Quasi-Experimental Design: Definition, Types, and Examples
A quasi-experimental design “by definition lacks random assignment”, and everything that follows — which comparisons you can make, how much confounding you must argue away, whether a systematic review will even accept the study — follows from that single missing feature.
- The one feature that separates quasi-experimental from experimental designs, and what it costs you
- Each design type with a published study showing how it works in practice
- The minimum requirements each design must meet, and how reviewers appraise the result
- “One group, measured before and after, is a quasi-experimental design.” It is — and it is also the version a systematic review is most likely to throw out. Cochrane’s Effective Practice and Organisation of Care group lists uncontrolled before-after studies among designs that are “strongly discouraged”, and sets a floor of two intervention and two control sites for a controlled before-after study. Running the single-group version is the most common way to produce a study that cannot be synthesised with anything else.
What a quasi-experimental design is
A quasi-experimental design is a quantitative design that examines the impact of an intervention on a target population without randomly assigning people to treatment and control groups. It is action-focused, and it shares most of the visible machinery of a true experiment — pretests, post-tests, comparison groups — while lacking the one feature that makes an experiment an experiment.
Those designs set out to do what experiments do: they “test causal hypotheses”. As UNICEF’s methodological brief states it, “a quasi-experimental design by definition lacks random assignment”.1 That single absence is the fundamental difference, and it is the source of every complication below.
Something still has to determine who receives the intervention. In a quasi-experiment that something is “self-selection” or “administrator selection”, or both.1 People choose to enrol, or a programme officer, clinician or school decides who is enrolled. Either way the groups differ before the intervention starts, and the entire methodological effort of a quasi-experiment goes into establishing how much of the final difference was already there.
That is the whole subject in one sentence. The techniques below are different answers to the same question: what would these people have looked like without the intervention?
Quasi-experimental vs experimental
Cochrane’s EPOC group defines the two in parallel, and the definitions differ by one word:2
| Design | EPOC definition2 |
|---|---|
| Randomised trial | “An experimental study in which people are allocated to different interventions using methods that are random.” |
| Non-randomised trial | “An experimental study in which people are allocated to different interventions using methods that are not random.” |
Both are experimental studies — in both, an investigator allocates an intervention. The difference is the allocation method, and EPOC notes that non-randomised trials carry a greater risk of bias than randomised ones.2
Quasi-experimental is not a synonym for observational. In a quasi-experiment someone still assigns the intervention; it is the method of assignment that is not random. In a purely observational study nobody assigns anything — exposure is simply recorded as it occurs. That is why quasi-experimental designs sit between randomised trials and observational studies rather than alongside the latter.
When it is the right choice
Quasi-experimental methods are “most often used when it is not possible to randomize individuals or groups”, which is always the case when an evaluation is designed after a programme has already run.1 Even when an evaluation is planned in advance, randomisation may be ruled out by “ethical, political or logistical constraints, like the need for a phased geographical roll-out”.1
There is an ethical argument in their favour as well, and it is often understated. Because these designs work with “pre-existing or self-selected groups”, they avoid withholding or delaying a treatment that may well be effective.1 Where equipoise is genuinely absent, that is not a compromise — it is the correct choice.
What you give up is stated just as plainly: causal conclusions from a quasi-experiment are “less definitive” than those from a well-conducted randomised trial.1 The design is a response to a constraint, not an upgrade.
The main types
The designs below answer the counterfactual question in different ways. Which one you can use is usually decided by the data you have, not by preference. The examples name real published studies; three of them are worked through in full in the next section.
