chicken soup for a cold or placing soap under the bedsheets to stop nighttime leg cramps—are probably nothing more than placebos. Although placebo effects are not well understood, they are probably driven primarily by people’s expectations that they will improve. Having the expectation to improve can result in reduced stress, anxiety, and depression, which can alter perceptions and even improve immune system functioning (Price, Finniss, & Benedetti, 2008) [1] .

Placebo effects are interesting in their own right (see  Note “The Powerful Placebo” ), but they also pose a serious problem for researchers who want to determine whether a treatment works.  Figure 6.2  shows some hypothetical results in which participants in a treatment condition improved more on average than participants in a no-treatment control condition. If these conditions (the two leftmost bars in  Figure 6.2 ) were the only conditions in this experiment, however, one could not conclude that the treatment worked. It could be instead that participants in the treatment group improved more because they expected to improve, while those in the no-treatment control condition did not.

Figure 6.2 Hypothetical Results From a Study Including Treatment, No-Treatment, and Placebo Conditions

Fortunately, there are several solutions to this problem. One is to include a placebo control condition , in which participants receive a placebo that looks much like the treatment but lacks the active ingredient or element thought to be responsible for the treatment’s effectiveness. When participants in a treatment condition take a pill, for example, then those in a placebo control condition would take an identical-looking pill that lacks the active ingredient in the treatment (a “sugar pill”). In research on psychotherapy effectiveness, the placebo might involve going to a psychotherapist and talking in an unstructured way about one’s problems. The idea is that if participants in both the treatment and the placebo control groups expect to improve, then any improvement in the treatment group over and above that in the placebo control group must have been caused by the treatment and not by participants’ expectations. This  difference  is what is shown by a comparison of the two outer bars in  Figure 6.2 .

Of course, the principle of informed consent requires that participants be told that they will be assigned to either a treatment or a placebo control condition—even though they cannot be told which until the experiment ends. In many cases the participants who had been in the control condition are then offered an opportunity to have the real treatment. An alternative approach is to use a waitlist control condition , in which participants are told that they will receive the treatment but must wait until the participants in the treatment condition have already received it. This disclosure allows researchers to compare participants who have received the treatment with participants who are not currently receiving it but who still expect to improve (eventually). A final solution to the problem of placebo effects is to leave out the control condition completely and compare any new treatment with the best available alternative treatment. For example, a new treatment for simple phobia could be compared with standard exposure therapy. Because participants in both conditions receive a treatment, their expectations about improvement should be similar. This approach also makes sense because once there is an effective treatment, the interesting question about a new treatment is not simply “Does it work?” but “Does it work better than what is already available?

The Powerful Placebo

Many people are not surprised that placebos can have a positive effect on disorders that seem fundamentally psychological, including depression, anxiety, and insomnia. However, placebos can also have a positive effect on disorders that most people think of as fundamentally physiological. These include asthma, ulcers, and warts (Shapiro & Shapiro, 1999) [2] . There is even evidence that placebo surgery—also called “sham surgery”—can be as effective as actual surgery.

Medical researcher J. Bruce Moseley and his colleagues conducted a study on the effectiveness of two arthroscopic surgery procedures for osteoarthritis of the knee (Moseley et al., 2002) [3] . The control participants in this study were prepped for surgery, received a tranquilizer, and even received three small incisions in their knees. But they did not receive the actual arthroscopic surgical procedure. The surprising result was that all participants improved in terms of both knee pain and function, and the sham surgery group improved just as much as the treatment groups. According to the researchers, “This study provides strong evidence that arthroscopic lavage with or without débridement [the surgical procedures used] is not better than and appears to be equivalent to a placebo procedure in improving knee pain and self-reported function” (p. 85).

Within-Subjects Experiments

In a  within-subjects experiment , each participant is tested under all conditions. Consider an experiment on the effect of a defendant’s physical attractiveness on judgments of his guilt. Again, in a between-subjects experiment, one group of participants would be shown an attractive defendant and asked to judge his guilt, and another group of participants would be shown an unattractive defendant and asked to judge his guilt. In a within-subjects experiment, however, the same group of participants would judge the guilt of both an attractive  and  an unattractive defendant.

The primary advantage of this approach is that it provides maximum control of extraneous participant variables. Participants in all conditions have the same mean IQ, same socioeconomic status, same number of siblings, and so on—because they are the very same people. Within-subjects experiments also make it possible to use statistical procedures that remove the effect of these extraneous participant variables on the dependent variable and therefore make the data less “noisy” and the effect of the independent variable easier to detect. We will look more closely at this idea later in the book .  However, not all experiments can use a within-subjects design nor would it be desirable to.

Carryover Effects and Counterbalancing

The primary disadvantage of within-subjects designs is that they can result in carryover effects. A  carryover effect  is an effect of being tested in one condition on participants’ behaviour in later conditions. One type of carryover effect is a  practice effect , where participants perform a task better in later conditions because they have had a chance to practice it. Another type is a fatigue effect , where participants perform a task worse in later conditions because they become tired or bored. Being tested in one condition can also change how participants perceive stimuli or interpret their task in later conditions. This  type of effect  is called a  context effect . For example, an average-looking defendant might be judged more harshly when participants have just judged an attractive defendant than when they have just judged an unattractive defendant. Within-subjects experiments also make it easier for participants to guess the hypothesis. For example, a participant who is asked to judge the guilt of an attractive defendant and then is asked to judge the guilt of an unattractive defendant is likely to guess that the hypothesis is that defendant attractiveness affects judgments of guilt. This  knowledge  could lead the participant to judge the unattractive defendant more harshly because he thinks this is what he is expected to do. Or it could make participants judge the two defendants similarly in an effort to be “fair.”

Carryover effects can be interesting in their own right. (Does the attractiveness of one person depend on the attractiveness of other people that we have seen recently?) But when they are not the focus of the research, carryover effects can be problematic. Imagine, for example, that participants judge the guilt of an attractive defendant and then judge the guilt of an unattractive defendant. If they judge the unattractive defendant more harshly, this might be because of his unattractiveness. But it could be instead that they judge him more harshly because they are becoming bored or tired. In other words, the order of the conditions is a confounding variable. The attractive condition is always the first condition and the unattractive condition the second. Thus any difference between the conditions in terms of the dependent variable could be caused by the order of the conditions and not the independent variable itself.

There is a solution to the problem of order effects, however, that can be used in many situations. It is  counterbalancing , which means testing different participants in different orders. For example, some participants would be tested in the attractive defendant condition followed by the unattractive defendant condition, and others would be tested in the unattractive condition followed by the attractive condition. With three conditions, there would be six different orders (ABC, ACB, BAC, BCA, CAB, and CBA), so some participants would be tested in each of the six orders. With counterbalancing, participants are assigned to orders randomly, using the techniques we have already discussed. Thus random assignment plays an important role in within-subjects designs just as in between-subjects designs. Here, instead of randomly assigning to conditions, they are randomly assigned to different orders of conditions. In fact, it can safely be said that if a study does not involve random assignment in one form or another, it is not an experiment.

An efficient way of counterbalancing is through a Latin square design which randomizes through having equal rows and columns. For example, if you have four treatments, you must have four versions. Like a Sudoku puzzle, no treatment can repeat in a row or column. For four versions of four treatments, the Latin square design would look like:

There are two ways to think about what counterbalancing accomplishes. One is that it controls the order of conditions so that it is no longer a confounding variable. Instead of the attractive condition always being first and the unattractive condition always being second, the attractive condition comes first for some participants and second for others. Likewise, the unattractive condition comes first for some participants and second for others. Thus any overall difference in the dependent variable between the two conditions cannot have been caused by the order of conditions. A second way to think about what counterbalancing accomplishes is that if there are carryover effects, it makes it possible to detect them. One can analyze the data separately for each order to see whether it had an effect.

When 9 Is “Larger” Than 221

Researcher Michael Birnbaum has argued that the  lack  of context provided by between-subjects designs is often a bigger problem than the context effects created by within-subjects designs. To demonstrate this problem, he asked participants to rate two numbers on how large they were on a scale of 1-to-10 where 1 was “very very small” and 10 was “very very large”.  One group of participants were asked to rate the number 9 and another group was asked to rate the number 221 (Birnbaum, 1999) [4] . Participants in this between-subjects design gave the number 9 a mean rating of 5.13 and the number 221 a mean rating of 3.10. In other words, they rated 9 as larger than 221! According to Birnbaum, this  difference  is because participants spontaneously compared 9 with other one-digit numbers (in which case it is  relatively large) and compared 221 with other three-digit numbers (in which case it is relatively  small).

Simultaneous Within-Subjects Designs

So far, we have discussed an approach to within-subjects designs in which participants are tested in one condition at a time. There is another approach, however, that is often used when participants make multiple responses in each condition. Imagine, for example, that participants judge the guilt of 10 attractive defendants and 10 unattractive defendants. Instead of having people make judgments about all 10 defendants of one type followed by all 10 defendants of the other type, the researcher could present all 20 defendants in a sequence that mixed the two types. The researcher could then compute each participant’s mean rating for each type of defendant. Or imagine an experiment designed to see whether people with social anxiety disorder remember negative adjectives (e.g., “stupid,” “incompetent”) better than positive ones (e.g., “happy,” “productive”). The researcher could have participants study a single list that includes both kinds of words and then have them try to recall as many words as possible. The researcher could then count the number of each type of word that was recalled. There are many ways to determine the order in which the stimuli are presented, but one common way is to generate a different random order for each participant.

Between-Subjects or Within-Subjects?

Almost every experiment can be conducted using either a between-subjects design or a within-subjects design. This possibility means that researchers must choose between the two approaches based on their relative merits for the particular situation.

Between-subjects experiments have the advantage of being conceptually simpler and requiring less testing time per participant. They also avoid carryover effects without the need for counterbalancing. Within-subjects experiments have the advantage of controlling extraneous participant variables, which generally reduces noise in the data and makes it easier to detect a relationship between the independent and dependent variables.

A good rule of thumb, then, is that if it is possible to conduct a within-subjects experiment (with proper counterbalancing) in the time that is available per participant—and you have no serious concerns about carryover effects—this design is probably the best option. If a within-subjects design would be difficult or impossible to carry out, then you should consider a between-subjects design instead. For example, if you were testing participants in a doctor’s waiting room or shoppers in line at a grocery store, you might not have enough time to test each participant in all conditions and therefore would opt for a between-subjects design. Or imagine you were trying to reduce people’s level of prejudice by having them interact with someone of another race. A within-subjects design with counterbalancing would require testing some participants in the treatment condition first and then in a control condition. But if the treatment works and reduces people’s level of prejudice, then they would no longer be suitable for testing in the control condition. This difficulty is true for many designs that involve a treatment meant to produce long-term change in participants’ behaviour (e.g., studies testing the effectiveness of psychotherapy). Clearly, a between-subjects design would be necessary here.

Remember also that using one type of design does not preclude using the other type in a different study. There is no reason that a researcher could not use both a between-subjects design and a within-subjects design to answer the same research question. In fact, professional researchers often take exactly this type of mixed methods approach.

Key Takeaways

  • Experiments can be conducted using either between-subjects or within-subjects designs. Deciding which to use in a particular situation requires careful consideration of the pros and cons of each approach.
  • Random assignment to conditions in between-subjects experiments or to orders of conditions in within-subjects experiments is a fundamental element of experimental research. Its purpose is to control extraneous variables so that they do not become confounding variables.
  • Experimental research on the effectiveness of a treatment requires both a treatment condition and a control condition, which can be a no-treatment control condition, a placebo control condition, or a waitlist control condition. Experimental treatments can also be compared with the best available alternative.
  • You want to test the relative effectiveness of two training programs for running a marathon.
  • Using photographs of people as stimuli, you want to see if smiling people are perceived as more intelligent than people who are not smiling.
  • In a field experiment, you want to see if the way a panhandler is dressed (neatly vs. sloppily) affects whether or not passersby give him any money.
  • You want to see if concrete nouns (e.g.,  dog ) are recalled better than abstract nouns (e.g.,  truth ).
  • Discussion: Imagine that an experiment shows that participants who receive psychodynamic therapy for a dog phobia improve more than participants in a no-treatment control group. Explain a fundamental problem with this research design and at least two ways that it might be corrected.
  • Price, D. D., Finniss, D. G., & Benedetti, F. (2008). A comprehensive review of the placebo effect: Recent advances and current thought. Annual Review of Psychology, 59 , 565–590. ↵
  • Shapiro, A. K., & Shapiro, E. (1999). The powerful placebo: From ancient priest to modern physician . Baltimore, MD: Johns Hopkins University Press. ↵
  • Moseley, J. B., O’Malley, K., Petersen, N. J., Menke, T. J., Brody, B. A., Kuykendall, D. H., … Wray, N. P. (2002). A controlled trial of arthroscopic surgery for osteoarthritis of the knee. The New England Journal of Medicine, 347 , 81–88. ↵
  • Birnbaum, M.H. (1999). How to show that 9>221: Collect judgments in a between-subjects design. Psychological Methods, 4 (3), 243-249. ↵

Research Methods in Psychology Copyright © 2015 by Paul C. Price, Rajiv Jhangiani, & I-Chant A. Chiang is licensed under a Creative Commons Attribution-NonCommercial-ShareAlike 4.0 International License , except where otherwise noted.

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Strand Debonding for Pretensioned Girders (2017)

Chapter: chapter 3 - experimental research approach, findings, and associated analytical simulations.

