Quasi-Experimental Design:
Types, Examples and Analysis

You can’t always randomize. Your intervention runs in the classes you teach, on the ward you manage, or under a policy that started on a date that’s already passed. So you compare the people who got it with people who didn’t, and sooner or later your committee asks the obvious question: how do you know it was the intervention, and not the difference between the groups?

In our 10 years of helping students navigate their methodologies, we’ve found that’s the question a quasi-experiment lives or dies on. In this post, I’ll explain the main quasi-experimental designs and how to choose one, show you how the choice of analysis can change your answer, and walk through five real doctoral projects, plus the alternative explanations your committee will ask you to rule out.

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What is a quasi-experimental design?

A quasi-experimental design is a study that introduces (or studies) an intervention and compares outcomes, but without randomly assigning people to the groups. A widely cited methods text, Shadish, Cook and Campbell’s Experimental and Quasi-Experimental Designs for Generalized Causal Inference, defines it in one line:

An experiment in which units are not assigned to conditions randomly.

Instead, assignment happens some other way. In their words, it’s “by means of self-selection, by which units choose treatment for themselves.” It can also be “by means of administrator selection, by which teachers, bureaucrats, legislators, therapists, physicians, or others decide which persons should get which treatment.” Quasi-experiments are quantitative designs, and the types of research design they sit among are the same four our coaches use: descriptive, correlational, experimental and quasi-experimental.

It helps to see the neighbors side by side. Here’s how a quasi-experiment differs from the designs it’s most often confused with:

Design	Is there an intervention or cause?	Who decides who gets it?
Randomized experiment	Yes, introduced by the researcher	A random process
Quasi-experiment	Yes, and it can be manipulated	Not random: you, an administrator, or the people themselves
Natural experiment	A naturally occurring event or change	Not the researcher: nature, or a decision outside the study
Correlational study	No intervention	Nobody: you measure what’s already there

The natural experiment row is the one that trips people up, because definitions differ. Shadish, Cook and Campbell describe it as “not really an experiment because the cause usually cannot be manipulated,” like an earthquake. Guidance written for the UK’s Medical Research Council notes that the term “lacks an exact definition,” and that the common thread in most definitions is broader: the exposure “has not been manipulated by the researcher.” Here’s how the two definitions play out with a policy change:

In practice, the label matters less than the description. In your methodology chapter, say what the change was, who decided who got it and when, and how you chose your comparison group or period. Then a committee member who uses the other definition still sees exactly what you studied, whatever you call it.

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Quasi-experimental or correlational?

This is the question I’d answer before anything else, because in our coaching sessions, students often call a study quasi-experimental when it’s really correlational. The test is simple: is there a specific intervention, program or change, and are you comparing outcomes with and without it?

The flowchart below is a rule we often use to place any quantitative study. Start at the left and notice that the very first question is about intervention, not about groups:

So a survey comparing burnout between nurses on day shifts and night shifts is correlational (some programs call this kind of group comparison “causal-comparative”), because the shift pattern is a standing condition you’re observing, not an intervention you’re evaluating. A study that introduces a new handover protocol on one ward and compares it with a similar ward is quasi-experimental.

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The main types of quasi-experimental design

There’s no single official list, and the sources draw the edges differently. The designs below are the ones you’ll often meet in dissertations. To describe them compactly, methodologists use a notation that goes back to Campbell and Stanley’s 1963 classic: O is an observation or measurement, X is the intervention, and time runs left to right. A dashed line between rows means the groups weren’t formed by random assignment.

One-group pretest-posttest

You measure one group, deliver the intervention, then measure again. In our experience, it’s one of the most common shapes for a DNP project, and it’s easy to see why: one setting, one group, no need to find a comparison. Here’s how one nursing doctoral project describes its design:

That’s a clear, honest description, and for a project evaluating a practice change, it may be all the setting allows. But know what you’re claiming, because the sources don’t even agree on what to call it.