| Type | Description | Example in research | Advantages | Limitations |
|---|---|---|---|---|
| Controlled before-after (non-equivalent control group) | Intervention and control groups, each measured before and after the intervention; groups are not formed at random2 | Service-level evaluations where whole sites adopt a change; Cochrane EPOC accepts them with at least two intervention and two control sites2 | Intuitive to run and report; a concurrent control absorbs background change affecting both groups | Sites may differ systematically; excluded if measurement is not contemporaneous or uses different methods2 |
| Interrupted time series | Repeated observations at multiple time points before and after a clearly dated intervention2 | Italy’s 2005 indoor smoking ban and hospital admissions for acute coronary events in Sicily3 | Uses routine data already collected; separates a step change from an existing trend; needs no control group | Vulnerable to co-occurring events, changes in data recording, seasonality and autocorrelation3 |
| Regression discontinuity | Compares outcomes just either side of an eligibility threshold; sharp when the threshold fully determines treatment, fuzzy when it only shifts the probability4 | The age-21 minimum legal drinking age in the United States and mortality among 19–22 year olds6 | Where the threshold is enforced, internal validity at the cut-off approaches that of a trial | The estimate is local to the threshold, giving “fundamentally only a limited degree of external validity”4 |
| Difference-in-differences | Compares the change over time in a treated group with the change in an untreated one; the “double difference” method1 | New Jersey’s 1992 minimum wage rise and fast-food employment, against eastern Pennsylvania5 | Removes fixed differences between groups and common time trends; works with repeated cross-sections | Rests on parallel trends, and on its own usually does not address selection bias1 |
| Propensity score methods | Participants matched, stratified or weighted on “the probability of treatment assignment conditional on observed covariates”7 | Applied within observational and quasi-experimental datasets via matching, stratification, inverse probability of treatment weighting, or covariate adjustment7 | Balances the distribution of measured baseline covariates between treated and untreated subjects7 | Rests on a no-unmeasured-confounders assumption; unobserved characteristics affecting participation still bias the estimate1 |
| Regression-based methods | Modelled outcomes with explicit adjustment for the selection process | “Instrumental variable estimation and sample selection models”1 | Can address selection on unobservables where a valid instrument exists | Ordinary least squares does not account for selection at all1 |
| Single-group pretest-posttest (uncontrolled before-after) | One group measured before and after, with no comparison group | Common in service evaluation and audit where no comparator exists | Feasible when nothing else is; may be the only option for a one-off change | Cannot separate the intervention from secular trend; “strongly discouraged” by Cochrane EPOC2 |
| Post-test-only with non-equivalent groups | A group that received the intervention is compared with one that did not, measured only afterwards, with no baseline and no random allocation. Campbell and Stanley call this the static-group comparison: “a group which has experienced X is compared with one which has not, for the purpose of establishing the effect of X”10 | Evaluations begun after an intervention has already run, where no baseline was collected and none can be reconstructed | Sometimes the only option left; cheap and quick, since it needs one round of measurement | There are “no formal means of certifying that the groups would have been equivalent had it not been for the X”10. Any difference “could well have come about through the differential recruitment of persons making up the groups”10. Cochrane EPOC’s eligible controlled designs all require measurement in both groups before the intervention,2 which this design cannot supply |
Two of these are frequently misread. Regression discontinuity does not estimate an average effect for the whole population — it estimates one at the cut-off, and for fuzzy designs only among compliers there.4 And difference-in-differences is not a fix for selection bias; it removes fixed differences between groups, leaving any divergence in their underlying trends untouched.1
Worked examples from published studies
Each of the three below is a real published study, chosen because its design is unusually legible. Figures are reproduced as the authors report them.
- Intervention
- Nationwide ban on smoking in indoor public places, in force 10 January 2005
- Population
- Sicily, Italy; people aged 0–69, 2002–2006
- Outcome and data
- Hospital admissions for acute coronary events (ICD-10 410–411); 59 months of routine data, roughly 600–1,100 events per time point
- Analysis
- Poisson segmented regression modelling a level change with no lag
The tutorial’s authors are explicit that this example is included to illustrate the method, not to add to the substantive evidence on smoking bans.3 It is reproduced here on the same terms.
- Intervention
- New Jersey’s minimum wage rose from $4.25 to $5.05 an hour on 1 April 1992; Pennsylvania’s did not change
- Sample
- 410 fast-food restaurants in New Jersey and eastern Pennsylvania — Burger King, KFC, Wendy’s and Roy Rogers. McDonald’s was excluded after a pilot produced very low response rates
- Measurement
- Two telephone waves: 15 February–4 March 1992, about a month before the rise, and 5 November–31 December 1992, about eight months after
- Follow-up
- 87% response at wave 1; 399 of 410 stores reached at wave 2, with closures tracked and retained in the analysis
The authors report that the estimate is sensitive to specification. Tracking closed stores rather than dropping them matters here: a design that loses its failures measures only its survivors.