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52 3.1 Research Approach The effects of strand debonding on the performance of prestressed girders were examined experimentally through design, fabrication, and testing of six girders. The data obtained at pre- stress release and at various stages of load testing were utilized for this purpose. The FEM plat- form described in Section 2.4 and STM discussed in Section 2.5 were utilized to develop a better understanding of the experimental data. 3.2 Design and Detailing of Test Specimens Both ends of six full-scale girders were tested for a total of 12 sets of results. The main test vari- ables were (1) girder shape (single-web, box, or U), (2) amount of debonding of partially debonded strands, (3) concrete strength, and (4) strand diameter. Each girder had different debonding ratios at ends A and B. Key aspects of the specimens are summarized in Table 3.1. The specimen details are shown in Appendix E. With the exception of AASHTO BI-36, all the girders had a 6-in. thick slab over the entire width of the top flange. The deck slab reinforcement was designed according to the empirical design procedure described in AASHTO LRFD Article 9.7.2.5. No slab was pro- vided on the BI-36 girder; additionally, a 2.5-ft. thick end diaphragm was provided to replicate a common practice used in box girders. The test girders were designed and detailed to satisfy the following criteria: a. Satisfy concrete tensile stress limits at prestress release (AASHTO LRFD Article 5.9.4.1.2). b. Check AASHTO LRFD Eq. 5.8.3.5-2 from the interior face of support to the critical section to ensure that there is adequate Aps fps, accounting for debonding. As debonded strands become bonded, their pretensioning force is gradually developed. Figure 3.1 compares transfer of pretensioning forces in a girder with bonded and partially debonded strands. In this representative case, the full capacity of all strands in the section, Aps fps, is not available before 21 ft into the span. The calculations were based on the current AASHTO-prescribed equation for strand development length: 2 3 [5.11.4.2.1]l f f dd ps pe b= κ −     The depths of the test girders were greater than 24 in.; hence, the value of k was taken as 1.6 for fully bonded strands. (The value of k would have been 1.0 had the girders been shallower than 24 in.) For the partially debonded strands, a value of 2.0 was used for k. Experimental Research Approach, Findings, and Associated Analytical Simulations C h a p t e r 3

experimental research approach, Findings, and associated analytical Simulations 53 Table 3.1. Key details of the test specimens. Girder db(in.) End Total No. of Strands Debonding Ratio Reinforcement Total Per Row 0 to 3' 3 to 6' 6 to 9' 9 to 12' >12' Longitudinal Transverse (No. 4) No. & Size Cutoff Point (ft) Web Bottom flange U shaped AASHTO BI-36 0.5 A Row1: 15 Section 0.50 0.36 0.18 0.09 0 4 No. 6 8.5 @ 12 in. (outside of end diaphragm) 2 spaces @ 3 in.Row 1 0.40 0.27 0.13 0 0 Row 2 0.71 0.57 0.29 0.29 0 7 spaces @ 6 in. B Row2: 7 Section 0.18 0.09 0 0 0 None N/A Row 1 0.13 0 0 0 0 @ 12 in. to midspan Row 2 0.29 0.29 0 0 0 AASHTO BT-54 0.6 A Row1: 10 Section 0.60 0.40 0.20 0 0 2 No. 6 6.5 4 spaces @ 3 in. 8 spaces @ 3 in.Row 1 0.40 0.40 0 0 0 8 No. 6 13.5 Row 2 0.80 0.40 0.40 0 0 10 spaces @ 6 in. B Row2: 10 Section 0.10 0 0 0 0 6 No. 6 6.5 @ 18 in. to midspan Row 1 0.20 0 0 0 0 @ 18 in. to midspan Row 2 0.00 0 0 0 0 AASHTO Type III-a 0.5 A Row1: 8 Section 0.50 0.25 0.13 0 0 2 No. 5 5.5 3 spaces @ 3 in. 3 spaces @ 3 in.Row 1 0.25 0 0 0 0 6 No. 5 10.5 Row 2 0.75 0.50 0.25 0 0 10 spaces @ 6 in. B Row2: 8 Section 0.25 0.13 0 0 0 2 No. 5 6.5 @ 18 in. to midspan Row 1 0.25 0 0 0 0 4 No. 5 9.5 @ 18 in. to midspan Row 2 0.25 0.25 0 0 0 AASHTO Type III-b 0.5 A Row 1: 8 Section 0.56 0.33 0.11 0 0 2 No. 5 5.5 3 spaces @ 3 in. 3 spaces @ 3 in.Row 1 0.25 0 0 0 0 6 No. 5 10.5 Row 2 0.80 0.60 0.20 0 0 10 spaces @ 6 in. B Row 2: 10 Section 0.22 0.11 0 0 0 4 No. 5 5.5 @ 18 in. to midspan Row 1 0.25 0 0 0 0 4 No. 5 9.5 @ 18 in. to midspan Row 2 0.20 0.20 0 0 0 Nebraska NU-1100 0.7 A Row 1: 18 Section 0.45 0.27 0.18 0.09 0 6 No. 6 5.5 3 spaces @ 3 in. 3 spaces @ 3 in.Row 1 0.44 0.33 0.22 0.11 0 Row 2 0.50 0 0 0 0 10 spaces @ 6 in. B Row 2: 4 Section 0.27 0.18 0.18 0.18 0 4 No. 6 5.5 @ 12 in. to midspan Row 1 0.33 0.22 0.22 0.22 0 @ 12 in. to midspan Row 2 0.00 0 0 0 0 Texas U-40 0.6 A Row 1: 19 Section 0.50 0.35 0.19 0 0 22 No. 6 14.5 3 spaces @ 3 in. 3 spaces @ 3 in.Row 1 0.42 0.21 0 0 0 Row 2 0.71 0.71 0.71 0 0 22 spaces @ 4 in. 22 spaces @ 4 in. B Row 2: 7 Section 0.23 0.15 0.08 0 0 16 No. 6 13.5 Row 1 0.21 0.11 0 0 0 @ 6 in. to midspan @ 6 in. to midspan Row 2 0.29 0.29 0.29 0 0 Note: db = strand diameter. c. Check AASHTO LRFD Eq. 5.8.3.5-1 elsewhere along span to ensure that there is adequate Aps fps, accounting for debonding. d. Provide longitudinal nonprestressed reinforcement (i.e., added As fy) per AASHTO LRFD Article 5.8.3.5 if the checks in b or c are not satisfied. e. Follow the detailing rules summarized in Table 3.2. 3.3 Material Properties The experimentally determined concrete strengths (AASHTO Method T22) and material properties for all the reinforcing bars (AASHTO Method T244) are summarized in Tables 3.3 and 3.4, respectively. The concrete mix designs are provided in Appendix F. All seven-wire pre- stressing strand used was 270 ksi low-relaxation strand.

54 Strand Debonding for pretensioned Girders 3.4 Transfer Length During fabrication of the girders, five vibrating wire strain gages were placed in the concrete near the centroid of the strands at each end of each girder. The strains measured by these gages were used to assess the in situ transfer lengths, which were compared with computed values. The strain at each point along the girder length was determined by dividing the calculated stress by the calculated modulus of elasticity of concrete at prestress transfer. The concrete compressive stresses at the elevation of the vibrating wire gages (compression is negative) were calculated based on both the gross section (Eq. 3.1) and transformed section properties (Eq. 3.2). Eq. 3.1, , , , f P A Pe y y I M y y I c g e g g c g g sw c g g ( ) ( ) = − − − + − Figure 3.1. Development of pretensioning force in girders with partially debonded strands. Table 3.2. Detailing rules used for the test girders. AASHTO BT-54, AASHTO Type III, and Nebraska NU-1100 o Do not debond more than 50% of the bottom row strands. o Keep the outermost strands in all rows located within the full-width section of the flange (shaded region) bonded. Full width is understood to mean the full width of the bottom flange less a distance accounting for the chamfer—typically 2 in. on both sides. o With the exception of the outermost strands, debond strands further from the section vertical centerline preferentially to those nearer the centerline. AASHTO BI-36 and Texas U-40 o Do not debond more than 50% of the bottom row strands. o Keep the strands located in the planes of the webs bonded. All girders o Follow AASHTO LRFD Article 5.11.4.3: Not more than 40 percent of the debonded strands, or four strands, whichever is greater, shall have the debonding terminated at any section. o Provide splitting resistance according to AASHTO LRFD Article 5.10.10.1. o Provide confinement reinforcement according to AASHTO LRFD Article 5.10.10.2. o Satisfy the requirements proposed in Section 4.2 of the report.

experimental research approach, Findings, and associated analytical Simulations 55 Eq. 3.2, , , , f P A Pe y y I M y y I c transformed e transformed transformed c transformed transformed sw c transformed transformed ( ) ( ) = − − − + − As shown schematically in Figure 3.2, P is introduced in the girder bulb but it is some distance into the girder, xf , before the entire cross-sectional area is engaged in resisting P. That is, Ae,g = Abulb or Ae,transformed = Abulb,transformed at x = 0, and Ae,g = Ag and Ae,transformed = Atransformed at x = xf . Distance xf is defined by the assumed load-spreading angle, described by q in Figure 3.2. Angle q is taken as 30°, which approximately corresponds to a 2:1 strut angle typically assumed in D regions. In the transformed section calculations, the staggered bonding of the prestressing strand and the presence of the nonprestressed reinforcement were taken into account. Moreover, “voids” in the section representing unbonded strands were incorporated. The effective prestressing force (P) was computed by accounting for elastic shortening deter- mined based on AASHTO LRFD Article 5.9.5.2.3a-1 evaluated at each section. The transfer Table 3.3. Measured concrete strengths (ksi). Girder End At Release, f’ci Age at Test (days) f’c at Test Slab at Time of Test AASHTO BI-36 A 7.4 102 12.6 N/A B 97 12.2 AASHTO BT-54 A 10.2 42 17.4 11.4* B 18 15.2 11.2* AASHTO Type III-a A 6.9 93 12.6 7.4 B 78 12.2 6.2 AASHTO Type III-b A 8.3 184 13.8 6.1 B 155 13.2 5.7 Nebraska NU-1100 A 8.4 67 14.0 6.9 B 41 13.2 6.1 Texas U-40 A 6.9 110 12.8 5.9 B 95 12.0 5.8 *Due to scheduling issues, it was necessary to achieve at least 6 ksi in 7 days. Therefore, the deck slab was cast using a mix design that is typically used for prestressed girders. Girder Bar Size fy (ksi) fu (ksi) u AASHTO BI-36 No. 3 82.1 120 0.126 No. 4 72.7 112 0.128 No. 6 65.4 102 0.186 AASHTO BT-54 No. 4 69.7 107 0.127 No. 6 65.9 106 0.132 AASHTO Type III-a No. 4 63.6 100 0.191 No. 5 75.6 113 0.159 AASHTO Type III-b No. 4 63.6 100 0.191 No. 5 75.6 113 0.159 Nebraska NU-1100 No. 3 75.1 101 0.238 No. 4 79.0 106 0.254 No. 5 70.1 103 0.128 No. 6 69.2 109 0.120 Texas U-40 No. 4 70.5 110 0.157 No. 5 67.1 105 0.093 No. 6 67.6 110 0.145 Table 3.4. Measured material properties of reinforcing bars.

56 Strand Debonding for pretensioned Girders length was taken either as 60db (db = strand diameter) per AASHTO LRFD Bridge Design Speci- fications or the value obtained from Eq. 3.3 (NCHRP Report 603: Ramirez and Russell 2008). In this equation, f ′ci is the concrete strength at release, summarized in Table 3.3. The resulting calculated transfer lengths are provided in Table 3.5. l d f dt b ci b 120 40 Eq. 3.3= ′ ≥ The stress determined from Eq. 3.1 or Eq. 3.2 was divided by the concrete modulus of elastic- ity at prestress transfer (Eci) to obtain the predicted concrete strain (ec); these strains are com- pared with the measured values. The value of Eci was determined from Eq. 3.4, which has been published in the 2015 edition of AASHTO LRFD Bridge Design Specifications. E K w fc c c120,000 Eq. 3.41 2.0 0.33= ′ The value of K1 was taken as 1.0 for all the girders with the exception of Nebraska NU-1100 for which 0.85 was used (Larson et al. 2009). The value of f ′c was set equal to f ′ci (concrete strength at release), and 0.145 kcf was used for wc. The calculated and measured strains are compared in Figure 3.3. Following common practice, the effects of the end diaphragms (blocks) in girder BI-36 were neglected. The gross section prop- erties (area and moment of inertia) are smaller than their counterparts computed from trans- formed section properties. Hence, the strains based on gross section properties are, expectedly, higher than those calculated from transformed section properties. With the exception of the Texas U-40 girder, the trend of the measured data is captured reasonably well. Finite element modeling will be presented in Section 3.7.2.2 to interpret the data for Texas U-40. At some locations and Table 3.5. Release concrete strengths and calculated transfer lengths. Girder f’ci (ksi) db (in.) Calculated Transfer Lengths (in.) AASHTO (60db) NCHRP 603 (Eq. 3.3) AASHTO BI-36 7.4 0.5 30 22 (44db) AASHTO BT-54 10.2 0.6 36 24 (40db) AASHTO Type III-a 6.9 0.5 30 23 (46db) AASHTO Type III-b 8.3 0.5 30 21 (42db) Nebraska NU-1100 8.4 0.7 42 29 (41db) Texas U-40 6.9 0.6 36 27 (45db) Figure 3.2. Transition of cross-sectional area from the bulb area to the girder area.

experimental research approach, Findings, and associated analytical Simulations 57 Figure 3.3. Measured and computed longitudinal concrete strains at soffit. (c) AASHTO Type III-a (b) AASHTO BT-54 (a) AASHTO BI-36 (continued on next page)

58 Strand Debonding for pretensioned Girders Figure 3.3. (Continued). (e) Nebraska NU-1100 (f) Texas U-40 (see Section 3.7.2.2 for additional evaluation) (d) AASHTO Type III-b

experimental research approach, Findings, and associated analytical Simulations 59 for some of the girders, the calculations based on the current AASHTO transfer length cor- relate better with experimental data, whereas the transfer length recommended in NCHRP Report 603 (Ramirez and Russell 2008) yields more accurate results for some other cases. No clear conclusion can, therefore, be made about the accuracy of either transfer length calcula- tion method. For the majority of cases, the measured strains are larger than the computed values. The friction between the form and girder, which is not reflected in the calculations, would affect the boundary conditions, and, hence, the level of compressive strain in the con- crete to a small degree. 3.5 Testing Program The two ends of each girder (End A and End B), which had different amounts of strand debonding, were tested separately. In each case End B was tested first. The test specimens were extensively instrumented to capture key behavior. The test setups and instrumentation are sum- marized in this section. 3.5.1 Test Setup The girders were supported on neoprene pads similar to those typically used in construction. For single-web girders, full-flange width pads, having a thickness of 1.375 in. were provided for all the girders except for BT-54, in which 22 in. of 24.5 in. bottom flange width was supported. For AASHTO BI-36, two 9-in. wide by 3-in. thick neoprene pads were placed under each web. Two 3-in. thick neoprene pads were also placed under each web of Texas U-40. These pads engaged the outer 7-in. width of the bottom flange. During testing of End B of Texas U-40, a third pad had inadvertently been installed at the middle of the soffit at both ends. After a total load of 120 kips, the girder was unloaded, the middle pads removed, and testing resumed. Only two pads, one under each web, were placed at each end when End A was tested. The data pre- sented for the Texas U-40 herein are for the second loading of End B with only the two outer pads in place. The lengths of the pads under the soffit were 12 in. for all the girders. Displacement transducers were attached to the girder to measure the compression of pads during testing so the beam deflections could be corrected for this movement. A single concentrated load was used to test the girders. The location of the load was selected such that the shear span-to-depth ratio (a/dv) would not be less than 2.0 in order to prevent direct transfer of the load to the support through arching action. The values of a/dv are sum- marized in Table 3.6. Each end was tested separately with End B tested first. After testing End B, the girder was repositioned in order to test End A, which had a larger debonding ratio than End B. With the exception of Texas U-40, which was tested as a simply supported span, testing of each end con- sisted of a simple span with a propped cantilever overhang, as shown in Figure 3.4. To prevent cracking due to the self-weight of the cantilevered portion, an air jack was used to prop the end of the girder. The air pressure was calibrated such that the force in the jack actively compensated for the self-weight of the cantilevered portion throughout the duration of the test; thus, the girder was effectively tested as a simply supported span. At the conclusion of testing End B of AASHTO BT-54, a number of minor cracks were found to have extended into the span of End A (see Figure 3.5). In order to mitigate the effects of these cracks, the girder was vertically post-tensioned as shown in Figure 3.6 before testing End A. The total applied post-tensioning force of 120 kips was sufficient to close the small cracks. Table 3.6. Shear spans and shear span-to- depth ratios. Girder a (ft) a/dv AASHTO BI-36 5.00 2.73 AASHTO BT-54 10.0 2.34 AASHTO Type III-a 7.75 2.15 AASHTO Type III-b 7.75 2.16 Nebraska NU-1100 7.75 2.20 Texas U-40 7.75 2.39

Figure 3.4. Loading arrangements. (a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a, AASHTO Type III-b, and Nebraska NU-1100 End A P (ii) Testing of End A Air jack End B P (i) Testing of End B Air jack 5'24'10' 6" 10' 6"5' 24' End A Air jack 34' 55' P End B Air jack 20' 5" 55' 10'34' P 20' 6" 10' (i) Testing of End B (ii) Testing of End A 7' 9" 39' End B End A P P (i) Testing of End B (ii) Testing of End A Air jack Air jack 7' 9" 55' 15' 6" 39' 15'6 " (d) Texas U-40 7' 9" 32' 31' 7' 9" 32' 31' (i) Testing of End B (ii) Testing of End A P P

experimental research approach, Findings, and associated analytical Simulations 61 3.5.2 Instrumentation During fabrication of the girders, a number of electrical resistance strain gages were bonded to transverse and longitudinal reinforcing bars. Moreover, a number of electrical resistance strain gages were bonded to the second-layer strands before casting AASHTO BT-54, AASHTO Type III-a, and AASHTO Type III-b. After the girders were delivered to the University of Cincinnati Large Scale Test Facility, additional strain gages were bonded to a number of the strands. These additional gages were applied within small “knockouts” left in the girders dur- ing concrete placement in a procedure used for all specimens tested in this program. At each end, six strain gages were bonded to the concrete surface to monitor compressive strain near the top of the bridge deck. Five vibrating wire gages were placed in the concrete near the centroid Figure 3.5. Extension of cracking into End A span in AASHTO BT-54. Figure 3.6. Post-tensioning of cracked end before testing End A of AASHTO BT-54.

