Threats to validity of Research Design

Chong-ho Yu & Barbara Ohlund (2012)

The books by Campbell and Stanley (1963), Cook and Campbell (1979), and Shadish, Cook, and Campbell, (2002) are considered seminal works in the field of experimental design. The following is summary of their books with insertion of our examples.

Problem and Background

Experimental method and essay-writing

Campbell and Stanley point out that adherence to experimentation dominated the field of education through the 1920s (Thorndike era) but that this gave way to great pessimism and rejection by the late 1930s. However, it should be noted that a departure from experimentation to essay writing (Thorndike to Gestalt Psychology) occurred most often by people already adept at the experimental tradition. Therefore we must be aware of the past so that we avoid total rejection of any method, and instead take a serious look at the effectiveness and applicability of current and past methods without making false assumptions.

Replication

Multiple experimentation is more typical of science than a one-shot experiment! Experiments really need replication and cross-validation at various times and conditions before the theory can be confirmed with confidence. In the past the only option is to replicate the same experiments over and over. Nevertheless, today the researcher is allowed to virtually repeat the study using one single sample by resampling. Specifically, many data mining software applications have the features of cross-validation and bootstrap forest. In cross-validation the data set is partitioned into many subsets and then multiple analyses are run. In each run the model is refined by previous "training" and thus the end result is considered a product of replicated experiments. In a similar vein, bootstrap forest randomly selects observations from the data and replicate the analysis many times. The conclusion is based on the convergence of these diverse results.

Cumulative wisdom

An interesting point made is that experiments which produce or support opposing theories against each other probably will not have clear cut outcomes. In fact, different researchers might observe something valid that represents a part of the truth. Adopting experimentation in education should not imply advocating a position incompatible with traditional wisdom. Rather, experimentation may be seen as a process of refining or enhancing this wisdom. Therefore, cumulative wisdom and scientific findings need not be opposing forces.

Factors Jeopardizing Internal and External Validity

Please note that validity discussed here is in the context of experimental design, not in the context of measurement.

  • Internal validity refers specifically to whether an experimental treatment/condition makes a difference to the outcome or not, and whether there is sufficient evidence to substantiate the claim.

  • External validity refers to the generalizibility of the treatment/condition outcomes across various settings.

Efficacy and effectiveness

In medical studies, usually efficacy studies in experimental settings are conducted to address the issue of internal validity whereas effectiveness studies in naturalistic settings (the "real" world) are employed to examine the external validity of the claim. Usually patients in experimentation are highly selected whereas patients in the real world are not. For example, subjects in clinical trials usually have just the illness under study. Patients who have multiple health conditions are excluded from the study because those uncontrolled variables could muddle the research results. However, in the real world it is not unusual that patients have multiple illnesses. As a result, a drug that could work well in a lab setting may fail in the real world. Thus, medical researchers must take both internal validity and external validity into account while testing the goodness of a treatment. On one hand, efficacy studies aim to answer this question: Does the treatment work in a close experimental environment? On the other hand, effectiveness studies attempt to address a different issue: Does the treatment work in the real-life situation? (Pittler & White, 1999).

drug Interestingly enough, the US drug approval and monitoring processes seem to compartmentalize efficacy and effectiveness. The US Food and Drug administration (FDA) is responsible for approving drugs before they are released to the market. Rigorous experiments and hard data are required to gain the FDA's approval. But after the drugs are on the market, it takes other agencies to monitor the effectiveness of the drugs. Contrary to the popular belief, FDA has no authority to recall unsafe drugs. Rather, FDA could suggest a voluntarily recall only. Several drugs that had been approved by FDA before were re-called from the market later (e.g. the anti-diabetic drug Avandia and pain-reliever Vioxx). This discrepancy between the results yielded from lab tests and the real world led to an investigation by the Institute of Medicine (IOM). To close the gap between internal and external validity, the IOM committee recommended that the FDA should take proactive steps to monitor the safety of the approved drugs throughout their time on the market (Ramsey, 2012).

Ecological validity

In recent years, the concepts of efficacy and effectiveness is also utilized by educational researchers (Schneider, Carnoy, Kilpatrick, Schmidt, & Shavelson, 2007). Indeed, there is a similar concept to "efficacy" in educational research: ecological validity. Educational researchers realize that it is impossible for teacher to blocking all interferences by closing the door. Contrary to the experimental ideal that a good study is a "noiseless" one, a study is regarded as ecologically valid if it captures teachers' everyday experience as they are bombarded with numerous things (Black & Wiliam, 1998; Valli & Buese, 2007)

Which one is more important?

