Several years ago, I had a grant from the National Science Foundation to review research on elementary science programs. I therefore got to attend NSF conferences for principal investigators. At one such conference, we were asked to present poster sessions. The group next to mine was showing an experiment in science education that had remarkably large effect sizes. I got to talking with the very friendly researcher, and discovered that the experiment involved a four-week unit on a topic in middle school science. I think it was electricity. Initially, I was very excited, electrified even, but then I asked a few questions about the control group.
“Of course there was a control group,” he said. “They would have taught electricity too. It’s pretty much a required portion of middle school science.”
Then I asked, “When did the control group teach about electricity?”
“We had no way of knowing,” said my new friend.
“So it’s possible that they had a four-week electricity unit before the time when your program was in use?”
“Sure,” he responded.
“Or possibly after?”
“Could have been,” he said. “It would have varied.”
Being the nerdy sort of person I am, I couldn’t just let this go.
“I assume you pretested students at the beginning of your electricity unit and at the end?”
“But wouldn’t this create the possibility that control classes that received their electricity unit before you began would have already finished the topic, so they would make no more progress in this topic during your experiment?”
“…I guess so.”
“And,” I continued, “students who received their electricity instruction after your experiment would make no progress either because they had no electricity instruction between pre- and posttest?”
I don’t recall how the conversation ended, but the point is, wonderful though my neighbor’s science program might be, the science achievement outcome of his experiment were, well, meaningless.
In the course of writing many reviews of research, my colleagues and I encounter misuses of control groups all the time, even in articles in respected journals written by well-known researchers. So I thought I’d write a blog on the fundamental issues involved in using control groups properly, and the ways in which control groups are often misused.
The purpose of a control group
The purpose of a control group in any experiment, randomized or matched, is to provide a valid estimate of what the experimental group would have achieved had it not received the experimental treatment, or if the study had not taken place at all. Through random assignment or matching, the experimental and control groups are essentially equal at pretest on all important variables (e.g., pretest scores, demographics), and nothing happens in the course of the experiment to upset this initial equality.
How control groups go wrong
Inequality in opportunities to learn tested content. Often, experiments appear to be legitimate (e.g., experimental and control groups are well matched at pretest), but the design contains major bias, because the content being taught in the experimental group is not the same as the content taught in the control group, and the final outcome measure is aligned to what the experimental group was taught but not what the control group was taught. My story at the start of this blog was an example of this. Between pre- and posttest, all students in the experimental group were learning about electricity, but many of those in the control group had already completed electricity or had not received it yet, so they might have been making great progress on other topics, which were not tested, but were unlikely to make much progress on the electricity content that was tested. In this case, the experimental and control groups could be said to be unequal in opportunities to learn electricity. In such a case, it matters little what the exact content or teaching methods were for the experimental program. Teaching a lot more about electricity is sure to add to learning of that topic regardless of how it is taught.
There are many other circumstances in which opportunities to learn are unequal. Many studies use unusual content, and then use tests partially or completely aligned to this unusual content, but not to what the control group was learning. Another common case is where experimental students learn something involving use of technology, but the control group uses paper and pencil to learn the same content. If the final test is given on the technology used by the experimental but not the control group, the potential for bias is obvious.
Unequal opportunities to learn (as a source of bias in experiments) relates to a topic I’ve written a lot about. Use of developer- or researcher-made outcome measures may introduce unequal opportunities to learn, because these measures are more aligned with what the experimental group was learning than what the control group was learning. However, the problem of unequal opportunities to learn is broader than that of developer/researcher-made measures. For example, the story that began this blog illustrated serious bias, but the measure could have been an off-the-shelf, valid measure of electricity concepts.
Problems with control groups that arise during the experiment. Many problems with control groups only arise after an experiment is under way, or completed. These involve situations in which there are different numbers of students/classes/schools that are not counted in the analysis. Usually, these are cases in which, in theory, experimental and control groups have equal opportunities to learn the tested content at the beginning of the experiment. However, some number of students assigned to the experimental group do not participate in the experiment enough to be considered to have truly received the treatment. Typical examples of this include after-school and summer-school programs. A group of students is randomly assigned to receive after-school services, for example, but perhaps only 60% of the students actually show up, or attend enough days to constitute sufficient participation. The problem is that the researchers know exactly who attended and who did not in the experimental group, but they have no idea which control students would or would not have attended if the control group had had the opportunity. The 40% of students who did not attend can probably be assumed to be less highly motivated, lower achieving, have less supportive parents, or to possess other characteristics that, on average, may identify students who are less likely to do well than students in general. If the researchers drop these 40% of students, the remaining 60% who did participate are likely (on average) to be more motivated, higher achieving, and so on, so the experimental program may look a lot more effective than it truly is. This kind of problem comes up quite often in studies of technology programs, because researchers can easily find out how often students in the experimental group actually logged in and did the required work. If they drop students who did not use the technology as prescribed, then the remaining students who did use the technology as intended are likely to perform better than control students, who will be a mix of students who would or would not have used the technology if they’d had the chance. Because these control groups contain more and less motivated students, while the experimental group only contains the students who were motivated to use the technology, the experimental group may have a huge advantage.
Problems of this kind can be avoided by using intent to treat (ITT) methods, in which all students who were pretested remain in the sample and are analyzed whether or not they used the software or attended the after-school program. Both the What Works Clearinghouse and Evidence for ESSA require use of ITT models in situations of this kind. The problem is that use of ITT analyses almost invariably reduces estimates of effect sizes, but to do otherwise may introduce quite a lot of bias in favor of the experimental groups.
Experiments without control groups
Of course, there are valid research designs that do not require use of control groups at all. These include regression discontinuity designs (in which long-term data trends are studied to see if there is a sharp change at the point when a treatment is introduced) and single-case experimental designs (in which as few as one student/class/school is observed frequently to see what happens when treatment conditions change). However, these designs have their own problems, and single case designs are rarely used outside of special education.
Control groups are essential in most rigorous experimental research in education, and with proper design they can do what they were intended to do with little bias. Education researchers are becoming increasingly sophisticated about fair use of control groups. Next time I go to an NSF conference, for example, I hope I won’t see posters on experiments that compare students who received an experimental treatment to those who did not even receive instruction on the same topic between pretest and posttest.
This blog was developed with support from the Laura and John Arnold Foundation. The views expressed here do not necessarily reflect those of the Foundation.