62 Strand Debonding for pretensioned Girders of the strands at each end. The locations and numbers of strain gages are summarized in Appendix G. The test specimens were externally instrumented to measure the slip of a number of bonded and debonded strands (the locations at which the slips were measured are provided in Appendix G), average shear deformation within the shear span, and the deflection at the load point. The vertical displacement of the girder at the center of each support was measured in order to account for the deformation of the neoprene pads. A calibrated pressure transducer was used to monitor the applied load from the hydraulic rams. 3.5.3 Test Results and Discussions With the exception of Nebraska NU-1100 and End B of Texas U-40, all the specimens were loaded to failure. Total failure at End B of Texas U-40 would have compromised, if not effec- tively prevented, the testing of End A. Therefore, End B of this girder was loaded to only its pre- dicted capacity, which will be discussed in Section 3.5.3.1. It was deemed unsafe to load the Nebraska NU-1100 girder, having 22 0.7-in. diameter strands, to failure considering the amount of energy that would have been released in the event of a catastrophic failure. This girder, there- fore, was loaded to only slightly above its predicted capacity. 3.5.3.1 Capacity, Stiffness, and Failure Mode The strains measured by the vibrating wire gages were used to infer the magnitude of prestress loss. The total losses ranged between 3% for Texas U-40 and 11% for Nebraska NU-1100. These values, in conjunction with the measured material properties, were used to calculate the expected capacity of each specimen per AASHTO LRFD Bridge Design Specifications (see Appendix H). In the calculations, the resistance factors were taken as unity since the test girders were cast under controlled conditions, the loading was well defined and known a priori, and the purpose of the calculation was to determine a predicted capacity, not a design load. The measured loads (and shears) were normalized with respect to the calculated capacities of each girder. The measured deflections were normalized with respect to the deflection measured at the calculated capacity. The resulting normalized load-deflection responses are illustrated in Figure 3.7. Table 3.7 com- pares the normalized peak loads and normalized deflections at peak load for End A and End B. In each case, End B met the current AASHTO limits on the amount of debonding, while End A exceeded these limits. Based on the presented results, the following observations are made: 1. All the specimens successfully developed their predicted capacities. The failure loads were at least 43% larger than the nominal capacities (no reduction factors) calculated based on the measured material properties and inferred prestress loss. The normalized failure loads were on the order of 20% greater when determined based on AASHTO LRFD Bridge Design Speci- fications and nominal material properties. The large amounts of debonding at End A were not detrimental to the expected load-carrying capacity of the girders. 2. With the exception of AASHTO BI-36, the normalized deflections at peak load for End A and End B are comparable. The normalized load-deflection for AASHTO BI-36 [Figure 3.7(a)] clearly illustrates that End A of this girder achieved its peak capacity at a larger deflection. 3. At peak load, which corresponds to failure if the specimen were loaded to its ultimate capac- ity, the deflection was at least 2.3 times that when the predicted capacity was developed. The large amounts of debonding did not negatively impact the “ductility” inherent in the pre- stressed girders. 4. The slopes of the normalized load-deflection relationships at End A and End B are essentially the same up to developing the predicted capacities (i.e., when the value of the normalized load is equal to 1). The larger amount of debonding at End A did not have a noticeable effect

experimental research approach, Findings, and associated analytical Simulations 63 on the overall stiffness of the girders. This observation should be expected, as the relatively small area of prestressing reinforcement does not affect the stiffness; and debonding, which is localized near the girder ends, has little or no effect on deflection. The failure patterns of the girders loaded to their ultimate capacity are summarized in Fig- ure 3.8. Based on these photographs, the failure modes were characterized as noted in this figure. The Nebraska NU-1100 and End B of Texas U-40 were not loaded to failure. The dowel action at End A of AASHTO Type III-b (shown in Figure 3.9) is believed to account for the residual strength following the initial loss of carrying capacity that is apparent in Figure 3.7(d). (a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a (d) AASHTO Type III-b (e) Nebraska NU-1100 (f) Texas U-40 End A End B A pp lie d lo ad /L o ad at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Deflection under point of application of load/Deflection measured at AASHTO capacity 0 1 2 3 4 5 6 7 End A End B A pp lie d lo ad /L oa d at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Deflection under point of application of load/Deflection measured at AASHTO capacity 0 1 2 3 4 5 6 End A End B A pp lie d lo ad /L o ad at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Deflection under point of application of load/Deflection measured at AASHTO capacity 0 1 2 3 4 5 6 7 8 9 10 End A End B A pp lie d lo ad /L oa d at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Deflection under point of application of load/Deflection measured at AASHTO capacity 0 1 2 3 4 5 6 7 8 9 10 End A End B A pp lie d lo ad /L o ad at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 Deflection under point of application of load/Deflection measured at AASHTO capacity 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 End A End B A pp lie d lo ad /L oa d at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Deflection under point of application of load/Deflection measured at AASHTO capacity 0 1 2 3 4 5 Figure 3.7. Normalized load-deflection responses.

64 Strand Debonding for pretensioned Girders Table 3.7. Comparison of normalized peak load and deflection at peak load. Girder Normalized Peak Load Normalized Deflection at Peak Load End A End B End A End B AASHTO BI-36 1.43 (1.84) 1.52 (2.04) 4.58 2.31 AASHTO BT-54 1.51 (1.95) 1.50 (1.92) 3.68 3.37 AASHTO Type III-a 1.69 (2.00) 1.78 (2.05) 5.64 5.47 AASHTO Type III-b 1.63 (1.97) 1.63 (1.92) 4.15 4.62 Nebraska NU-1100 1.21* (1.64) 0.96* (1.21) 1.37 1.00* Texas U-40 1.53 (1.80) 1.00* (1.17) 3.03 1.01* *Not loaded to failure. ( ) capacity ratio based on the nominal material properties, all applicable. AASHTO reductions, and prestressing loss determined per AASHTO LRFD Article 5.9.5.1. Failure mode: Shear compression End A Failure mode: Shear compression End B (a) AASHTO BI-36 Figure 3.8. Failure patterns and modes of failure. 3.5.3.2 Crack Patterns Photo collages of each girder at failure, shown in Figure 3.10, were assembled to determine the angles of diagonal cracks. These collages generally do not indicate any discernible differences between the crack patterns at either end of a given girder. However, for some girders (e.g., Type III-a and Type III-b), End A experienced more cracking and exhibited more of a flexure-shear behavior than End B whose behavior was predominately controlled by web shear. These observations are consistent with the smaller amount of prestressing force (due to greater debonding) at End A.

experimental research approach, Findings, and associated analytical Simulations 65 Failure mode: Shear compression End A Failure mode: Shear compression End B (c) AASHTO Type III-a Failure mode: Shear tension End A Failure mode: “Sliding shear” at the web-flange interface End B (b) AASHTO BT-54 Figure 3.8. (Continued).

Figure 3.8. (Continued). Failure mode: Shear tension and bearing End A (e) Texas U-40 End B was not loaded to failure Failure mode: Shear compression End A Failure mode: Shear compression End B (d) AASHTO Type III-b Figure 3.9. Dowel action evident in AASHTO Type III-b.

experimental research approach, Findings, and associated analytical Simulations 67 Figure 3.10. Photo collages of crack patterns. North face South face Max. dr = 0.60 End A Max. dr = 0.10 End B (b) AASHTO BT-54 North face South face Max. dr = 0.50 End A Max. dr = 0.18 End B (a) AASHTO BI-36 (continued on next page)

68 Strand Debonding for pretensioned Girders North face South face Max. dr = 0.50 End A Max. dr = 0.25 End B (c) AASHTO Type III-a North face South face Max. dr = 0.56 End A Max. dr = 0.22 End B (d) AASHTO Type III-b Figure 3.10. (Continued).

experimental research approach, Findings, and associated analytical Simulations 69 North face South face Max. dr = 0.45 End A Max. dr = 0.27 End B (e) Nebraska NU-1100 North face South face Max. dr = 0.50 End A Max. dr = 0.23 End B (f) Texas U-40 Figure 3.10. (Continued).

70 Strand Debonding for pretensioned Girders As evident from Table 3.8, the average crack angles were essentially the same for the two ends of a single girder having different debonding ratios. The crack widths at End A, which had a larger debonding ratio than End B, were generally slightly wider than those at End B. However, the maximum measured crack widths corresponding to the AASHTO-predicted capacities are small; the largest crack width was less than 0.03 in. The larger dr did not have a deleterious effect on observed crack angles or crack widths. 3.5.3.3 Shear Deformation Using the displacements measured by the diagonal displacement transducers (see Appendix G), the average shear deformations in two adjacent regions were obtained: Region 1 is approximately one-half the shear span closer to the support, and Region 2 is the other half of the shear span closer to the applied load. The relationship between the normalized shear and average shear strains in these regions is shown in Figure 3.11. In this figure, the normalizing “shear at AASHTO capacity” refers to the shear capacity determined using measured material properties, prestress loss inferred from the strains measured by the vibrating wire gages, and taking the resistance factors as unity. The diagonal sensors used to obtain this data were removed prior to reaching the failure load. The load at which the displacement transducers were removed was not always identical for End A and End B in the same girder. In general, the shear strain for a given value of applied shear at End A was larger than that at End B. The smaller amount of prestressing force (resulting from the larger dr) at End A could not restrain the growth and widening of the cracks as well as in End B. 3.5.3.4 Shear Resistance from Transverse Reinforcement The measured stress-strain relationships were used to infer stresses in the transverse rein- forcement. The measured relationships are presented in Appendix F and are modeled in the more appropriate of two ways as indicated in Appendix F. If the measured stress-strain relation- ships exhibited a well-defined yield point, a trilinear stress-strain model, such as that shown in Figure 3.12(a), was used. The values defining the model ( fy, Es, Esh, ey, and esh) were obtained based on the data from material testing (Appendix F). In the absence of a well-defined yield point, a Ramberg-Osgood (R-O) (Ramberg and Osgood 1943) function [Figure 3.12(b) and Eq. 3.5] was calibrated to fit the experimentally obtained stress-strain relationships of the reinforcing steel. This continuous function is more precise than the conventional elastic-perfectly plastic assumptions used in design. 1 1 Eq. 3.51f E A A B fss s C C pu( )= ε + − + ε    ≤ Table 3.8. Average measured angles of diagonal cracks. Girder End A End B Max. dr (deg.) wmax (in.) Max. dr (deg.) wmax (in.) AASHTO BI-36 0.50 29 0.01 0.18 30 0.01 AASHTO BT-54 0.60 34 0.025 0.10 32 0.022 AASHTO Type III-a 0.50 35 0.028 0.25 35 0.014 AASHTO Type III-b 0.56 33 0.015 0.22 34 0.025 Nebraska NU-1100 0.45 32 * 0.27 32 0.015 Texas U-40 0.50 32 0.014 0.23 34 0.01 : Average angle of diagonal cracks measured at the conclusion of testing. wmax: Maximum crack width at a load nearly equal to the AASHTO-predicted girder capacity. *: Not measured.

experimental research approach, Findings, and associated analytical Simulations 71 (a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a (d) AASHTO Type III-b (e) Nebraska NU-1100 (f) Texas U-40 End A (Region 1) End A (Region 2) End B (Region 1) End B (Region 2)Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Average shear strain (%) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 0.40 0.45 End A (Region 1) End A (Region 2) End B (Region 1) End B (Region 2)Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Average shear strain (%) 0 0.05 0.10 0.15 End A (Region 1) End A (Region 2) End B (Region 1) End B (Region 2)Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Average shear strain (%) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 End A (Region 1) End A (Region 2) End B (Region 1) End B (Region 2)Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Average shear strain (%) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 End A (Region 1) End A (Region 2) End B (Region 1) End B (Region 2)Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 Average shear strain (%) 0 0.05 0.10 0.15 0.20 End A (Region 1) End A (Region 2) End B (Region 1) End B (Region 2)Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Average shear strain (%) 0 0.05 0.10 0.15 Figure 3.11. Normalized applied shear vs. average shear strain. Where: A, B, and, C = Parameters established from a best fit of experimental stress-strain data. The values of these parameters are summarized in Appendix F. fss = Steel stress fpu = Ultimate strength Es = Modulus of elasticity usually taken as 29,000 ksi e = Strain

72 Strand Debonding for pretensioned Girders For AASHTO BT-54 and Texas U-40, the R-O model in Figure 3.12(b) was used while the stress-strain relationships for the transverse steel in the other girders were characterized based on the elastic-plastic model shown in Figure 3.12(a). The calibrated equation was used to infer stresses corresponding to the strains measured by the strain gages bonded to the transverse reinforcement. Based on Article 5.8.3 in AASHTO LRFD Bridge Design Specifications, the shear resistance provided by the transverse steel, Vs, was computed. AASHTO LRFD Eq. 5.8.3.3-4 was modified slightly by using the experimentally inferred stress ( fv) instead of the yield strength of transverse reinforcement ( fvy), as shown in Eq. 3.6. V A f d s A f d s s v v v v v vcot cot sin cot Eq. 3.6 ( ) ( ) = θ + α α = θ The value of q was selected based on the values tabulated in Table 3.8. This calculation was performed at six locations (1, 2, 3, 4, 5, and 6 ft from the ends of the girder) where the transverse reinforcement had been instrumented. Since there was no inclined prestressing strand, the dif- ference between the applied shear and the average of Vs from these six locations corresponds to the concrete contribution to shear resistance. The resulting concrete contribution to shear capacity as a function of deflection under the load point is plotted in Figure 3.13. For a given value of deflection, the concrete shear resistance at End A (greater dr) is less than its counterpart in End B. This observation is consistent with the differences in the amount of prestressing force at the two ends. The smaller prestressing force at End A resulted in more cracking and hence a reduction in the contribution of the concrete to the shear resistance, as evident from Table 3.9. This reduction at the AASHTO-predicted capacity is not, however, proportional to the relative magnitude of drs at the two ends. For instance, the concrete at End A resisted 15% less shear than End B in AASHTO BT-54, which had the greatest difference between the drs at the two ends, but AASHTO Type III-b exhibited the largest apparent reduction in concrete contribution (19%) even though the difference between the drs at its two ends was less substantial. 3.5.3.5 Apparent Strand Slip Displacement transducers measured the movements of the instrumented strands relative to the end surface of the girder (see Appendix G). For fully bonded strands, this movement is the actual slip. In the case of debonded strands, the strand is assumed to be unstressed between the point of measurement and the beginning of strand embedment (at 3, 6, 9, or 12 ft into the beam); thus, the debonded portion of strand is moving as a rigid body. However, due to flexure- and shear-induced tensile strains, the concrete mass between the end of the girder and the begin- ning of strand embedment is elongating, i.e., ecl in Figure 3.14 where ec = concrete longitudinal Figure 3.12. Modeling of stress-strain relationships for steel reinforcing. (a) Trilinear idealization of stress-strain diagram (b) Ramberg-Osgood idealization of stress- strain diagram Es y sh fy Esh Stress, fss Stress, fss Strain, Es AEs Strain, E(1-A)/B C is a measure of transition "roundness"