Whether internal validity or external validity is more important has been a controversial topic in the research community. Campbell and Stanley (1963) stated that although ideally speaking a good study should be strong in both types of validity, internal validity is indispensable and essential while the question of external validity is never completely answerable. External validity is concerned with whether the same result of a given study can be observed in other situations. Like inductive inference, this question will never be conclusive. No matter how many new cases concur with the previous finding, it takes just one counter-example to weaken the external validity of the study. In other words, Campbell and Stanley's statement implies that internal validity is more important than external validity. Cronbach (1982) is opposed to this notion. He argued that if a treatment is expected to be relevant to a broader context, the causal inference must go beyond the specific conditions. If the study lacks generalizability, then the so-called internally valid causal effect is useless to decision makers. In a similar vein, Briggs (2008) asserted that although statistical conclusion validity and internal validity together affirms a causal effect, construct validity and external validity are still necessary for generalizing a causal conclusion to other settings.

Factors which jeopardize internal validity

  • History: the specific events which occur between the first and second measurement. The 2008 economic recession is a good example. Due to the budget crisis many schools cut back resources. A treatment implemented around that period of time may be affected by a lack of supporting infrastructure.

  • Maturation: the processes within subjects which act as a function of the passage of time. i.e. if the project lasts a few years, most participants may improve their performance regardless of treatment.

  • Testing: the effects of taking a test on the outcomes of taking a second test. In other words, the pretest becomes a form of "treatment."

  • Instrumentation: the changes in the instrument, observers, or scorers which may produce changes in outcomes.

  • Statistical regression: It is also known as regression towards the mean. This threat is caused by the selection of subjects on the basis of extreme scores or characteristics. If there are forty poor students in the treatment program, it is likely that they will show some improvement after the treatment. However, if the students are extremely poor and thus are unresponsive to any treatment, then it is called the floor effect.

  • Selection of subjects: the biases which may result in selection of comparison groups. Randomization (Random assignment) of group membership is a counter-attack against this threat. However, when the sample size is small, randomization may lead to Simpson Paradox, which has been discussed in an earlier lesson.

  • Experimental mortality: the loss of subjects. For example, in a Web-based instruction project entitled Eruditio, it started with 161 subjects and only 95 of them completed the entire module. Those who stayed in the project all the way to end may be more motivated to learn and thus achieved higher performance. The hidden variable, intention to treat, might skew the result.

  • Selection-maturation interaction: the selection of comparison groups and maturation interacting which may lead to confounding outcomes, and erroneous interpretation that the treatment caused the effect.

  • John Henry effect: John Henry was a worker who outperformed a machine under an experimental setting because he was aware that his performance was compared with that of a machine.

Factors which jeopardize external validity

  • Reactive or interaction effect of testing: a pretest might increase or decrease a subject's sensitivity or responsiveness to the experimental variable. Indeed, the effect of pretest to subsequent tests has been empirically substantiated (Wilson & Putnam, 1982, Lana, 1959).

  • Interaction effects of selection biases and the experimental variable

  • Reactive effects of experimental arrangements: it is difficult to generalize to non-experimental settings if the effect was attributable to the experimental arrangement of the research.

  • Multiple treatment interference: as multiple treatments are given to the same subjects, it is difficult to control for the effects of prior treatments.

Three Experimental Designs

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

There is a single group and it is studied only once. A group is introduced to a treatment or condition and then observed for changes which are attributed to the treatment

X O

The problems with this design are:

  • A total lack of manipulation. Also, the scientific evidence is very weak in terms of making a comparison and recording contrasts.

  • There is also a tendency to have the fallacy of misplaced precision, where the researcher engages in tedious collection of specific detail, careful observation, testing and etc., and misinterprets this as obtaining solid research. However, a detailed data collection procedure should not be equated with a good design. In the chapter on design, measurement, and analysis, these three components are clearly distinguished from each other.

  • History, maturation, selection, mortality, and interaction of selection and the experimental variable are potential threats against the internal validity of this design.

One Group Pre-Posttest Design

This is a presentation of a pretest, followed by a treatment, and then a posttest where the difference between O1 and O2 is explained by X:

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. For example, if the US government does nothing to the economic depression starting from 2008 and let the crisis runs its course (this is what Mitt Romney said), ten years later the economy may still be improved. In this case, it is problematic to compare the economy in 2021 and that in 2011 to determine whether a particular policy is effective; rather, the right way is to compare the economy in 2021 with the overall (e.g. 2011 to 2021). In SPSS the default pairwise comparison is to contrast each measure with the final measure, but it may be misleading. In SAS the default contrast scheme is Deviation, in which each measure is compared to the grand mean of all measures (overall).

  • 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 variability are proactive counter-measures against such misinterpretations of the result. If the researcher selects a very polarized sample consisting of extremely skillful and extremely poor students, the former group might either show no improvement (ceiling effect) or decrease their scores, and the latter might appear to show some improvement. Needless to say, this result is midleading, and to correct this type of misinterpretation, researchers may want to do a time-reversed (posttest-pretest) analysis to analyze the true treatment effects. Researchers may also exclude outliers from the analysis or to adjust the scores by winsorizing the means (pushing the outliers towards the center of the distribution).

  • 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

This is a two group design, where one group is exposed to a treatment and the results are tested while a control group is not exposed to the treatment and similarly tested in order to compare the effects of treatment.