- Threshold
- The United States minimum legal drinking age of 21, with the analysis covering adults aged 19–22
- Data
- National Health Interview Survey alcohol data, 1997–2005; National Center for Health Statistics mortality files, 1997–2004; Census population denominators
- Outcome
- Mortality — the log of the number of deaths at each exact age, also reported as deaths per 100,000 person-years
- Why it works
- Turning 21 is arbitrary with respect to almost everything else about a person, so those just under and just over the threshold are otherwise comparable
A textbook illustration of what “local” means: the estimate is credible at age 21 and says nothing directly about drinking at 30.4
Further published examples, by field
The studies below were selected to show the designs at work across different settings. Each is cited so the design statement can be checked against the paper. Readers looking for a methods treatment rather than a study should go to Penfold and Zhang, a tutorial on using interrupted time series to evaluate quality improvement, which works through a hypothetical Medicaid example and supplies sample analysis code.18
| Field | Study | Design, in the authors’ words | What it did |
|---|---|---|---|
| Nursing education | ECG-interpretation software for undergraduate nursing students, Iran11 | “A nonequivalent control group pretest-posttest design”11 | Compared purpose-built ECG software with conventional teaching among third- and fourth-year nursing students at two Iranian educational hospitals |
| Nursing education | Paediatric nursing competency programme, South Korea12 | “A quasi-experimental study” using a nonequivalent control group pretest-posttest design12 | Combined problem-based learning, simulation and clinical practice into a competency programme and tested it on 40 nursing students |
| Nursing education | Management in Nursing course and time management13 | “a semi-experimental, single-group pre-test/post-test design”13 | Measured 133 fourth-year nursing students before and after a management course, on time management and career planning attitudes |
| Nursing education | Mixed reality before an acute coronary syndrome simulation, South Korea14 | “utilized a single-group pretest-posttest design”14 | Gave 39 senior nursing students a mixed-reality preparation session before a team simulation and measured the change |
| Health economics | Teacher training and HIV/AIDS prevention, Cameroon15 | A “regression discontinuity design identification strategy”15 | Used the administrative cut-off that decided where the programme was rolled out to estimate its effect on schoolgirls’ sexual behaviour and childbearing |
| Health services research | Emergency department medication review and outpatient utilisation, British Columbia16 | “a population-based evaluation of a continuous quality improvement project using administrative health data”16 | Compared outpatient physician and emergency visits for 10,783 high-risk adults across three hospitals, before and after pharmacist-led medication review |
| Critical care pharmacotherapy | Vasopressin guideline in septic shock17 | “This retrospective quasi-experimental study”, analysed as an interrupted time series17 | Compared monthly mortality and drug costs for 1,148 medical ICU patients in the year before and after a guideline change |
Two things are worth noticing in that table. First, the clinical topic in a title names the subject matter, not the field: four of these seven are nursing education studies, whatever the ECG, paediatric or acute coronary syndrome in their titles might suggest. Second, authors label the same design differently. One paper above calls itself “semi-experimental”;13 another describes itself in one place as a population-based evaluation and in another as a “non-randomized, non-blinded controlled clinical trial”.16 Classify a study by what was done to whom and when it was measured, not by the phrase in the abstract.
How these designs appear in education research
Three patterns recur, and each has a worked instance above.
- A new teaching method against the existing one. Two intact classes or cohorts, one taught the new way, both measured before and after: a non-equivalent control group design. The ECG software study is this pattern.11
- The effect of a course on the students who took it. One cohort measured at the start and at the end, with no comparison group: a single-group pretest-posttest design, and the weakest of the three, because nothing separates the course from everything else that happened over a semester.132
- A programme rolled out by an eligibility rule. Where a threshold decides which schools or districts receive an intervention, that threshold can carry the comparison: a regression discontinuity design. The Cameroon teacher-training evaluation is this pattern.15
What the results look like
Each design has a characteristic results figure, and a reader who knows the shape can judge the claim before reading the statistics. The four below are schematic — they show what to look for, not data from any study.
Repeated measurements, a dated intervention, and a counterfactual carried forward from the pre-intervention trend.