Figure 3.13. Concrete shear resistance vs. deflection. (a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a (d) AASHTO Type III-b (e) Nebraska NU-1100 (f) Texas U-40 End A End BSh ea r re sis ta n ce fro m co n cr et e (ki ps ) 0 30 60 90 120 150 180 210 240 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 End A End BSh ea r re sis ta n ce fro m co n cr et e (ki ps ) 0 40 80 120 160 200 240 280 320 360 400 Deflection under point of application of load (in.) 0 0.6 1.2 1.8 End A End BSh ea r re sis ta n ce fro m co n cr et e (ki ps ) 0 70 140 210 280 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 End A End BSh ea r re sis ta n ce fro m co n cr et e (ki ps ) 0 50 100 150 200 250 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 End A End BS he ar re sis ta n ce fro m co n cr et e (ki ps ) 0 40 80 120 160 200 240 280 Deflection under point of application of load (in.) 0 0.15 0.30 0.45 0.60 End A End BSh ea r re sis ta nc e fro m co n cr et e (ki ps ) 0 40 80 120 160 200 240 280 320 360 400 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 Table 3.9. Normalized concrete shear resistance at AASHTO-predicted girder capacities. Girder End A End B % Reduction in Max. dr Vc / f'cbvdv Max. dr Vc / f'cbvdv Vc / f'cbvdv AASHTO BI-36 0.50 0.19 0.18 0.20 5% AASHTO BT-54 0.60 0.17 0.10 0.20 15% AASHTO Type III-a 0.50 0.14 0.25 0.16 13% AASHTO Type III-b 0.56 0.13 0.22 0.16 19% Nebraska NU-1100 0.45 0.23 0.22 0.23 0% Texas U-40 0.50 0.24 0.22 0.26 8%

74 Strand Debonding for pretensioned Girders strain and l = the length over which the strand is debonded. The slip measured at the end of the girder on debonded strands will, therefore, be greater than the actual slip exhibited at the beginning of strand embedment (a distance l into the girder). The difference between measured slips and actual slips will, therefore, be proportional to the unbonded length (Hypothesis A). This proportionality is unlikely to be linear since the strains concerned are not uniform over the debonded lengths. The strains causing the concrete deformation can only be assessed in a very general fashion because the available data (the strains measured by the vibrating wire gages every 1 ft up to 5 ft into the girder) did not have sufficient resolution. It was, therefore, not deemed appropriate to attempt to correct measured slip values to account for ec l. The strains will also be affected by the location of the strand in the section (since a strain gradient is present) and by the extent and pattern of local cracking. Nonetheless, in a broad sense it may be hypothesized (Hypothesis B) that the concrete strains will be greater at End A because of the smaller prestressing force in com- parison to End B. The over-estimation of the actual slip at the beginning of strand embedment will, therefore, be greater at End A. The relationships between the normalized applied shear and apparent slip of bonded and debonded strands having various debonding lengths are plotted in Figure 3.15. The values of apparent slip at the AASHTO-predicted capacity are summarized in Table 3.10. Based on the presented data, the following observations about “measured slip” may be drawn: 1. At AASHTO-predicted girder capacities, measured slip rarely exceeded 0.04 in., except for Texas U-40. The measured slip of fully bonded strands was negligible in all cases. 2. In all cases, although the measured slip was negligible, the effect of specimen initial cracking is evident as a change in slope of the normalized shear-apparent slip curves. 3. Prior to initial cracking, the slope of the slip behavior is inversely proportional to the debond- ing length. This observation is consistent with Hypothesis A. 4. In all but AASHTO BT-54, considering End A strands, the measured slip is typically propor- tional to the unbonded length, which is consistent with Hypothesis A. The measured slips of AASHTO BT-54 are not entirely consistent: the strand having 9 ft debonding has the lowest measured slip of the debonded strands. 5. Beyond the AASHTO-predicted capacity, measured slip is observed to increase as cracking and, presumably, yield of strand and embedded steel takes place. 6. Comparing the post-AASHTO capacity of the fully bonded strands, End A is seen to exhibit greater slip at comparable load levels, which supports Hypothesis B. Figure 3.14. Conceptual illustration of elongation of debonded strands.

Figure 3.15. Normalized shear-apparent slip relationships. (a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a (d) AASHTO Type III-b (e) Nebraska NU-1100 (f) Texas U-40 End A (bonded) End A (debonded 3') End A (debonded 6') End A (debonded 9') End A (debonded 12') End B (bonded) End B (debonded 3') End B (debonded 6')Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Apparent slip (in.) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 0.40 0.45 0.50 0.55 End A (bonded) End A (debonded 3') End A (debonded 6') End A (debonded 9') End B (bonded) End B (debonded 3')A pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Apparent slip (in.) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 0.40 0.45 0.50 End A (bonded) End A (debonded 3') End A (debonded 6') End A (debonded 9') End B (bonded) End B (debonded 3') End B (debonded 6')Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Apparent slip (in.) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 0.40 0.45 0.50 0.55 0.60 End A (bonded) End A (debonded 3') End A (debonded 6') End A (debonded 9') End B (bonded) End B (debonded 3') End B (debonded 6')Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Apparent slip (in.) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 0.40 0.45 0.50 0.55 0.60 End A (bonded) End A (debonded 3') End A (debonded 6') End A (debonded 9') End A (debonded 12') End B (bonded) End B (debonded 3') End B (debonded 12')Ap pl ie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 Apparent slip (in.) 0 0.025 0.050 0.075 0.100 End A (bonded) End A (debonded 3') End A (debonded 6') End A (debonded 9') End B (bonded) End B (debonded 3') End B (debonded 6') End B (debonded 9')A pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Apparent slip (in.) 0 0.05 0.10 0.15 0.20 0.25 0.30 0.35 0.40 0.45 Girder Bonded Strands Debonded Strands ldebond = 3 ft ldebond = 6 ft ldebond = 9 ft ldebond = 12 ft End A End B End A End B End A End B End A End B End A End B AASHTO BI-36 < 0.001 < 0.001 0.016 0.004 0.019 < 0.001 0.016 N/A 0.002 N/A AASHTO BT-54 0.009 0.004 0.041 0.008 0.043 N/A 0.023 N/A N/A N/A AASHTO Type III-a 0.004 < 0.001 0.005 0.002 0.011 0.006 0.010 N/A N/A N/A AASHTO Type III-b < 0.001 < 0.001 0.008 < 0.001 0.018 0.006 0.022 N/A N/A N/A Nebraska NU-1100 0.005 0.002 0.033 0.011 0.035 N/A 0.039 N/A 0.040 0.030 Texas U-40 0.011 0.003 0.036 0.060 0.073 0.034 0.103 0.099 N/A N/A Table 3.10. Apparent strand slip at AASHTO-predicted capacity.

76 Strand Debonding for pretensioned Girders 7. Comparing the measured slip of the End A and End B strands having unbonded lengths of 3 ft (the only strands available for such comparison), End A, having greater debonding, exhibits greater slip except for Texas U-40. This observation supports Hypothesis B. Thus, both Hypotheses A and B are supported by experimental observations: (A) the difference between measured slips and actual slips is proportional to the unbonded length; and (B) the con- crete strains will be greater at End A because of the smaller prestressing force in comparison to End B. 3.5.3.6 Contribution of Longitudinal Reinforcement The amount of required nonprestressed longitudinal reinforcement at the critical section and at the interior face of the support had been determined according to AASHTO LRFD Eq. 5.8.3.5-1 and Eq. 5.8.3.5-2., respectively: 0.5 0.5 cot 5.8.3.5–1A f A f M d N V V Vps ps s y u v f u c u v p s [ ]+ ≥ φ + φ + φ − −     θ 0.5 cot 5.8.3.5–2A f A f V V Vps ps s y u v s p [ ]+ ≥ + φ − −     θ Based on a similar procedure discussed in Section 3.5.3.4, stresses in the nonprestressed lon- gitudinal reinforcement were inferred from the measured strains. The R-O function given by Eq. 3.5 and shown in Figure 3.12b was used for all the girders except for AASHTO BI-36 and Texas U-40 girder, for which the nonprestressed longitudinal reinforcement stress-strain relationships were based on the trilinear function depicted in Figure 3.12a. The resulting stresses normalized with respect to the nonprestressed reinforcement yield strength are plotted in Figure 3.16 against the normalized applied shear. If available, stresses at three sections are plotted: (1) at the critical section near the support, (2) dv from the interior face of the support, and (3) at the point where the load was applied. The following observations are made: 1. At AASHTO-predicted capacity (i.e., when the normalized shear is unity), the stress in the nonprestressed reinforcing steel is at most 0.56fy, as can be seen more clearly from Table 3.11. However, the longitudinal nonprestressed reinforcement is assumed to have yielded accord- ing to AASHTO LRFD Eq. 5.8.3.5-1 and Eq. 5.8.3.5-2. A plausible explanation for this dif- ference could be that AASHTO LRFD Bridge Design Specifications do not account for the tensile strength of the precompressed concrete. Hence, the available capacity (in the absence of nonprestressed reinforcement) is larger than Aps fps alone. 2. For the girders that were loaded to failure, the nonprestressed longitudinal bars had begun to yield at sections 2 and 3, i.e., at the critical section near the support and dv from the interior face of the support, respectively. 3.6 Summary The experimentally determined girder capacities exceed those computed based on AASHTO LRFD Bridge Design Specifications using the measured material properties and prestress losses with no strength reduction factor. Regardless of the drs, the measured deflection at the peak load was several times larger than the measured deflection at the calculated AASHTO capacity. The nonprestressed reinforcement used to compensate for larger prestressed reinforcing drs is adequate in terms of capacity. Even though this reinforcement cannot replicate the effects of prestressing force in bonded strands, the differences in the overall stiffness, crack widths, and

(a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a (d) AASHTO Type III-b (e) Nebraska NU-1100 (f) Texas U-40 End A (Section 2) End A (Section 3) End A (Section 4) Section 2: critical section near support Section 3: dv from the face of support Section 4: at application of load End B did not have nonprestressed reinforcementA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Stress in nonprestressed reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1.0 1.1 1.2 End A (Section 2) End A (Section 3) End A (Section 4) End B (Section 2) End B (Section 3) Section 2: critical section near support Section 3: dv from the face of support Section 4: at application of load Nonprestressed reinforcement at End B was terminated prior to Section 4.A pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Stress in nonprestressed reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1.0 1.1 End A (Section 2) End A (Section 3) End A (Section 4) End B (Section 2) End B (Section 3) End B (Section 4) Section 2: critical section near support Section 3: dv from the face of support Section 4: at application of loadA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Stress in nonprestressed reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1.0 1.1 End A (Section 2) End A (Section 3) End A (Section 4) End B (Section 2) End B (Section 3) End B (Section 4) Section 2: critical section near support Section 3: dv from the face of support Section 4: at application of loadA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Stress in nonprestressed reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1.0 1.1 End A (Section 2) End A (Section 3) End B (Section 2) End B (Section 3) Section 2: critical section near support Section 3: dv from the face of supportA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 Stress in nonprestressed reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 End A (Section 2) End A (Section 3) End B (Section 2) End B (Section 3) Section 2: critical section near support Section 3: dv from the face of support Section 4: at application of load Strain gages at Section 4 malfunctioned. A pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Stress in nonprestressed reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1.0 Figure 3.16. Normalized stress in nonprestressed longitudinal reinforcement. Girder End A End B Max. dr fs /fy Max. dr fs /fy Section 2 Section 3 Section 4 Section 2 Section 3 Section 4 AASHTO BI-36 0.50 0.03 0.11 0.21 0.18 N/A AASHTO BT-54 0.60 0.12 0.23 0.15 0.10 0.17 0.20 N/A AASHTO Type III-a 0.50 0.12 0.14 0.15 0.25 0.04 0.11 0.16 AASHTO Type III-b 0.56 0.07 0.23 0.27 0.22 0.20 0.08 0.03 Nebraska NU-1100 0.45 0.56 0.10 N/A 0.27 0.31 0.09 N/A Texas U-40 0.50 0.35 0.28 N/A 0.23 0.30 0.18 N/A Table 3.11. Normalized stress in nonprestressed longitudinal reinforcement at AASHTO-predicted girder capacities.

78 Strand Debonding for pretensioned Girders crack patterns and angle of cracks of the two girder ends, with different magnitudes of drs, were found to be small. The results are consistent with the hypothesis that bonded strand and nonprestressed tension reinforcement work together to resist longitudinal forces induced by shear (i.e., those calculated using AASHTO LRFD Eq. 5.8.3.5-1 and -2 provided the detailing rules shown in Table 3.2 and elaborated upon in Section 4.2 are satisfied). 3.7 Modeling of Test Specimens The FEM platform described in Section 2.4 and STM modeling described in Section 2.5 were applied to the test girders in order to both validate the analytical approaches and to gain a better understand of observed experimental behavior. 3.7.1 FEM Simulation of Test Girders Reinforcing steel and concrete material properties were selected based on those determined experimentally for each girder. Due to the test times, concrete properties vary from End A to End B; this variation was captured in the models. The material properties used to model each girder are summarized in Table 3.12. The transfer length was taken as 30db, which is consid- ered to be more realistic of in situ behavior than 60db used in AASHTO LRFD Bridge Design Specifications. As evident from Figure 3.17, the load-deflection responses determined from FEM predict the experimental curves quite well. The “saw tooth” behavior of the experimental curves reflects the relaxation of the applied load when loading was paused to inspect the girders for cracking and checking the data. The observed and predicted crack patterns at failure are compared in Figure 3.18. The crack patterns based on nonlinear FEM analysis replicate those observed rea- sonably well. 3.7.2 Utilization of Calibrated Analytical FEM Platform As evident from the results shown in Section 3.7.1, the overall measured responses of the test girders are quite close to those predicted by the FEM platform. Using the platform, additional analyses were conducted to (1) further evaluate the transfer lengths and (2) examine the ramifi- cations of rebonding a large number of previously debonded strands. 3.7.2.1 Transfer Length The distribution of the longitudinal strain at prestress force transfer (release) was computed by FEM analysis. As shown in Figure 3.19, the FEM results are generally close to those deter- mined using fundamental mechanics (see Section 3.4). The results for Texas U-40 girder are dis- cussed in Section 3.7.2.2. At a few locations, the strains from FEM are closer to the measured data in comparison to those from basic principles. Nevertheless, a number of the measured strains do not correspond to those based on FEM analysis. The field boundary conditions include some restraint from the forms and are therefore different from a simple span that is used in the cal- culations and analyses. 3.7.2.2 Further Evaluation of Longitudinal Strains at Release in Texas U-40 In the Texas U-40 girder, the concrete strains measured at release were markedly smaller than those determined from fundamental mechanics, AASHTO, or NCHRP Report 603 methods, all