For example, Campbell and Stanley classed it as “pre-experimental”. Shadish, Cook and Campbell, by contrast, list it among the quasi-experimental designs that lack a control group. A review of quasi-experimental designs in health effectiveness and implementation research calls a pre-post design a quasi-experimental design but leaves the version without a control group out of its review.

What they share is the problem: without a comparison, anything else that changed between the two measurements could explain the result. If you can add a comparison group, or a second pretest (one of the improvements Shadish, Cook and Campbell suggest), do.

Nonequivalent groups pretest-posttest

In our experience, this is the design most education and health dissertations mean by “quasi-experimental”: an intervention group and a comparison group, both measured before and after, where the groups are intact units such as classes, wards or schools. The health research review defines the comparison as “a control group that is not randomly assigned to receive or not receive the intervention.” Here’s the design in an EdD on Honors Advanced Algebra:

Cutts’s pretest did what a pretest is supposed to do: it showed the groups weren’t equivalent at the start. As the dissertation puts it, “students in the control group had a significantly higher mean on the pre-test than the students in the treatment group,” a result the author noted “was important to keep in mind when comparing the results to the post-test scores.” That’s the right instinct. The next step is to build the pretest into the analysis itself, which the analysis section below shows how to do.

Interrupted time series

Instead of one measurement before and after, you take many, so you can see the trend the intervention interrupts. A tutorial on interrupted time series regression for public health calls it “a valuable study design for evaluating the effectiveness of population-level health interventions that have been implemented at a clearly defined point in time.” It suits routine data: monthly falls on a ward, weekly attendance, annual admissions.

How many time points? The health research review says an interrupted time series “requires at least three time points in the pre- and postintervention periods,” with more recommended, while the tutorial says “there are no fixed limits,” because power depends on the variability of your data and the size of the effect. Treat the review’s three either side as a minimum, not a target.

Difference-in-differences

This design compares the change in the intervention group with the change in a comparison group over the same period. An economics PhD we host uses it on Philadelphia’s soda tax:

Notice the word “counterfactual”: the comparison group stands in for what would have happened to Philadelphia without the tax. That only works under what a review of best practices for difference-in-differences studies in public health policy research calls the common trends assumption: “a graph of the time series should look like a set of parallel lines” before the policy. The authors are blunt about the catch. With one period before and one after, “the common trend assumption is not testable.”

With several periods before the change, you can at least check whether the lines ran parallel, so if you plan this design, collect more than one pre-period. Because the researcher didn’t introduce the tax, a study like this is often called a natural experiment too.

Regression discontinuity

Here, eligibility is decided by a cutoff on a score: students below a reading benchmark get tutoring, patients above a risk score get a follow-up call. You compare people just either side of the cutoff. The design was first used on merit awards given to students above a test-score cutoff, and as a review of regression discontinuity designs in economics explains, “individuals with scores just below the cutoff (who did not receive the award) were good comparisons to those just above the cutoff (who did receive the award).”

When eligibility really is decided by a cutoff, it’s a strong design, so strong that the What Works Clearinghouse (WWC), the US Department of Education’s evidence reviewer, doesn’t treat it as a quasi-experiment at all: like a randomized trial, it can earn the WWC’s top rating. The economics review’s key condition is that people can’t precisely manipulate their score to land on the right side of the line.

Matching and propensity scores

When you can’t control who gets the intervention but you have records on many characteristics, you can build a comparison group that looks like the intervention group. There are two common ways: matching on the characteristics directly, or matching on a propensity score, which an introduction to propensity score methods defines as “the probability of treatment assignment conditional on observed baseline characteristics.” In plain terms, that’s each person’s predicted chance of getting the intervention, given everything you know about them. Here’s how both work in practice:

Strictly, this is a technique you add to a design, not a design of its own. Its limit is in that definition: observed characteristics. If the patients who signed up were also more motivated, and motivation isn’t in the records, neither method can guarantee balance on it. The same introduction calls the assumption that everything relevant was measured “the crucial assumption that underlies propensity score analyses.”

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Which design fits your situation?

