What level of α is traditionally used by researchers in education and social sciences?

To make things easier, the following will act as representations within particular designs:

• X--Treatment
• O--Observation or measurement
• R--Random assignment

The three experimental designs discussed in this section are:

The One Shot Case Study

X O

The Problems with this design are:

• A total lack of control. Also, it is of very little scientific value as securing scientific evidence to make a comparison, and recording differences or contrasts.
• There is also a tendency to have the error of misplaced precision, where the researcher engages in tedious collection of specific detail, careful observation, testing and etc., and misinterprets this as obtaining good research. However you can not misinterpret that a detailed data collection procedure equals a good design.
• History, maturation, selection, mortality and interaction of selection and the experimental variable are all threats to the internal validity of this design.

One Group Pre-Posttest Design

O1 X O2

However, there exists threats to the validity of the above assertion:

• History--between O1 and O2 many events may have occurred apart from X to produce the differences in outcomes. The longer the time lapse between O1 and O2, the more likely history becomes a threat.
• Maturation--between O1 and O2 students may have grown older or internal states may have changed and therefore the differences obtained would be attributable to these changes as opposed to X.
• Testing--the effect of giving the pretest itself may effect the outcomes of the second test (i.e., IQ tests taken a second time result in 3-5 point increase than those taking it the first time). In the social sciences, it has been known that the process of measuring may change that which is being measured--the reactive effect occurs when the testing process itself leads to the change in behavior rather than it being a passive record of behavior (reactivity--we want to use non-reactive measures when possible).
• Instrumentation--examples are in threats to validity above
• Statistical regression--or regression toward the mean. Time-reversed control analysis and direct examination for changes in population variabilities are useful precautions against such misinterpretations. What this means is that if you select samples according to their extreme characteristics or scores, the tendency is to regress toward the mean. Therefore those with extreme high scores appear to be decreasing their scores, and those with extreme low scores appear to be increasing their scores. However this interpretation is not accurate, and to control for misinterpretations, researchers may want to do a time-reversed (posttest-pretest) analysis to analyze the true treatment effects. Researchers may exclude outliers from the analysis.
• Others--History, maturation, testing, instrumentation interaction of testing and maturation, interaction of testing and the experimental variable and the interaction of selection and the experimental variable are also threats to validity for this design.

The Static Group Comparison

Threats to validity include:

• Selection--groups selected may actually be disparate prior to any treatment.
• Mortality--the differences between O1 and O2 may be because of the drop-out rate of subjects from a specific experimental group, which would cause the groups to be unequal.
• Others--Interaction of selection and maturation and interaction of selection and the experimental variable.

The next three designs discussed are the most strongly recommended designs:

The Pretest-Posttest Control Group Design

This design controls for all of the seven threats to validity described in detail so far. An explanation of how this design controls for these threats is below.

• History--this is controlled in that the general history events which may have contributed to the O1 and O2 effects would also produce the O3 and O4 effects. This is true only if the experiment is run in a specific manner--meaning that you may not test the treatment and control groups at different times and in vastly different settings as these differences may effect the results. Rather, you must test simultaneously the control and experimental groups. Intrasession history must also be taken into consideration. For example if the groups truly are run simultaneously, then there must be different experimenters involved, and the differences between the experimenters may contribute to effects.

  A solution to history in this case is the randomization of experimental occasions--balanced in terms of experimenter, time of day, week and etc.

• Maturation and testing--these are controlled in that they are manifested equally in both treatment and control groups.
• Instrumentation--this is controlled where conditions control for intrasession history, especially where fixed tests are used. However when observers or interviewers are being used, there exists a potential for problems. If there are insufficient observers to be randomly assigned to experimental conditions, the care must be taken to keep the observers ignorant of the purpose of the experiment.
• Regression--this is controlled by the mean differences regardless of the extremety of scores or characteristics, if the treatment and control groups are randomly assigned from the same extreme pool. If this occurs, both groups will regress similarly, regardless of treatment.
• Selection--this is controlled by randomization.
• Mortality--this was said to be controlled in this design, however upon reading the text, it seems it may or may not be controlled for. Unless the mortality rate is equal in treatment and control groups, it is not possible to indicate with certainty that mortality did not contribute to the experiment results. Even when even mortality actually occurs, there remains a possibility of complex interactions which may make the effects drop-out rates differ between the two groups. Conditions between the two groups must remain similar--for example, if the treatment group must attend treatment session, then the control group must also attend sessions where either not treatment occurs, or a "placebo" treatment occurs. However even in this there remains possibilities of threats to validity. For example, even the presence of a "placebo" may contribute to an effect similar to the treatment, the placebo treatment must be somewhat believable and therefore may end up having similar results!

The factors described so far effect internal validity. These factors could produce changes which may be interpreted as the result of the treatment. These are called main effects which have been controlled in this design giving it internal validity.