experimental research approach, Findings, and associated analytical Simulations 79 Table 3.12. FEM material properties. Girder concrete f’c ksi BI-36 BT-54 NU-1100 End A End B End A End B End A End B 12.6 12.2 17.4 15.2 14.0 13.2 Ec ksi 6472 6434 7592 7096 6550 6513 ft psi 760 740 870 820 810 780 0.20 Slab concrete f’c ksi N/A N/A 11.4 11.2 6.9 6.1 Prestressing strand fpu ksi 270 fpi ksi 0.75fpu = 202.5 No. 3 transverse steel fy ksi N/A 65 75 fu ksi 97 101 u 0.200 0.238 No. 4 transverse steel fy ksi 68 70 79 fu ksi 103 107 106 u 0.114 0.127 0.250 No. 5 longitudinal steel fy ksi N/A N/A 70 fu ksi 103 u 0.128 No. 6 longitudinal steel fy ksi 69 66 69 fu ksi 108 106 109 u 0.144 0.132 0.120 Girder concrete f’c ksi Type III-a Type III-b Texas U-40 End A End B End A End B End A End B 12.6 12.2 13.8 13.2 12.8 12.0 Ec ksi 6473 6454 6542 6513 6511 6304 ft psi 760 750 806 780 750 730 0.20 Slab concrete f’c ksi 7.4 6.2 6.2 5.7 5.9 5.8 Prestressing strand fpu ksi 270 fpi ksi 0.75fpu = 202.5 No. 3 transverse steel fy ksi 75 N/A fu ksi 111 u 0.258 No. 4 transverse steel fy ksi 64 71 fu ksi 100 110 u 0.223 0.157 No. 5 longitudinal steel fy ksi 76 67 fu ksi 113 106 u 0.232 0.093 No. 6 longitudinal steel fy ksi N/A 68 fu ksi 110 u 0.145 using a plane sections assumption. The experimental strains were measured along the centerline of the girder at approximately the mid-depth of the bottom flange corresponding to approxi- mately location 1 shown in Figure 3.20. As seen in Figure 3.20, the strand layout was concentrated toward the webs of the girder. Due to the flexibility of the open section, the webs are expected to resist most of the flexural strains/ stresses at release. Furthermore, the axial strains are developed over the transfer length and are distributed into the concrete as a diagonal strut, rather than engaging the entire cross section immediately. Taken together, it may be expected that the strains in the flange would be notably reduced over a much longer length of the girder. This hypothesis was tested using the calibrated FEM model for the test specimen (see Section 3.7.1). Figure 3.21 shows a view of the longitudinal strains in the girder soffit confirming the hypothesis. There is a distinct shear lag effect along the girder flange. Figure 3.22 shows the measured and FEM-predicted strains along the girder following pre- stress transfer. The results from basic principles are also provided. The FEM-predicted strains

80 Strand Debonding for pretensioned Girders Figure 3.17. Measured vs. FEM-computed load-deflection relationships. (a) AASHTO BI-36 (c) AASHTO Type III-a End A End B Experimental FEM A pp lie d lo ad (ki ps ) 0 50 100 150 200 250 300 350 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 3.0 Experimental FEM A pp lie d lo ad (ki ps ) 0 50 100 150 200 250 300 350 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 3.0 End A End B Experimental FEM A pp lie d lo ad (ki ps ) 0 100 200 300 400 500 600 700 800 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 Experimental FEM A pp lie d lo ad (ki ps ) 0 100 200 300 400 500 600 700 800 0 Deflection under point of application of load (in.) 0.5 1.0 1.5 2.0 (b) AASHTO BT-54 End A End B Experimental FEM A pp lie d lo ad (ki ps ) 0 50 100 150 200 250 300 350 400 450 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 3.0 Experimental FEM A pp lie d lo ad (ki ps ) 0 50 100 150 200 250 300 350 400 450 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 3.0

experimental research approach, Findings, and associated analytical Simulations 81 (d) AASHTO Type III-b (e) Nebraska NU-1100 End A End B End A End B End A End B (f) Texas U-40 Experimental FEM A pp lie d lo ad (ki ps ) 0 100 200 300 400 500 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 3.0 Experimental FEM A pp lie d lo ad (ki ps ) 0 100 200 300 400 500 Deflection under point of application of load (in.) 0 0.5 1.0 1.5 2.0 2.5 3.0 Experimental FEM A pp lie d lo ad (ki ps ) 0 100 200 300 400 500 Deflection under point of application of load (in.) 0 0.1 0.2 0.3 0.4 0.5 0.6 Experimental FEM A pp lie d lo ad (ki ps ) 0 100 200 300 400 500 Deflection under point of application of load (in.) 0 0.1 0.2 0.3 0.4 0.5 0.6 Experimental FEM A pp lie d lo ad (ki ps ) 0 200 400 600 800 1000 Deflection under point of application of load (in.) 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 Experimental FEM A pp lie d lo ad (ki ps ) 0 200 400 600 800 1000 Deflection under point of application of load (in.) 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 Figure 3.17. (Continued).

82 Strand Debonding for pretensioned Girders (a) AASHTO BI-36 (b) AASHTO BT-54 Test specimen at failure Peak load FEM: 318 kips, Test: 297 kips FEM: 341 kips, Test: 336 kips All predicted cracks Cracks > 0.004 in. Cracks > 0.008 in. End A End B Test specimen at failure Peak load FEM: 630 kips, Test: 640 kips FEM: 720 kips, Test: 724 kips All predicted cracks Cracks > 0.004 in. Cracks > 0.008 in. End A End B Test specimen at failure Peak load FEM: 379 kips, Test: 388 kips FEM: 421 kips, Test: 446 kips All predicted cracks Cracks > 0.004 in. Cracks > 0.008 in. End A End B (c) AASHTO Type III-a Figure 3.18. Observed and FEM-predicted crack patterns.

experimental research approach, Findings, and associated analytical Simulations 83 (d) AASHTO Type III-b (e) Nebraska NU-1100 Test specimen at failure Peak load FEM: 395 kips, Test: 401 kips FEM: 440 kips, Test: 478 kips All predicted cracks Cracks > 0.004 in. Cracks > 0.008 in. End A End B Test specimen at failure Peak load FEM: 470 kips, Test: 468 kips FEM: 350 kips, Test: 346 kips All predicted cracks Cracks > 0.004 in. Cracks > 0.008 in. End A End B Test specimen at failure Peak load FEM: 890 kips, Test: 998 kips FEM: 693 kips, Test: 710 kips All predicted cracks Cracks > 0.004 in. Cracks > 0.008 in. End A End B (f) Texas U-40 Figure 3.18. (Continued).

84 Strand Debonding for pretensioned Girders Figure 3.19. Comparison of measured and computed longitudinal strains at release. (a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a

experimental research approach, Findings, and associated analytical Simulations 85 Figure 3.19. (Continued). (d) AASHTO Type III-b (e) Nebraska NU-1100 (a) End A (b) End B Figure 3.20. Cross section of U-40 test girder. Figure 3.21. Longitudinal strains along girder soffit (reverse plan view). End B End A - 0. 00 04 0 - 0. 00 03 8 - 0. 00 03 6 - 0. 00 03 4 - 0. 00 03 2 - 0. 00 03 0 - 0. 00 02 8 - 0. 00 02 6 - 0. 00 02 4 - 0. 00 02 2 - 0. 00 02 0 - 0. 00 01 8 - 0. 00 01 6 - 0. 00 01 4 - 0. 00 01 2 - 0. 00 01 0 - 0. 00 00 8 - 0. 00 00 6 - 0. 00 00 4 - 0. 00 00 2 0. 00 00 0 0. 00 00 2 0. 00 00 4 0. 00 00 6 0. 00 00 8 0. 00 01 0

86 Strand Debonding for pretensioned Girders are shown along the girder centerline (strand location 1 shown in Figure 3.20) and near the web at strand location 14 (Figure 3.20) at increments of 23.6 in. along the girder length. The FEM predictions capture the markedly reduced strains observed along the girder centerline, confirm- ing the research team’s hypothesis. 3.7.2.3 STM Simulation of Test Girders Each test girder had a single instrumented transverse tie at each end (see Appendix G). Using the measured strains, the stresses were inferred using a procedure similar to that described in Section 3.5.3.4. In Figure 3.23, the inferred stress normalized with respect to fy is plotted against the normalized applied shear. The STM was applied to both the design and as-built experimental behavior of the single-web test beams. The model parameters and results are given in Table 3.13. As is seen, the ties provided in the as-built beams exceeded the requirements determined from the STM. Additionally, when experimentally determined tie yield stress values are used, the capacity of the as-built tie details met or exceeded the predicted tie capacity demand at the ultimate observed shear (Vexp). Using the calculated tie force corresponding to Vexp (Table 3.13), the stress in each confin- ing reinforcement bar was obtained by assuming a uniform stress for all confining bars within Figure 3.22. Measured strains vs. computed values in Texas U-40.

experimental research approach, Findings, and associated analytical Simulations 87 Figure 3.23. Stress in confinement reinforcement. (a) AASHTO BI-36 (b) AASHTO BT-54 (c) AASHTO Type III-a (d) AASHTO Type III-b (e) Nebraska NU-1100 (f) Texas U-40 End A End BA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Stress in confinement reinforcement/fy 0 0.01 0.02 0.03 0.04 0.05 0.06 0.07 0.08 End A End BA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Stress in confinement reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 1.0 End A End BA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Stress in confinement reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 End A End B A pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 1.8 Stress in confinement reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 End A End BA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 Stress in confinement reinforcement/fy 0 0.1 0.2 0.3 0.4 End A End BA pp lie d sh ea r/S he ar at A A SH TO ca pa ci ty 0 0.2 0.4 0.6 0.8 1.0 1.2 1.4 1.6 Stress in confinement reinforcement/fy 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8

88 Strand Debonding for pretensioned Girders H/4 + Lbearing. Figure 3.24 illustrates the relationship between the resulting stress (normalized with respect to the yield strength) and the experimentally inferred stress. The correlation between the computed and experimental data is excellent considering the complexity of assessing behavior of confining reinforcement. All specimens appear to have experienced some degree of transverse cracking, and the transverse steel, which remained elastic in all cases, controlled such cracking. The nature of the tension tie-induced longitudinal cracking is such that it is expected to propagate from the dr BT-54 NU-1100 Type III-a Type III-b End A End B End A End B End A End B End A End B 0.60 0.11 0.45 0.38 0.50 0.30 0.56 0.29 H (in.) 60 60 49 49 51 51 51 51 N 8 18 12 16 8 12 8 14 nf 3 7 5 6 2 2 2 3 xp (in.) 7.7 6.1 9.8 9.7 8.0 8.0 8.0 7.0 yp (in.) 2.7 3.1 2.4 2.3 3.0 3.0 3.0 3.3 hb (in.) 10.5 10.5 12.7 12.7 14.5 14.5 14.5 14.5 bb (in.) 22 22 36.8 36.8 20 20 20 20 cb (in.) 6.9 6.7 10.7 11.5 7.5 8.3 7.5 7.9 0.478 0.253 0.233 0.054 0.216 0.097 0.216 0.079 Vdes, (kips) 300 341 311 277 184 201 198 236 t = Vdesign (kips) 143 86 72 15 40 20 43 19 Ties req’d (No. @ in.)1 7 @ 4.5 4 @ 9 4 @ 8 1 2 @ 25 1 2 @ 25 1 Vexp. (kips) 452 511 375 277 311 357 321 383 t = Vexp (kips) 216 129 87 15 67 35 69 30 fy of ties (ksi) 70 70 79 79 64 64 64 64 Ties req’d (No. @ in.)1 9 @ 3.4 6 @ 5.4 4 @ 8 1 3 @ 12.5 2 @ 25 4 @ 8.3 2 @ 25 Ties provided1 9 @ 3 4 @ 3 + 2 @ 6 4 @ 3 + 2 @ 6 4 @ 3 + 2 @ 6 Tie stress Figure Figure 3.23b Figure 3.23e Figure 3.23c Figure 3.23d Initial transverse cracking 0.7Vdes 0.85Vdes 0.3Vdes 0.4Vdes 0.5Vdes 1.0Vdes 0.95Vdes 1.1Vdes Maximum tie stress 0.84fy 0.73fy 0.37fy 0.22fy 0.45fy 0.20fy 0.63fy 0.26fy 1No. 4 hoops located over a distance H/4 + Lbearing; Lbearing = 12 in. in all cases Table 3.13. STM of test specimen bulb confinement. NU-1100 (End B) Type IIIa (End B) Type IIIb (End B) NU-1100 (End A) Type IIIa (End A) Type IIIa (End A) BT-54 (End B) BT-54 (End A) Best linear fit (R2 = 0.83) M ax im u m m ea su re d tie fo rc e (1/ f y) 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Predicted tie force (1/fy) 0 0.1 0.2 0.3 0.4 0.5 0.6 0.7 0.8 0.9 Figure 3.24. Predicted vs. inferred tie stress.

experimental research approach, Findings, and associated analytical Simulations 89 bearing. An example is shown in Figure 3.25 showing the 36.8 in. wide soffit of NU-1100 End A. Each transverse line is a distance of approximately H/4 (the lines are spaced at 12 in. while H/4 = 12.25 in.). The cracks resulting from loading clearly propagate from the bearing and extend as far as H/2 from the face of the bearing. 3.8 Web Cracking Web cracking has long been a concern for thin-webbed prestressed concrete girders. The AASHTO Standard Specifications for Highway Bridges (1997) required that the factored shear force be checked against the term Vcw. Vcw was defined as the shear force at the section required to create a maximum principal tensile stress of 0.125√f ′c in ksi units in the web at the neutral axis of the section resisting external loads (i.e., the composite section neutral axis for composite beams, and the non-composite neutral axis for non-composite beams). If the neutral axis fell within the top flange, the stress was calculated at the web/top flange interface. In lieu of calculating the principal stress, a simplified equation could be used. It was known that limiting the total shear force to 0.125√f ′c (ksi), which was the assumed stress required to crack the web, was conservative, but it was considered the best approach available at the time. The first edition of the AASHTO LRFD Bridge Design Specifications did not include Vcw or the companion Vci flexural shear strength checks. The sectional method (a.k.a. the modified compression field theory) in the AASHTO LRFD Bridge Design Specifications was adequate to address web-cracking issues. However, the original version of the sectional method was difficult to use and to automate in a computer code, as it required the use of tables and iteration. In 2007, AASHTO restored Vcw and Vci checks to the LRFD Bridge Design Specifications as the simplified method (Article 5.8.3.4.3). The only change from the form used in the Standard Specifications was the crack angle, q, had to be calculated when Vcw was less than Vci (the crack angle was assumed as 45° for Vci and was assumed as 45° for Vcw in the Standard Specifications). Concerns over web cracking remain. Web cracking is addressed in two articles of the cur- rent AASHTO LRFD Articles 5.8.3.4.3 and 5.8.5. Article 5.8.3.4.3 is the simplified method of determining shear resistance of concrete sections. Vcw controls near the end of the girder where debonding, if present, occurs. Hence, it is necessary to determine whether debonding has any influence on this calculation. In June 2016, the AASHTO Subcommittee on Bridges and Struc- tures (SCOBS) approved a reorganization of Section 5 of the AASHTO LRFD Bridge Design Spec- ifications for publication in 2017. As part of this reorganization, the simplified method utilizing Figure 3.25. Soffit of NU-1100 End A following testing.