In our experience, most students don’t choose a design in the abstract. They start with a situation and need to know what it allows. Find yours in the left column:

Your situation	What to consider
One group, measured before and after, no comparison available	One-group pretest-posttest (the weakest option; some texts call it pre-experimental)
An intact class, ward or site, plus a similar one that doesn’t get the intervention	Nonequivalent groups pretest-posttest
A change that started on a known date, with routine data going back months	Interrupted time series
The same, plus a comparable site or group that didn’t get the change	Difference-in-differences (or a controlled time series)
Eligibility decided by a cutoff on a score	Regression discontinuity
No control over who got it, but rich records on everyone	A matched or propensity-score comparison

Each design answers the question “compared with what?” in its own way: a comparison group, a longer run of measurements, or a known rule for who got the intervention. If your situation allows more than one, I’d choose the one that rules out more alternative explanations, even if it means a few more months of data.

A word of warning from our coaching sessions: watch for design drift. A committee member suggests adding “a quick before-and-after measure” to a descriptive study, and without anyone deciding it, the study has become a test of an intervention, with all the threats and analysis choices that come with one. If that happens, rewrite the design section to match.

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How to analyze a quasi-experiment

The analysis follows the design. For the nonequivalent groups design, there are three obvious ways to compare the groups, and with unequal groups they give different estimates of the effect.

Here’s an illustrative example with made-up numbers: two intact classes of 30 students, one taught with a new method, both tested before and after. A real study would want more than one class per method, for reasons the clustering note below explains.

	New method	Usual method	Difference
Pretest mean (SD 10)	61	59	2
Posttest mean (SD 10)	74	68	6
Gain (posttest − pretest)	13	9	4
Posttest adjusted for pretest (ANCOVA)	73.2	68.8	4.4

So is the new method worth 6 points, 4 or 4.4? Comparing posttests alone gives 6, but it ignores the 2-point head start. Gain scores give 4. ANCOVA, which adjusts the posttest for the pretest, gives 4.4. All three are things students report, and they don’t agree on the size of the effect.

Two lessons come out of that table.

The first is about baseline equivalence: whether your groups were similar at the start, on the outcome and on other measured characteristics that could affect it, before the intervention began. A t-test on the pretests here isn’t significant (p = .44), and it’s tempting to conclude the groups were equivalent. But a non-significant test isn’t evidence of equivalence.

The WWC judges it by size instead: in its standards handbook, a baseline difference of 0.05 standard deviations or less is fine, one between 0.05 and 0.25 requires statistical adjustment, and anything over 0.25 doesn’t meet its standard. The 2-point gap here is 0.2 SD, so it has to be adjusted for. That’s the WWC’s rule for education evidence reviews, not a universal law, but it’s a defensible standard to cite.

The second lesson is that the choice between gain scores and ANCOVA isn’t automatic. A comparison of the two methods in randomized and nonrandomized studies showed that with groups that differ at baseline, the two methods “cannot both be unbiased, and may contradict each other.” Which one to trust depends on how the groups came to differ:

• If assignment depended on the pretest (the lowest scorers got the tutoring, say), “ANCOVA must be used.”
• If the groups were pre-existing (two classes that happened to differ), “ANOVA of change seems less biased than ANCOVA,” and the paper recommends two control groups and two baseline measurements.

In our example, the classes were pre-existing, so by that reasoning the gain-score estimate of 4 points is the one to lead with.

That also satisfies the WWC’s adjustment rule: it accepts simple gain scores as an adjustment when the pretest and posttest use the same measure and correlate at .60 or more, and here they correlate at .8. With a bigger baseline gap, the two methods can disagree about more than size: in the depression study that paper reanalyzed, “ANCOVA suggests absence, but ANOVA of change suggests presence, of a treatment effect.”

This is a version of Lord’s paradox, a famous 1967 puzzle in which two statisticians, each using a standard method on the same data, reach different conclusions. The chart below recreates Lord’s setup with illustrative data: two groups weighed in September and again in June, neither of which changed on average. Look first at the dashed line, then at the two solid ones:

The practical response is to decide your primary analysis in advance, justify it from how your groups were formed, and report the other as a check. If they agree, your finding is sturdier. If they don’t, say so. And if you’re still at the planning stage, I’d collect a second pretest: it’s the cheapest way to see whether the groups were already on different paths before the intervention began.