However, in this design, there are threats to external validity (also called interaction effects because they involve the treatment and some other variable the interaction of which cause the threat to validity). It is important to note here that external validity or generalizability always turns out to involve extrapolation into a realm not represented in one's sample.

In contrast, internal validity are solvable within the limits of the logic of probability statistics. This means that we can control for internal validity based on probability statistics within the experiment conducted, however, external validity or generalizability can not logically occur because we can't logically extrapolate to different conditions. (Hume's truism that induction or generalization is never fully justified logically).

External threats include:

• Interaction of testing and X--because the interaction between taking a pretest and the treatment itself may effect the results of the experimental group, it is desirable to use a design which does not use a pretest.
• Interaction of selection and X--although selection is controlled for by randomly assigning subjects into experimental and control groups, there remains a possibility that the effects demonstrated hold true only for that population from which the experimental and control groups were selected. An example is a researcher trying to select schools to observe, however has been turned down by 9, and accepted by the 10th. The characteristics of the 10th school may be vastly different than the other 9, and therefore not representative of an average school. Therefore in any report, the researcher should describe the population studied as well as any populations which rejected the invitation.
• Reactive arrangements--this refers to the artificiality of the experimental setting and the subject's knowledge that he is participating in an experiment. This situation is unrepresentative of the school setting or any natural setting, and can seriously impact the experiment results. To remediate this problem, experiments should be incorporated as variants of the regular curricula, tests should be integrated into the normal testing routine, and treatment should be delivered by regular staff with individual students.

Research should be conducted in schools in this manner--ideas for research should originate with teachers or other school personnel. The designs for this research should be worked out with someone expert at research methodology, and the research itself carried out by those who came up with the research idea. Results should be analyzed by the expert, and then the final interpretation delivered by an intermediary.

Tests of significance for this design--although this design may be developed and conducted appropriately, statistical tests of significance are not always used appropriately.

• Wrong statistic in common use--many use a t-test by computing two ts, one for the pre-post difference in the experimental group and one for the pre-post difference of the control group. If the experimental t-test is statistically significant as opposed to the control group, the treatment is said to have an effect. However this does not take into consideration how "close" the t-test may really have been. A better procedure is to run a 2X2 ANOVA repeated measures, testing the pre-post difference as the within-subject factor, the group difference as the between-subject factor, and the interaction effect of both factors.
• Use of gain scores and covariance--the most used test is to compute pre-posttest gain scores for each group, and then to compute a t-test between the experimental and control groups on the gain scores. Also used are randomized "blocking" or "leveling" on pretest scores and the analysis of covariance are usually preferable to simple gain-score comparisons.
• Statistics for random assignment of intact classrooms to treatments--when intact classrooms have been assigned at random to treatments (as opposed to individuals being assigned to treatments), class means are used as the basic observations, and treatment effects are tested against variations in these means. A covariance analysis would use pretest means as the covariate.

The Soloman Four-Group Design

In this design, subjects are randomly assigned to four different groups: experimental with both pre-posttests, experimental with no pretest, control with pre-posttests, and control without pretests. By using experimental and control groups with and without pretests, both the main effects of testing and the interaction of testing and the treatment are controlled. Therefore generalizability increases and the effect of X is replicated in four different ways.

Statistical tests for this design--a good way to test the results is to rule out the pretest as a "treatment" and treat the posttest scores with a 2X2 analysis of variance design-pretested against unpretested.

The Posttest-Only Control Group Design

Statistical tests for this design--the most simple form would be the t-test. However covariance analysis and blocking on subject variables (prior grades, test scores, etc.) can be used which increase the power of the significance test similarly to what is provided by a pretest.

As illustrated above, Cook and Campbell devoted much efforts to avoid/reduce the threats against internal valdity (cause and effect) and external validity (generalization). However, some widespread concepts may also contribute other types of threats against internal and external validity.

Some researchers downplay the importance of causal inference and assert the worth of understanding. This understanding includes "what," "how," and "why." However, is "why" considered a "cause and effect" relationship? If a question "why X happens" is asked and the answer is "Y happens," does it imply that "Y causes X"? If X and Y are correlated only, it does not address the question "why." Replacing "cause and effect" with "understanding" makes the conclusion confusing and misdirect researchers away from the issue of "internal validity."

Some researchers apply a phenomenological approach to "explanation." In this view, an explanation is applied to only a particular case in a particular time and place, and thus generalization is considered inappropriate. In fact, a particular explanation does not explain anything. For example, if one askes, "Why Alex Yu behaves in that way," the asnwer could be "because he is Alex Yu. He is a unqiue human being. He has a particular family background and a specific social circle." These "particular" statements are alway right, thereby misguide researchers away from the issue of external validity.

What is the first step a researcher might use to analyze the qualitative data in a study?

What is the contribution of quantitative research in social science?

What research purpose is best suited for quantitative research studies?

Which is most important in a good qualitative research study?