90 Strand Debonding for pretensioned Girders Vcw and Vci was eliminated. Consequently, the need to determine whether debonding has any influence on the calculation of Vcw will no longer exist. However, this effect was investigated as part of this project before it was known that the article would be deleted. AASHTO LRFD Article 5.8.5 requires that the principal tensile stress in the web of segmen- tal box girders be investigated. The principal tensile stress may not exceed 0.11√ f ′c ksi under Service III loading. As part of the reorganization of Section 5, this article was extended to apply to all prestressed concrete sections with compressive strengths used for design greater than 10 ksi. In anticipation of this implementation in 2017, the effect of debonding on web principal tensile stresses was investigated. AASHTO LRFD Articles 5.8.3.4.3 and 5.8.5 were examined using the experimental data obtained as part of this project and previous studies reported in Shahawy et al. (1993 and 1996). 3.8.1 Calculation of Principal Tensile Stress The state of stress in the web is shown in Figure 3.26. The normal stress, fpc, is calculated from Eq. 3.7. f P A P e I y y M y y I M y y I pc pe nc pe nc bnc dnc bnc nc L bc c Eq. 3.7( ) ( ) ( )= − − + − + − In Eq. 3.7, compressive stresses are positive and tensile stresses are negative. The sign of each term provides the correct sense of the stress. The shear stress, v, is calculated from Eq. 3.8. (Also see Figure 3.27.) v V Q t I V Q t I dnc nc w nc L c w c Eq. 3.8= + The principal tensile web stress is then calculated from Eq. 3.9. 2 2 Eq. 3.9 2 2f f f vt pc pc − = −     + Note that the principal stress is shown as negative, indicating tension. 3.8.2 AASHTO LRFD Specifications Article 5.8.5 The following procedure was used to check the web stress in the test girders: 1. The stress was checked at the critical section, dv, from the face of the bearing pad. For simplic- ity, dv was taken as 0.9de where de is the effective depth of the beam. 2. Ppe was calculated at the critical section. The area of the prestressing steel was adjusted to account for debonded strands. Prestress losses were estimated using strain measurements from the girders. In general, this loss was between 3% and 10%. If a debonded strand was bonded before the critical section, the assumed stress in the strand was linearly interpolated if the bonded length was less than the transfer length of 60db. 3. Vdnc and Mdnc were calculated assuming a concrete unit weight of 0.150 kcf. The dead load shears and moments were small compared to the applied load; hence, variation of this assumption would not introduce appreciable error. Figure 3.26. State of web stresses. v v v v fpcfpc

experimental research approach, Findings, and associated analytical Simulations 91 4. VL and ML were calculated from the applied load at the time the first diagonal crack was visu- ally observed in the experiment. 5. Composite section properties were calculated by transforming the deck into an equivalent width of beam concrete using the modulus of elasticity computed based on concrete strength of both the beam and slab concrete measured at the time of testing; otherwise, gross section properties were used. 6. Using Eqs. 3.7, 3.8, and 3.9, the principal tensile stress was calculated at 3 points: (1) the inter- face of the bottom flange and the web, (2) the interface of the top flange and the web, and (3) the composite section neutral axis (for the non-composite BI-36, the non-composite neutral axis was used). The maximum principal tensile stress was compared to the allowable stress of 0.11√f ′c where f ′c is the measured beam concrete strength at the time of testing in ksi. Table 3.14 shows the maximum principal tensile stresses at the occurrence of web crack- ing, calculated at the three locations described in step 6. The stress at the bottom flange/web junction did not control for any of the cases shown. When the maximum principal tensile web stress is compared to the allowable value of 0.11√f ′c, the ratio exceeds 1 for all but the BI-36 box girder. That is, the calculated principal tensile stress at cracking in the web was greater than the minimum allowable stress for all but the box girder. This trend should be expected. The data Figure 3.27. Definition of Q for the area above y for the section shown. Table 3.14. Maximum principal tensile stresses for test girders (f ′c > 10 ksi). Girder End Max. dr f’c (ksi) Maximum Principal Tensile Stresses Allowable Stress 0.11 f’c (ksi) Max Stress Allowable NA Stress Allowable @ Neutral Axis (ksi) @ Web/Top Flange (ksi) @ Web/Bottom Flange (ksi) AASHTO BI-36 A 0.50 12.4 0.323 0.265 0.245 0.387 0.832 0.832 AASHTO BI-36 B 0.18 12.4 0.246 0.231 0.158 0.387 0.634 0.634 AASHTO BT- 54 A 0.60 15.0 0.564 0.616 0.304 0.428 1.44 1.32 AASHTO BT- 54 B 0.10 17.4 0.618 0.804 0.249 0.459 1.75 1.35 AASHTO Type III-a A 0.50 12.4 0.472 0.367 0.460 0.388 1.22 1.22 AASHTO Type III-a B 0.25 12.4 0.407 0.423 0.220 0.388 1.09 1.05 AASHTO Type III-b A 0.56 13.5 0.414 0.362 0.379 0.404 1.02 1.02 AASHTO Type III-b B 0.22 12.5 0.491 0.440 0.440 0.404 1.21 1.21 Nebraska NU-1100 A 0.45 13.6 0.484 0.551 0.399 0.406 1.36 1.19 Nebraska NU-1100 B 0.27 13.6 0.518 0.616 0.406 0.406 1.52 1.28 Texas U-40 A 0.50 12.0 0.506 0.473 0.303 0.381 1.33 1.33 Texas U 40 B 0.23 12.0 0.583 0.586 0.220 0.381 1.54 1.53 Controlling stress is in bold.

92 Strand Debonding for pretensioned Girders for the BI-36 appear to be an anomaly and will be discussed later. Assuming the anomaly of the BI-36 can be explained, the data would indicate that the proposed changes to Article 5.8.5 requiring the principal tensile stress be checked in the webs of all prestressed girders with design strengths above 10 ksi would remain appropriate even for heavily debonded girders such as those described here. Table 3.14 also shows that checking the stress only at the neutral axis is sufficient for all but the box girders. All of the girders in this experimental program had measured concrete strengths exceed- ing 10 ksi. Data reported in Shahawy et al. (1993 and 1996) were used to examine the proposed changes to the AASHTO LRFD Specifications Article 5.8.5 for cases with concrete strengths less than 10 ksi. Using information found in the references, the principal tensile stress check was conducted for the girders with debonded strands where cracking data was available. Based on the previous observations, the maximum principal tensile stress was computed only at the neutral axis of composite section. The cracking load was taken from diagrams provided in the Shahawy et al. 1993 reference. The only concrete strength reported was an average strength of 7 ksi (Shahawy et al. 1996). This value was used for both the girders and the slabs. Table 3.15 shows the results of this analysis. All of the girders reported by Shahawy et al. meet the provision of the calculated principal stress at first cracking exceeding 0.11√f ′c. The smallest ratio is 1.48 and several exceed 2.0. Hence, the proposed provision of Article 5.8.5, which does not require a principal tensile stress check for pretensioned girders with concrete strengths below 10 ksi, appears to be acceptable. 3.8.3 AASHTO LRFD Specifications Article 5.8.3.4.3 The proposed revision to Article 5.8.5 will require a stress check all along the height of the web since the maximum principal tensile stress may not occur at the neutral axis. The data shown in Table 3.14, except that for the BI-36 girder, suggest that checking the stress at the neutral axis is sufficient to prevent web cracking for girders with debonded strands. The value of the stirrup contribution, Vs, to shear capacity depends on the angle of the crack intersecting the stirrups. Based on a Mohr’s Circle analysis, the angle of the crack, q, can be calculated as (Eq. 3.10): 0.5arctan 2 Eq. 3.10 v fpc θ =    Specimen I.D. Max. dr Ratio of Calculated Principal Tensile Stress at NA of Composite Section to 0.11 f’c A2-25-3R N 0.25 2.11 A2-25-3R S 0.25 1.85 A2-50-3R N 0.50 1.78 A2-50-3R S 0.50 1.73 C0-50-R N 0.50 2.42 C0-50-R S 0.50 1.48 C1-25-R N 0.25 1.59 C1-25-R S 0.25 1.52 C1-50-R N 0.50 1.72 C1-50-R S 0.50 1.48 Table 3.15. Maximum principal tensile stresses for Shahawy et al. girders (f ′c < 10 ksi).

experimental research approach, Findings, and associated analytical Simulations 93 In the current version of the AASHTO LRFD Specifications, the crack angle used for deter- mining Vs in conjunction with Vcw is calculated from Eq. 5.8.3.4.3-4 (Eq. 3.11). cot 1.0 3 1.8 Eq. 3.11 f f pc c θ = + ′     ≤ In Table 3.16, the angle calculated from Mohr’s Circle (Eq. 3.10) and that from AASHTO LRFD Eq. 5.8.3.4.3-4 (Eq. 3.11) are compared to the average measured crack angle. All calcu- lations were performed at the neutral axis as the AASHTO equation was developed for crack angles at the neutral axis, and the experimental crack angles were measured at the neutral axis. The angle predicted by the LRFD equations agrees quite well with the angle predicted by Mohr’s Circle, and both agree reasonably well with the measured angles. One important observation is that the measured angles on the “A” ends do not agree as well with the predictions as the “B” ends; the angles on the “A” ends tend to be shallower than predicted. The “A” ends all have the higher drs. In both the Mohr’s Circle and the AASHTO equations, increasing fpc results in a shallower angle. A possible conclusion from the experimental data is that the crack angle on End A is shal- lower due to a higher fpc, and the higher fpc may be caused by the prestressing force being higher than calculated. The higher stress is likely caused by the fact that the calculation assumes that stress in debonded strands after they are rebonded is linear over the transfer length of 60db. In reality, the stress is not linear and the transfer length is likely less than 60db. Thus, the prestress- ing force at the section is likely higher than assumed; this difference would be more pronounced at End A having large drs. When using the simplified method for design, the maximum factored shear force must be less than Vcw in the areas where Vcw controls. Thus, Vcw + Vs should be compared to the total shear force at failure. However, Vcw is defined as the shear force that causes the principal tensile stress to exceed 0.125√f ′c (ksi), which is assumed to crack the web. Thus, it may be appropri- ate also to compare Vcw to the load that causes cracking in the web. Table 3.17 presents both comparisons. Note that the data from Shahawy et al. (1993, 1996) are not included in this table because Vcw had been checked using the Standard Specifications that tend to produce results that are more conservative than those obtained based on AASHTO LRFD Bridge Design Specifications. Girder End Max. dr Measured Angle (deg.) Mohr's Circle (deg.) Eq. 3.10 AASHTO LRFD (deg.) Eq. 3.11 Measured Mohr's Circle Measured AASHTO AASHTO BI-36 A 0.50 28.8 31.3 34.2 0.92 0.84 AASHTO BI-36 B 0.18 29.7 24.8 29.5 1.20 1.01 AASHTO BT-54 A 0.60 33.9 37.5 37.9 0.90 0.89 AASHTO BT-54 B 0.10 31.5 34.3 32.9 0.92 0.96 AASHTO Type III-a A 0.50 34.7 34.7 35.9 1.00 0.97 AASHTO Type III-a B 0.25 34.9 34.3 34.0 1.02 1.03 AASHTO Type III-b A 0.56 32.6 35.5 36.0 0.92 0.90 AASHTO Type III-b B 0.22 33.6 31.3 32.8 1.07 1.02 Nebraska NU-1100 A 0.46 32.3 32.9 32.9 0.98 0.98 Nebraska NU-1100 B 0.27 31.8 31.9 31.0 1.00 1.03 Texas U-40 A 0.50 32.0 38.4 38.5 0.83 0.83 Texas U-40 B 0.23 34.0 37.4 36.7 0.91 0.94 Table 3.16. Crack angles for test girders.

94 Strand Debonding for pretensioned Girders The data shown in Table 3.17 indicate that, for all but the BI-36 girder, the total applied shear force at cracking exceeds Vcw, and the total shear force at failure exceeds Vcw + Vs in all cases except End B in NU-1100; however, this girder end was not loaded to failure. The results shown in Tables 3.16 and 3.17 indicate that no change would be needed to Arti- cle 5.8.3.4.3. Vcw is a conservative prediction of the shear force at failure for all girders tested to failure, and is a conservative prediction of web cracking for all but the box girders (which are addressed below). 3.8.4 Evaluation of Data for AASHTO BI-36 Test Girder As indicated in the two previous sections, the BI-36 box girder did not satisfy the criterion of the maximum principal tensile stress in the web at the time of first cracking, i.e., the measured principal stress at cracking was less than 0.11√f ′c . Two plausible explanations are provided in the following: The box girder was the only non-composite sections tested. If Eq. 3.9 is rearranged, Eq. 12 is obtained: Eq. 3.12 2 v f f fpc t t( )= + Increasing fpc increases v, which increases the shear force (and the load) that causes cracking. In a non-composite girder, fpc = Ppe/Anc. The other terms are bending terms, which are zero at the neutral axis of non-composite girders. If the value of Ppe is overestimated, the cracking load will be overestimated, or restated, for a given load; overestimating Ppe will underestimate the principal tensile stress in the web. Increasing fpc would also increase Vcw; thus, underestimating the loss of prestressing force would increase the value of Vcw. Using the data from the box girder, a “what if ” analysis was done. In order to obtain the observed cracking load, the prestress losses would have to be between 35% and 50%. This loss is clearly unre- alistic as prestressing force losses are usually 15%–25%, and those values occur after a very long time. The girder was 97 days old when End B was tested, and 105 days old at the time of testing of End A; hence, the losses would be expected to be less than 15%–25%. Table 3.17. Comparison of Vcw to cracking shear and measured maximum shear. Girder End Measured V at Cracking (kips) Calculated Vcw (kips) Measured V at Failure (kips) Calculated Vcw+Vs (kips) AASHTO BI-36 A 106 106 246 205 AASHTO BI-36 B 106 135 278 255 AASHTO BT-54 A 209 127 452 241 AASHTO BT-54 B 256 154 511 291 AASHTO Type III-a A 155 119 311 215 AASHTO Type III-a B 187 132 357 235 AASHTO Type III-b A 171 123 321 219 AASHTO Type III-b B 171 145 383 253 Nebraska NU-1100 A 176 120 375* 316 Nebraska NU-1100 B 196 116 277* 301 Texas U-40 A 286 167 748 433 Texas U-40 B 345 187 532* 474 *Not loaded to failure

experimental research approach, Findings, and associated analytical Simulations 95 A second explanation is that the critical section is in the hollow section of the box, which is 4 in. from the solid end diaphragm. The transition from the solid end diaphragm to the hollow section creates a disturbed region (D region) and the equations for shear and bending stresses do not apply. This hypothesis was examined by comparing the stresses calculated from fundamental mechanics (Mohr’s Circle) to those predicted by the calibrated FEM models. The stresses were computed for three girders: (1) AASHTO BI-36 with end diaphragms, (2) AASHTO Type III-b with a single web, and (3) Texas U-40 that did not have end diaphragms. The results shown in Table 3.18 indicate that the locations of peak stresses from basic principles and FEM analysis are essentially identical, and that basic principles are sufficiently accurate to estimate the peak stresses for the AASHTO Type III-b and Texas U-40 but not the AASHTO BI-36. Basic prin- ciples are based on the Bernoulli beam assumption (i.e., plane sections remain plane), which are not applicable to D regions. For the AASHTO BI-36, the FEM model shows almost twice the stress calculated from basic principles (Mohr’s Circle). In areas within h of concrete end diaphragms, a more exact analysis of the web stresses is needed to obtain appropriate values. Because this is impractical in a design situation, the calcu- lated tensile stress should be limited to 0.08 fc′ ksi under the Service I limit state. Table 3.18. Comparison of stresses at the onset of web cracking. AASHTO BI- 36 AASHTO Type III-b Texas U-40 End A End B End A End B End A End B Applied load (kips) 120 120 200 200 360 440 Peak principal stress (psi) from FEM 687 607 392 435 514 435 Location of peak stress from FEM Near N.A. N.A. N.A. N.A. Approximately @ N.A. Near top flange Stress (psi) from basic principles 323 246 472 407 506 586 Location of peak stress from basic principles N.A. N.A. N.A. N.A. N.A. Top flange/web Stress from basic principles/FEM stress 0.47 0.41 1.20 0.94 0.98 1.35 N.A. = Neutral axis.