For the other designs, the analysis is more settled:

Design	Usual analysis
One-group pretest-posttest	Paired t-test (or its nonparametric equivalent)
Nonequivalent groups pretest-posttest	ANCOVA or an analysis of gain scores, chosen as above
Interrupted time series	Segmented regression on the time series
Difference-in-differences	A regression with a group × period interaction
Regression discontinuity	Regression on either side of the cutoff

One more thing catches dissertations out: clustering. If you assigned whole classes or schools rather than individual students, the students within each are more alike than students chosen at random, and an analysis that treats them as independent overstates your precision.

The WWC lists failing to “account for clustering in an individual-level analysis for a cluster-level assignment study” among the cases where it recalculates a study’s statistical significance itself rather than accept the reported result.

It’s also why the two-class example above is only an illustration. With a single class, school or ward per condition, the unit and the intervention can’t be separated: the WWC calls this an “N = 1 confounding factor,” and a study with one is rated as not meeting its standards, however carefully it’s analyzed. If your groups are intact units, use several per condition if you can, and raise the analysis with your chair or a statistician before you begin.

The threats your committee will raise

A threat, in this sense, is anything other than your intervention that could explain your result. Every quasi-experiment has the same weakness, and the health research review puts it in one sentence: “the key threat to internal validity of QEDs is a lack of similarity between the comparison and intervention groups or time periods.” Shadish, Cook and Campbell break that weakness into named threats. Here are the ones that come up most often, each with the design move that answers it:

Threat and what it means (Shadish, Cook & Campbell)	How to answer it
Selection: “Systematic differences over conditions in respondent characteristics that could also cause the observed effect”	A pretest; matching; checking baseline equivalence
History: “Events occurring concurrently with treatment could cause the observed effect”	A comparison group exposed to the same events; a controlled time series
Maturation: “Naturally occurring changes over time could be confused with a treatment effect”	A comparison group; several pretests to show the existing trend
Regression: Units selected for extreme scores tend to score less extremely next time	Avoid selecting on extreme scores; if you must, draw the comparison group from the same population with the same cutoff
Attrition: Loss of participants “systematically correlated with conditions”	Report dropout by group and compare who left
Testing: “Exposure to a test can affect scores on subsequent exposures to that test”	Give the comparison group the same tests at the same times
Instrumentation: “The nature of a measure may change over time or conditions”	Same instrument, same scoring, same conditions for both groups

Notice that most of the answers are design and measurement choices: in a quasi-experiment, you answer threats with design wherever you can, not with argument alone. As their methods text puts it, the researcher “has to enumerate alternative explanations one by one, decide which are plausible, and then use logic, design, and measurement to assess whether each one is operating.”

The best dissertations and theses name their own threats before a committee member can. Here’s a marketing PhD doing it, straight after reporting a result from state-level data:

Look at the structure. It names confounding (“other unobserved metrics”), then history (“other changes to the SNAP program in the preceding year”), then what the design can’t show, and then what the author did about it. You may not be able to add a controlled experiment, but you can copy the sequence: name the threat, then say what in your design answers it, or admit that nothing does.

A school-level EdD shows the same honesty in a single sentence:

Griffin compared one school that adopted Positive Behavioral Support with “a similar elementary school within the same school district,” using three years of archival data that start the year before the program. That first year is valuable: a year of data before the intervention, for both schools, is the raw material for a difference-in-differences analysis, though with a single pre-year, whether the two schools were on parallel trends beforehand can’t be checked.

The design’s limit is the one the WWC calls an N = 1 confounding factor: with one school per condition, the program and everything else about that school can’t be separated. If you’re planning a school-level study, more schools per condition and data reaching back before the intervention are the two biggest upgrades.