X O1

O2
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.


Three True Experimental Designs

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

The Pretest-Posttest Control Group Design

This designs takes on this form:

R O1 X O2
RO3
O4
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. However, this is true if and only if the experiment is run in a specific manner: the researcher may not test the treatment and control groups at different times and in vastly different settings as these differences may influence the results. Rather, the researcher must test the control and experimental groups concurrently. Intrasession history must also be taken into account. For example if the groups are tested at the same time, then different experimenters might be involved, and the differences between the experimenters may contribute to the effects.

    In this case, a possible counter-measure is the randomization of experimental conditions, such as counter-balancing in terms of experimenter, time of day, week and etc.

  • Maturation and testing: these are controlled in the sense that they are manifested equally in both treatment and control groups.

  • Instrumentation: this is controlled where conditions control for intrasession history, especially where the same tests are used. However, when different raters, observers or interviewers are involved, this becomes a potential problem. If there are not enough raters or observers to be randomly assigned to different experimental conditions, the raters or observers must be blind to the purpose of the experiment.

  • Regression: this is controlled by the mean differences regardless of the extremely 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, 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 the treatment session, then the control group must also attend sessions where either no 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 affect 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 by the logic of probability statistics, meaning that we can control for internal validity based on probability statistics within the experiment conducted. On the other hand, external validity or generalizability can not logically occur because we can't logically extrapolate to different settings. (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. In addition, it is helpful to use randomized "blocking" or "leveling" on pretest scores because blocking can localize the within-subject variance, also known as the error variance. It is important to point out that gain scores are subject to the ceiling and floor effects. In the former the subjects start with a very high pretest score and in the latter the subjects have very poor pretest performance. In this case, analysis of covariance (ANCOVA) is usually preferable to a simple gain-score comparison.

  • 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

The design is as:

RO1XO2
RO3
O4
R
X O5
R

O6

In this research design, subjects are randomly assigned into four different groups: experimental with both pre-posttests, experimental with no pretest, control with pre-posttests, and control without pretests. In this configuration, both the main effects of testing and the interaction of testing and the treatment are controlled. As a result, generalizability is improved 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. Alternatively, the pretest, which is a form of pre-existing difference, can be used as a covariate in ANCOVA.

The Posttest-Only Control Group Design

This design is as:
RXO1
R
O2
This design can be viewed as the last two groups in the Solomon 4-group design. And can be seen as controlling for testing as main effect and interaction, but unlike this design, it doesn't measure them. But the measurement of these effects isn't necessary to the central question of whether of not X did have an effect. This design is appropriate for times when pretests are not acceptable.

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.


Discussion on causal inference and generalization

As illustrated above, Cook and Campbell devoted much efforts to avoid/reduce the threats against internal validity (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 narrow approach to "explanation." In this view, an explanation is contextualized to only a particular case in a particular time and place, and thus generalization is considered inappropriate. In fact, an over-specific explanation might not explain anything at all. For example, if one asks, "Why Alex Yu behaves in that way," the answer could be "because he is Alex Yu. He is a unique human being. He has a particular family background and a specific social circle." These "particular" statements are always right, thereby misguide researchers away from the issue of external validity.


Reference

  • Black, P., & Wiliam, D. (1998). Assessment and classroom learning. Assessment in Education: Principles, Policy and Practice, 5, 7-74.

  • Briggs, D. C. (2008). Comments on Slavin: Synthesizing causal inferences. Educational Researcher, 37, 15-22.

  • Campbell, D. & Stanley, J. (1963). Experimental and quasi-experimental designs for research. Chicago, IL: Rand-McNally.

  • Cook, T. D., & Campbell, D. T. (1979). Quasi-experimentation: Design and analysis issues for field settings. Boston, MA: Houghton Mifflin Company.

  • Cronbach, L. (1982). Designing evaluations of educational and social programs. San Francisco: Jossey-Bass.

  • Pittler, M. H., & White, A. R. (1999). Efficacy and effectiveness. Focus on Alternative and Complementary Therapy, 4,109–10. Retrieved June 8, 2009, from http://www.medicinescomplete.com/journals/fact/current/fact0403a02t01.htm

  • Ramsey, L. (2012, May 2). U.S. needs to expand monitoring after drug approval. PharmPro. Retrieved from http://www.pharmpro.com/news/2012/05/us-needs-to-expand-monitoring-after-drug-approval/

  • Schneider, B., Carnoy, M., Kilpatrick, J. Schmidt, W. H., & Shavelson, R. J. (2007). Estimating causal effects using experimental and observational designs: A think tank white paper. Washington, D.C.: American Educational Research Association.

  • Shadish, W. R., Cook, T. D., & Campbell, D. T. (2002). Experimental and quasi-experimental designs for generalized causal inference. Boston, MA: Houghton Mifflin.

  • Valli, L., & Buese, D. (2007). The changing roles of teachers in an era of high0stakes accountability. American Education Research Journal, 44, 519-558.


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