TRB's National Cooperative Highway Research Program (NCHRP) Research Report 849: Strand Debonding for Pretensioned Girders provides proposed revisions to the current debonding provisions found within the American Association of State Highway and Transportation Officials (AASHTO) Load and Resistance Factor Design (LRFD) Bridge Design Specifications with detailed examples of the application of the proposed revisions. The proposed revisions are based on comprehensive analytical and testing programs for investigating the effects of end anchorages, beam sections, end-diaphragm details, concrete strengths up to 15 ksi, and strand sizes.

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  • Chapter 3: Home

Introduction to Quantitative Research Design

Quantitative research: target population and sample, script for purpose statement in quantitative methodology.

  • Qualitative Descriptive Design
  • Qualitative Narrative Inquiry Research
  • SAGE Research Methods
  • Alignment of Dissertation Components for DIS-9902ABC
  • IRB Resources This link opens in a new window
  • Research Examples (SAGE) This link opens in a new window
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The first step in developing research is identifying the appropriate quantitative design as well as target population and sample. 

Please access the NU library database "SAGE Research Methods" for help in identifying the appropriate design for your quantitative dissertation.

Quantitative studies are experimental, quasi-experimental, or non-experimental. 

Experimental is the traditional study you may be familiar with – random sampling and experimental and control groups investigating the cause-and-effect relationship between dependent variable(s) and independent variable(s). The independent variable is manipulated by the researcher. The researcher also designs the intervention. Some examples of designs are independent measures/between groups, repeated measures/with-in groups, and matched pairs. 

Quasi-experimental is when the sample cannot be randomly sampled but still focuses on the cause-and-effect relationship between dependent variable(s) and independent variable(s). The researcher does not have control over the intervention, i.e., the groups already exist, and the independent variable (intervention/treatment) is not manipulated. The intervention/treatment has usually occurred prior to the current study. Control groups can be used but are not required like in an experimental study. Some examples of designs are causal comparative, regression analysis, and pre-test/posttest.

NOTE: Quasi-experimental is often used interchangeably with ex-post facto design, which means “after the fact.”

Non-experimental is when the sample is not randomly sampled and cause-and-effect are neither desired nor possible. These studies often can find a relationship between variables, but not which variable caused the other to change. Therefore, these studies do not have dependent nor independent variables.  Some examples of designs are correlational, cross-sectional, and observational.  

The primary non-experimental quantitative design is correlational. However, you need to keep in mind that correlational just confirms if a relationship exists between two variables, not the degree or strength of that relationship NOR the cause of the relationship. 

NOTE: Variables in correlational studies are NOT dependent and independent, they are just variables. 

If you wish to conduct a more rigorous type of quantitative study still looking at relationships, you can choose regression analysis, which will demonstrate how one variable affects the other. In regression analysis, the “independent variable(s)” should be referred to as “predictor variable(s)” and the “dependent variable(s)” as “outcome variable(s).” 

Also, a causal-comparative design (which is a quasi-experimental design) can help determine differences between groups due to an independent variable’s effect on them.

The Target Population.

The target population is the population that the sample will be drawn from. It is all individuals who possess the desired characteristics (inclusion criteria) to participate in the Dissertation.

The sampling design represents the plan for obtaining a sample from the target population. A sampling frame can be employed to identify participants and can provide access to the population for recruitment of sample. 

The Sampling Frame.

To identify all individuals in the dissertation population a sampling frame is identified and provides access to the population for recruitment of sample. Review Trochim's Knowledge Base at http://www.socialresearchmethods.net/kb/ for more information.

Exercise #1

Use the script below by replacing the italicized text with the appropriate information to state the target population.

"The target population for the proposed study is comprised of all (individuals with relevant characteristics), within (describe the sampling frame)."

The Study Sample.

The sample is a subset of the target population. Participants comprise the sample and should be labeled with relevant characteristics to the dissertation. The sampling method is the technique used to obtain the sample. Review Trochim's Knowledge Base at http://www.socialresearchmethods.net/kb/ for more information. 

A G*Power analysis is often conducted to determine the minimum sample size needed for a quantitative study.  There are calculators to help with this analysis - https://www.psychologie.hhu.de/arbeitsgruppen/allgemeine-psychologie-und-arbeitspsychologie/gpower.html.

NOTE: It is important to understand the target population to determine the correct minimum sample size.

Exercise #2

Use the script below to state the sample.

"A (sampling method) was used to determine a sample of (sample number) participants to be recruited for this study. The following inclusion criteria (list relevant characteristics needed to participate) must be met."

Creswell (2003) advised the following script for purpose statements in quantitative methodology:

“The purpose of this _____________________ (experiment? survey?) project is (was? will be?) to test the theory of _________________that _________________ (compares? relates?) the ___________(independent variable) to _________________________(dependent variable), controlling for _______________________ (control variables) for ___________________ (participants) at _________________________ (site). The independent variable(s) _____________________ will be generally defined as _______________________ (provide a general definition). The dependent variable(s) will be generally defined as _____________________ (provide a general definition), and the control and intervening variables(s), _________________ (identify the control and intervening variables) will be statistically controlled in this project” (pg. 97).

Creswell, J. (2003). Research design: Qualitative, quantitative and mixed methods approaches (2nd ed.) .  SAGE Publications.

  • << Previous: Chapter 3: Home
  • Next: Developing the Qualitative Research Design >>
  • Last Updated: Nov 2, 2023 10:17 AM
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Experimental Study of Multiphase Flow in Porous Media during CO2 Geo-Sequestration Processes pp 51–89 Cite as

Experimental Setup, Material and Procedure

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Part of the book series: Springer Theses ((Springer Theses))

A major part of the experimental work related to this research, consisting of a number of different types of core-flooding experiments, was carried out using the state-of-the-art, high pressure-high temperature, three-phase steady-state core-flooding apparatus located within the Department of Petroleum Engineering at Curtin University. To be able to achieve the objectives of this research program, various types of flooding experiments were designed and carried out using the above-mentioned core-flooding rig. In the first part of this chapter a detailed description of the experimental apparatus and its various components is presented.

  • Relative Permeability
  • Overburden Pressure
  • Flooding Experiment
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  • Gravity Segregation

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Saeedi, A. (2012). Experimental Setup, Material and Procedure. In: Experimental Study of Multiphase Flow in Porous Media during CO2 Geo-Sequestration Processes. Springer Theses. Springer, Berlin, Heidelberg. https://doi.org/10.1007/978-3-642-25041-5_3

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Regions & Countries

3. christianity’s place in politics, and ‘christian nationalism’.

Most Americans express support for the principle of separation of church and state. And few say they think the federal government should declare Christianity to be the official religion of the United States.

But many Americans do think that even though the U.S. shouldn’t officially be declared a Christian country, the federal government should promote Christian moral values. And half of U.S. adults say they think the Bible should have at least some influence in U.S. laws, including 28% who say that if the Bible conflicts with the will of the people, the Bible should have more sway.

Fewer than half of U.S. adults say they have ever heard or read anything about Christian nationalism, including 5% who say they have a favorable view of it and 25% who say they have an unfavorable view.

How much influence should the Bible have on U.S. laws?

U.S. adults are divided over the amount of influence the Bible should have on the country’s laws. About half of adults (49%) say the Bible should have “a great deal” (23%) or “some” influence (26%), while 51% say it should have “not much” or “none at all.”

Table shows Republicans twice as likely as Democrats to say the Bible should have at least some influence on U.S. laws

This is the third time we’ve asked this question in the last four years, and responses have remained fairly steady over that time .

White evangelical Protestants are more likely than adults in most other groups to say the Bible should have at least some influence on U.S. laws (86%) – including 55% who say the Bible should have “a great deal” of influence. A majority of Hispanic Protestants (78%) and Black Protestants (74%) also think the Bible should hold at least some influence on the country’s laws.

By contrast, 80% of religiously unaffiliated adults, 79% of Jews and 57% of Muslims say the Bible should not have influence on the laws of the United States. This includes 84% of atheists and 78% of agnostics who say the Bible should have no influence at all.

There also are large political divides on this topic. While 67% of Republicans and Republican leaners say the Bible should influence U.S. laws at least some, only 32% of Democrats and Democratic leaners share this opinion.

Younger adults and college graduates are less likely than other adults to say that the Bible should have at least some influence on U.S. laws.

What should happen when the Bible and the will of the people conflict?

Respondents who said the Bible should have at least some influence on U.S. laws were asked a follow-up question: When the Bible and the will of the people conflict with each other, which should have more influence?

Overall, 28% of U.S. adults say the Bible should have influence over U.S. laws and that it should take priority over the will of the people if the two conflict, while 19% say the Bible should have influence but that the will of the people should take precedence.

White evangelical Protestants and Hispanic Protestants are more likely than those in other religious groups to say the Bible should carry more weight in U.S. laws than the will of the people – 64% and 61%, respectively, say the Bible should have more influence on laws when the Bible and the will of the people conflict. And 49% of Black Protestants voice this opinion.

Among Catholics, 24% say the Bible should have more influence than the will of the people if the two conflict, 23% say the will of the people should take precedence over the Bible, and 50% say the Bible should have little or no influence on U.S. laws.

Republicans are much more likely than Democrats to say the Bible should have more influence than the will of the people when the two conflict (42% vs. 16%).

Table shows 42% of Republicans say that when they conflict, the Bible should take priority over the will of the people in U.S. laws

How much influence does the Bible have on U.S. laws today?

Distinct from their preferences on how much influence the Bible should have on U.S. laws, a majority of adults (57%) say they think the Bible currently does have at least some influence on this country’s laws.

Table shows 45% of atheists say the Bible currently has a great deal of influence on U.S. laws

Atheists (86%) and agnostics (83%) are far more likely than people in other religious groups to say the Bible has influence on U.S. laws.

And 73% of Jewish respondents say the Bible has a great deal of or some influence over today’s laws.

Black Protestants are the only group in which a clear majority says the Bible does not currently have much influence on the country’s laws.

Democrats are significantly more likely than Republicans to think the Bible has at least some influence on today’s laws (67% vs. 48%).

Should the government stop enforcing church-state separation?

Just over half of Americans say the federal government should enforce the separation of church and state (55%) – virtually unchanged from when we asked this question three years ago .

Table shows 16% of Americans want to stop enforcement of church-state separation

Meanwhile, 16% of U.S. adults say the government should stop enforcing church-state separation. And 28% of Americans say they have no opinion on this question or that neither option represents their views.

Almost all atheists (95%) say church-state separation should continue to be enforced by the federal government. Agnostics (89%) and Jews (84%) also are widely in favor of continued enforcement.

On the other hand, White evangelical Protestants are almost equally divided on this question: 35% say they favor federal enforcement of church-state separation, 31% say the government should stop enforcing this separation, and 32% choose neither of these options.

White evangelical Protestants are more likely than any of the other religious groups in this analysis to say the government should stop enforcing church-state separation.

Republicans are about twice as likely as Democrats to say the federal government should stop enforcing church-state separation (23% vs. 10%). But Republicans express more support for separation of church and state than opposition to it (43% vs. 23%).

Meanwhile, a clear majority of Democrats support the government enforcing the separation of church and state (68%).

Americans with a college degree are significantly more likely than other adults to say the federal government should enforce the separation of church and state.

Should the federal government declare Christianity the country’s official religion?

Survey respondents were asked to pick which of three statements best aligns with their views:

  • The federal government should declare Christianity the official religion of the United States.
  • The federal government should not declare Christianity the official religion of the United States, but it should promote Christian moral values.
  • The federal government should not declare Christianity the official religion of the United States, and it should not promote Christian moral values.

Table shows Most Christians say the government should promote Christian values

An overwhelming majority of Americans – 83% – say the government should not declare Christianity the official religion of the country. Only 13% of Americans support declaring Christianity as the national religion.  (In our 2021 survey, a different question found a similar result on this topic.)

Another 44% of U.S. adults say the government should not declare the U.S. a Christian nation but should promote Christian values.

The remaining 39% do not want the government to promote Christian values or to declare a Christian nation.

A slim majority of Christians say they want the government to promote Christian values without declaring an official religion. In other religious groups, respondents most commonly say the government should neither declare a Christian nation nor promote Christian values. Atheists (90%) are particularly likely to fall in this camp.

While relatively few people say the federal government should declare Christianity the official religion of the U.S., this view is somewhat more common among White evangelical Protestants, Black Protestants and Hispanic Protestants. About a quarter in each group expresses this opinion.

Most Republicans (57%) say the federal government should promote Christian moral values but not declare the U.S. a Christian nation, while most Democrats (58%) say the government should not promote Christian values or declare the U.S a Christian nation.

Republicans also are more likely than Democrats to say Christianity should be declared the official national religion (21% vs. 7%).

Young adults are more likely than older adults to say that the government should neither declare Christianity the country’s official religion nor promote Christian moral values.

Do Americans know about ‘Christian nationalism’?

A slim majority of U.S. adults (54%) say they have heard or read “nothing at all” about “Christian nationalism” – the same share who said this when we asked this question two years ago .

Among the 45% who have heard anything about Christian nationalism, relatively few say they’ve heard “a great deal” (6%) or “quite a bit” (9%). More Americans say they’ve heard or read “some” (16%) or “a little” (14%) about Christian nationalism.

Table shows Slim majority of Americans have never heard of Christian nationalism

Most atheists, agnostics and Jews have heard at least a little about Christian nationalism. By contrast, 60% of Christians say they have heard or read nothing at all about it.

Views of Christian nationalism

Respondents who had heard or read anything about Christian nationalism were then asked a follow-up question: All in all, do you have a favorable or unfavorable view of Christian nationalism?

Table shows Unfavorable views of Christian nationalism are more common than favorable views

Overall, 25% of U.S. adults say they have heard of Christian nationalism and have an unfavorable view of it. Far fewer adults say they have a favorable view of Christian nationalism (5%).

There are no religious groups in which more people have a favorable than unfavorable view of Christian nationalism.

And some religious groups are particularly likely to hold an unfavorable view. For instance, 49% of Jewish respondents have an unfavorable view of Christian nationalism, while 1% say they have a favorable view.

Democrats are far more likely than Republicans to have heard about Christian nationalism and to have an unfavorable view of it. Most Republicans say they have never heard of Christian nationalism.

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Table of contents, 5 facts about religion and americans’ views of donald trump, u.s. christians more likely than ‘nones’ to say situation at the border is a crisis, from businesses and banks to colleges and churches: americans’ views of u.s. institutions, most u.s. parents pass along their religion and politics to their children, growing share of americans see the supreme court as ‘friendly’ toward religion, most popular.

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research chapter 3 experimental

The Mandalorian: Doctor Pershing's Research Was a Reference to Snoke

  • The Mandalorian's story connects past and future of Star Wars universe, hinting at Snoke and Palpatine's origins.
  • Season 3 starts strong with Din Djarin's mission and introduces clone army based on Moff Gideon's genetic template.
  • Dr. Pershing's cloning research leads to creation of Snoke, with ties to Palpatine's futile efforts for immortality.