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What a quasi-experiment can and can’t claim

A quasi-experiment can support a causal claim, but a more cautious one than a randomized experiment. Shadish, Cook and Campbell explain why: “quasi-experimental control groups may differ from the treatment condition in many systematic (nonrandom) ways other than the presence of the treatment.” The WWC makes the same point in its ratings: the highest a quasi-experimental study can receive is “Meets WWC Standards With Reservations,” because “there may be differences between groups in unobservable characteristics.”

Here’s the line, side by side:

You can claim	You can’t claim
Results consistent with an effect of the intervention	That the intervention definitely caused the change
That your design addresses the alternative explanations it was built for (a comparison group facing the same events addresses history, for example)	That the groups were equivalent on things you didn’t measure
An estimate of the effect’s size in your setting	That the same effect would appear in other settings or groups

The left column is what your discussion chapter can say with confidence. The right column belongs in your limitations section, stated plainly, before anyone else has to point it out.

That doesn’t make the design second-rate. The health research review is clear that “randomized designs are still preferred over quasi-experiments except where randomization is not possible,” and in many dissertations set in schools, hospitals and organizations, it isn’t. What it changes is your language. Instead of “the program caused the improvement,” write that the results are consistent with an effect of the program, then say which alternative explanations your design rules out and which it can’t.

If you’d like help choosing a design or defending the one you have, our coaches help students with their research methodology, from the design decision to the threats section your committee will read most closely.

Still have questions?

Is quasi-experimental research quantitative or qualitative?

Quantitative. A quasi-experiment measures outcomes and compares them statistically between groups or time periods. Some dissertations pair one with interviews in a mixed methods design, but the quasi-experiment itself is the quantitative part.

What are the main types of quasi-experimental design?

There’s no single official list. The designs you’ll meet most often in dissertations are the nonequivalent groups pretest-posttest design, interrupted time series, difference-in-differences and regression discontinuity, often strengthened by matching. The one-group pretest-posttest design is common too, but Campbell and Stanley classed it as pre-experimental.

What’s the difference between quasi and true experiments?

Random assignment. In a true experiment, a random process decides who gets the intervention, so the groups differ only by chance at the start. In a quasi-experiment, the people themselves choose, or you or an administrator decide, so the groups may differ in ways that also affect the outcome.

Is a one-group pretest-posttest quasi-experimental?

Sources disagree. Campbell and Stanley’s 1963 text classed it as pre-experimental, while a widely cited 2002 methods text lists it among the quasi-experimental designs that lack a control group. Either way, it’s hard to interpret: without a comparison, anything else that changed between the two measurements could explain the result. Adding a comparison group or a second pretest makes it considerably easier to interpret.

Can a quasi-experiment prove cause and effect?

Not with the confidence of a randomized experiment. It can support a causal conclusion if its design rules out the main alternative explanations, such as differences between the groups or events happening at the same time. Write your conclusions as consistent with an effect, and say which explanations you could and couldn’t rule out.

Does a quasi-experiment need a control group?

Not always, but it needs something to compare against: a comparison group that didn’t get the intervention, or a comparison period, as in an interrupted time series with many measurements before the change. With neither, just one measurement before and one after, it’s a one-group pretest-posttest design, which Campbell and Stanley classed as pre-experimental and which is much harder to interpret.

What’s the difference between quasi and natural experiments?

In a quasi-experiment, the cause can be manipulated, such as a new program someone chose to introduce, but people aren’t randomly assigned to it. In a natural experiment, the contrast comes from an event the researcher didn’t control: in the narrow sense, something nobody can manipulate, like a natural disaster; in the broader sense, also a decision made outside the study, like a new law. The terms overlap, so describe what happened rather than relying on the label.

Should I use ANCOVA or gain scores?

It depends on how your groups were formed. If people were assigned based on their pretest scores, ANCOVA is the appropriate choice. If you’re comparing pre-existing groups that happened to differ at the start, a methodological comparison of the two suggests gain scores are less biased. Choose in advance, justify the choice, and report the other analysis as a check.

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Jansen, D. (2026). Quasi-Experimental Design: Types, Examples and Analysis. Grad Coach. https://gradcoach.com/quasi-experimental-design/

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