Ever since old Ben Kenobi mentioned "the clone wars" in Star Wars: A New Hope , this is a universe whose stories are told out of order. So, it should come as no surprise that The Mandalorian wouldn't just link to the characters of this universe's past but also point towards its future. Specifically, Din Djarin and Grogu's story inevitably leads to the galaxy's future, as shown in the sequel trilogy of films. While the series has hinted and teased at this, The Mandalorian has drawn a distinct line from its story to the mysterious Supreme Leader Snoke of the First Order.

Even though viewership was slightly down , The Mandalorian Season 3 started with a bang. "The Apostate" set up Din Darin's mission to be absolved of his sins against the Mandalorian Creed, and "The Mines of Mandalore" showed him accomplishing that task. Along the way, the series confirmed the existence of the Mythosaur, reintroduced Bo-Katan and showed Grogu starting to advance his command of the Force. However, "Chapter 19: The Convert" unexpectedly brought Doctor Pershing back into the fold. Because the first two episodes were heavily focused on Mandalorian culture, it was surprising to see Dr. Pershing. After being captured in Season 2, the scientist entered the New Republic's Amnesty Program, and by "The Convert," he was well on his way to becoming a fully incorporated member of society. Unfortunately for him, the episode ended by connecting him to the future development of Supreme Leader Snoke.

Updated March 19, 2024, by Joshua M. Patton: When Season 3 came to a close, The Mandalorian revealed the connection wasn't quite as direct as some fans predicted. Rather than trying to remake Palpatine, Moff Gideon wanted to remake the Empire in his own image. Literally, he cloned himself, hoping to give those clones the power to touch the Force with Grogu's blood. Still, this series provides an important puzzle piece to figure out the "somehow" in "Somehow, Palpatine returned." This article has been updated to include references to Project Necromancer beyond The Mandalorian and conform to CBR's current formatting standards.

Emperor Palpatine Wanted to Revolutionize Cloning

Clones have had a long and complicated history in Star Wars, but George Lucas finally ironed things out in the prequels. At the request of Sifo Dyas, the Kaminoans used Jango Fett's DNA template to create a clone army for the Republic. After the Clone Wars, Palpatine had Kamino destroyed. Before he did, however, a special forces group of clones known colloquially as "the Bad Batch" escaped the Empire with Omega, a female copy of Jango Fett's genetic template but "improved" with the mutational enhancements present in Clone Force 99.

After Kamino's destruction, some clones started to get suspicious. Captain Rex tried to help one who had evidence of Admiral Rampart's destruction of Kamino. With the help of Senator Ryo Chuchi and Bail Organa, Clone Force 99 and Rex recovered that evidence. They did this to save the Clone Troopers, but it didn't work. The Emperor used that scandal as a pretext to decommission the Clone Army and replace them with Stormtroopers. The Bad Batch Season 3 is finishing that story, but the animated series has also shown that Palpatine wasn't anywhere near done cloning things.

After Kamino was destroyed, the Empire kidnapped Kaminoan scientist Nala Se and sent her to a hidden lab on Mount Tantiss. While she refused to cooperate initially, the assumption is that she'll eventually work with Dr. Hemlock and advance the Imperials' cloning abilities. During a tour of the Tantiss lab, Emperor Palpatine told Dr. Hemlock, the evil lead scientist, that his work was the "most important" to securing the Empire's future. In particular, Palpatine was talking about Project Necromancer, in which Hemlock was trying to find a way to transfer an "M-count" from an original to a clone .

Viewers of The Mandalorian already know this means allowing clones to wield the Force like Jedi, something Kaminoan clones can't typically do. However, Nala Se was presumably already working on this. Omega's blood allows for a perfect M-count transfer.

Kaminoan Cloning Verses Imperial Strand Casting

Flash forward a few decades, and Dr. Pershing was the next generation of Mount Tantiss scientists. (At least that's what his uniform indicates.) Fans will have to wait until the finale of The Bad Batch series to find out what Hemlock and his group accomplished (and Omega's fate). However, Dr. Pershing had his own goals. Since he was introduced, fans have assumed that Pershing was trying to use Grogu to practice cloning Force-sensitive individuals. I n a video discovered by Din Djarin, Cara Dune and Greef Karga, Pershing spoke of the little Jedi's "M-count." Also, there were deformed attempts at creating clones in the facility which bore some resemblance to Snoke's deformities.

Then, "The Convert" went and made things even worse. It revealed that his work was something revolutionary. While the Kaminoans had mastered the art of replicating an individual, Pershing admitted that he was working on the way to create strand-casts. Those strand-casts use two or more individuals' DNA to create a whole new person. While the limits of this science are unclear, it means that any two people in the Star Wars universe could be paired this way to create an "offspring." However, the process was difficult and seemingly had a high failure rate.

Of course, Pershing had wanted his efforts to be used for medical improvements, not remaking the most evil Sith ever to have lived. But Moff Gideon had commandeered the project for his own evil ends. He used Pershing's technology to create a clone army based on his genetic template. These soldiers could touch the Force with Grogu's blood, which helped with the M-count transfer. However, Din Djarin, Bo Katan and the other Mandalorians destroyed these clones and, presumably, Gideon when they retook Mandalore. However, Pershing's work lived on to create Snoke and, it seems, Rey Skywalker.

How The Mandalorian's Dr. Pershing Ties Into the Creation of Snoke

The mandalorian star reveals why din djarin kept his helmet on in season 3.

The book The Secrets of the Sith by Marc Sumerak details how Emperor Palpatine used this technology to continue his futile effort to attain immortality. When direct cloning of his body didn't work, he tried strand-casting. However, his powerful Sith essence caused these new bodies to decay so fast that he was confined to Exegol. The book reveals that most of the experiments did not survive, at least not until a strand cast that came to be known as Snoke beat the odds . His body couldn't contain Palpatine's consciousness, but the tall humanoid was powerful in the Force. Palpatine used him as a puppet, at least before Snoke's untimely death . However, the purpose of the Snoke clone was to train Ben Solo in the dark side. Once the young Jedi killed his master, a Sith rite of passage, he would discover Exegol and Palpatine hoped to use his body as his vessel.

However, another strand-cast who lived would provide Palpatine a different option. Dathan was an early strand-cast who survived, and Palpatine considered him his "son." Yet, since the boy could not touch the Force, Palpatine grew to hate him. He allowed Dathan to flee because he felt the Palpatine blood in his veins might produce a worthy heir. Once Rey was born, the daughter of Dathan and a human woman named Miramar, Palpatine sent Ochi of Bestoon to hunt them down and bring him the girl. He failed, and Rey embraced the Skywalker legacy instead of the dark side of one of her biological grandfathers.

Still, all this means Dr. Pershing's research is directly related to the eventual creation of the First Order's leader. Granted, Pershing may be out of commission after the events of "The Convert," leaving someone else to continue his work. Either way, it wouldn't be surprising if The Mandalorian took fans to Mount Tantiss at some point to further this story, perhaps in the upcoming The Mandalorian and Grogu film . Still, the mystery of Snoke's origins is becoming clearer through the TV series and the Star Wars Expanded Universe.

The Mandalorian Seasons 1-3 are streaming on Disney+, and new episodes of The Bad Batch debut on Wednesdays.

Star Wars: The Mandalorian

A Star Wars story about a lone Mandalorian gunslinger tasked with protecting a young Force-sensitive alien.

Release Date November 12, 2019

Cast Emily Swallow, Werner Herzog, Ming-Na Wen, Katee Sackhoff, Dave Filoni, Pedro Pascal, Gina Carano, Bill Burr, Jon Favreau, Taika Waititi, Temuera Morrison, Nick Nolte, Giancarlo Esposito, Carl Weathers, Amy Sedaris

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The Mandalorian: Doctor Pershing's Research Was a Reference to Snoke

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  1. Chapter III

    research chapter 3 experimental

  2. chapter 3 research methodology quantitative

    research chapter 3 experimental

  3. (PDF) CHAPTER THREE RESEARCH METHODOLOGY 3.1 Introduction

    research chapter 3 experimental

  4. Dissertation first three chapters

    research chapter 3 experimental

  5. CHAPTER 3: EXPERIMENTAL

    research chapter 3 experimental

  6. Chapter 3 Methodology Example In Research : CHAPTER-3...

    research chapter 3 experimental

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  1. Research Processes Questions and Hypotheses

  2. RESEARCH || CHAPTER 3

  3. Operations Research

  4. How to write Areas for Further Research

  5. Research Methods Chapters 5 & 6

  6. Exploring Research Chapter 3, Research Methodology

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  1. (PDF) Chapter 3 Research Design and Methodology

    Chapter 3 consists of three parts: (1) Purpose of the study and research design, (2) Methods, and (3) Statistical Data analysis procedure. Part one, Purpose of the study and Research...

  2. PDF Chapter 3 Experimental Methodology

    This task will be split into three sub-tasks: 1) an image is used to retrieve related images from a still image archive, 2) a text query is used to retrieve related images, 3) an image query is used to retrieve relevant annotations for that image.

  3. Chapter III

    Chapter III- Experimental Research Methodology - Free download as Word Doc (.doc / .docx), PDF File (.pdf), Text File (.txt) or read online for free. chapter

  4. Experimental design (Chapter 3)

    The first two sections introduce control and randomization, the basic ingredients of proper experimental design. Sections 3.3 and 3.4 elaborate on these ingredients and discuss specific designs. Distilled practical advice appears in the next section, and the last section illustrates the main ideas while reviewing some "test-bed" market ...

  5. PDF Presenting Methodology and Research Approach

    qualitative research, in general, and in your tra-dition or genre, in particular; hence, it is written in future tense. In the dissertation's chapter 3, you report on what you have already done. You write after the fact; hence, you write in past tense. As such, many of the sections of chapter 3 can be written only after you have

  6. PDF Chapter 3 Research Strategies and Methods

    3.1 Research Strategies A research strategy is an overall plan for conducting a research study. A research strategy guides a researcher in planning, executing, and monitoring the study. While the research strategy provides useful support at a high level, it needs to be complemented with research methods that can guide the research work at a more

  7. An Introduction to Experimental Design Research

    Abstract. Design research brings together influences from the whole gamut of social, psychological, and more technical sciences to create a tradition of empirical study stretching back over 50 years (Horvath 2004; Cross 2007 ). A growing part of this empirical tradition is experimental, which has gained in importance as the field has matured.

  8. Chapter 3 Experimental Research

    Chapter 3 Experimental Research. In the late 1960s social psychologists John Darley and Bibb Latané proposed a counterintuitive hypothesis. The more witnesses there are to an accident or a crime, the less likely any of them is to help the victim (Darley & Latané, 1968).They also suggested the theory that this happens because each witness feels less responsible for helping—a process ...

  9. Experimental Design

    Random assignment is a method for assigning participants in a sample to the different conditions, and it is an important element of all experimental research in psychology and other fields too. In its strictest sense, random assignment should meet two criteria. One is that each participant has an equal chance of being assigned to each condition ...

  10. PDF Chapter 3 Research Design

    world or in a lab or experimental setting. Deductive research is to use data to test or prove a theory (Fig. 3.2). Whether a study is deductive or inductive, or using com-bined methods, each researcher needs to identify the research problems that he or she intends to tackle. Identifying research problems can be from quick analyses, reading previous

  11. PDF CHAPTER III RESEARCH METHODOLOGY

    Schematically, the quasi-experimental design can be drawn as follows: Note: X represents the exposure of a group to an experimental variable O refers to the process of observation or measurement (Campbell & Stanley, 1963, p.13) variable is termed as an attribute of an object which varies from object to object.

  12. PDF CHAPTER III: METHOD

    Describe quantitative, CHAPTER III: METHOD introduce the qualitative, the method of the chapter and mixed-methods). used (i.e. The purpose of this chapter is to introduce the research methodology for this methodology the specific connects to it question(s). research presented questions research Chapter I. in

  13. PDF Chapter 3 Experimental Design

    Experimental Design. Abstract This chapter covers various issues related to the experimental design, a statistical technique at the core of a discrete choice experiment. Specifically, it focuses ...

  14. PDF Writing Chapter 3 Chapter 3: Methodology

    Instruments. This section should include the instruments you plan on using to measure the variables in the research questions. (a) the source or developers of the instrument. (b) validity and reliability information. •. (c) information on how it was normed. •. (d) other salient information (e.g., number of. items in each scale, subscales ...

  15. Chapter 3

    Suggested Citation: "Chapter 3 - Examples of Effective Experiment Design and Data Analysis in Transportation Research." National Academies of Sciences, Engineering, and Medicine. 2012. Effective Experiment Design and Data Analysis in Transportation Research. Washington, DC: The National Academies Press. doi: 10.17226/22707. × Save Cancel Page 13

  16. PDF CHAPTER III METHODOLOGY 3.1 Research Method

    CHAPTER III METHODOLOGY 3.1 Research Method The method used in this study is pre-experimental research methods. Throughout the pre-experimental method of research, researchers study only one experimental group and provide interventions during the experiment. The researchers have no control group to compare with the experimental group using ...

  17. Chapter 3

    Read chapter Chapter 3 - Experimental Research Approach, Findings, and Associated Analytical Simulations: TRB's National Cooperative Highway Research Prog... Login Register Cart Help. Strand Debonding for Pretensioned Girders (2017) Chapter: Chapter 3 - Experimental Research Approach, Findings, and Associated Analytical Simulations.

  18. Experimental Research

    Experimental Research C. George Thomas Chapter First Online: 25 February 2021 4046 Accesses Abstract Experiments are part of the scientific method that helps to decide the fate of two or more competing hypotheses or explanations on a phenomenon. The term 'experiment' arises from Latin, Experiri, which means, 'to try'.

  19. research chapter 3 experimental research Flashcards

    researcher attempts to control all aspects of the research, except the experimental treatment; difficult to control all variables; have a control group. selective manipulation. intent is to increase likelihood that treatment groups are similar at the beginning of study; matched pair and conner balanced designs. matched pairs design.

  20. LibGuides: Chapter 3: Developing the Quantitative Research Design

    Chapter 3 Introduction to Quantitative Research Design The first step in developing research is identifying the appropriate quantitative design as well as target population and sample. Please access the NU library database "SAGE Research Methods" for help in identifying the appropriate design for your quantitative dissertation.

  21. Chapter 3:Experimental Research Flashcards

    1. state the research problem 2. determine if experimental methods apply 3. specify the independent variable 4. specify the dependent variables 5. state the tentative hypotheses 6. determine measures to be used 7. pause to consider potential success 8. identify intervening variables 9. create formal statement of research hypotheses 10. design the experiment 11. make a final estimate of ...

  22. Chapter 3

    CHAPTER III METHODOLOGY. This chapter reveals the methods of research to be employed by the researcher in conducting the study which includes the research design, population of the study, research instrument and its development establishing its validity and reliability, data gathering procedures, and the appropriate statistical treatment of data

  23. PDF Chapter 3 Experimental Setup, Material and Procedure

    Chapter 3 Experimental Setup, Material and Procedure 3.1 Introduction A major part of the experimental work related to this research, consisting of a number of different types of core-flooding experiments, was carried out using the state-of-the-art, high pressure-high temperature, three-phase steady-state core-

  24. 3. Christianity's place in politics, and 'Christian nationalism'

    About Pew Research Center Pew Research Center is a nonpartisan fact tank that informs the public about the issues, attitudes and trends shaping the world. It conducts public opinion polling, demographic research, media content analysis and other empirical social science research. Pew Research Center does not take policy positions.

  25. The Mandalorian: Doctor Pershing's Research Was a Reference to Snoke

    The Mandalorian's story connects past and future of Star Wars universe, hinting at Snoke and Palpatine's origins. Season 3 starts strong with Din Djarin's mission and introduces clone army based ...