What to look for. A level change, a slope change, or both. The claim rests entirely on the dashed counterfactual being a fair extrapolation, which is why anything else that changed at the same moment — a new diagnostic test, a change in how the data were recorded — destroys the inference.3
Schematic. Illustrative shapes, not data from any study.
Two groups, two time points, and a counterfactual built by assuming the treated group would have moved parallel to the control.
What to look for. Whether the two groups were moving in parallel before the intervention. The estimate is the vertical gap between the treated line and its dashed counterfactual; if the trends were already diverging, that gap measures the divergence rather than the intervention.1
Schematic. Illustrative shapes, not data from any study.
Outcome plotted against the variable that decides eligibility, with a fitted line either side of the threshold.
What to look for. A visible step at the cut-off and smooth, well-behaved data either side. The estimate is the size of that step — and it is local to the threshold, which is why the design carries “fundamentally only a limited degree of external validity”.4
Schematic. Illustrative shapes, not data from any study.
The standard check reported alongside a propensity score analysis, usually called a love plot.
What to look for. Every covariate pulled close to zero after matching. This figure demonstrates that “the distribution of measured baseline covariates is similar between treated and untreated subjects”7 — and that is all it demonstrates. A perfect love plot says nothing about the covariates nobody measured.1
Schematic. Illustrative shapes, not data from any study.
Whichever design you use, the figure should show the raw data points and not only the fitted lines. A fitted line alone hides the scatter that tells a reader whether the model was reasonable, and TREND’s checklist exists precisely to prevent such selective presentation.9
The thresholds that decide whether a design counts
This is the part most introductions leave out, and it is the part that determines whether your study can later be pooled with others. Cochrane EPOC publishes explicit minimum requirements, and a study that misses them is excluded regardless of how well it was conducted.2
| Design | Stated minimum2 |
|---|---|
| Interrupted time series | “At least three data points before and three after the intervention”, and “a clearly defined point in time when the intervention occurred” |
| Controlled before-after | “At least two intervention sites and two control sites”. Studies with only one intervention or control site are excluded |
| Cluster-randomised trial | “We recommend only including studies with at least two intervention sites and two control sites” |
| Uncontrolled before-after, cross-sectional | “Strongly discouraged” |
Two further exclusions apply to controlled before-after studies specifically: data collection that “is not contemporaneous in study and control sites”, and data collection that “does not use identical methods of measurement”.2 Both are decided when you design the study, and neither can be repaired afterwards.
EPOC’s three-points-either-side rule decides whether a study can enter a review. It does not tell you whether the study can detect anything. The interrupted time series tutorial is explicit that there is no fixed minimum number of data points, that power rises with more of them, and that studies with few time points or small expected effects “should be interpreted with caution as they may be underpowered” — recommending simulation-based power calculations in those cases.3 Clear the floor, then work out separately how many points you actually need.
How these designs are appraised
Expect your study to be assessed with ROBINS-I, the tool built to evaluate “the risk of bias (RoB) in the results of non-randomized intervention studies”. It covers cohort and case-control studies, controlled before-and-after studies, interrupted time series and quasi-randomised studies.8
It works through seven bias domains, each with signalling questions and an algorithm producing a domain-level judgement, with the domains weighted equally in the overall assessment:8
- Confounding
- Selection of participants into the study
- Classification of interventions
- Deviations from intended interventions
- Missing data
- Measurement of outcomes
- Selection of the reported result
Reading that list at the design stage rather than at review is the single most useful thing you can do with it. Confounding and selection are decided by how the study is set up; measurement and classification by how variables are defined before data collection; missing data by follow-up procedures; and selection of the reported result by whether outcomes were specified in advance.
The time series tutorial names the specific threats for that design, and they map onto the same idea: choosing the impact model from the outcome data rather than a priori can produce spurious findings of effectiveness; a concurrent change such as the introduction of a new troponin test can masquerade as an intervention effect; and a change in how routine data are recorded, if it coincides with the intervention, will look exactly like one.3
Reporting a quasi-experimental study
There is a reporting guideline for exactly this situation. The Transparent Reporting of Evaluations with Nonrandomized Designs — TREND — provides “a 22-item checklist developed to guide standardized reporting of nonrandomized controlled trials”.9
It was created by the CDC’s HIV Prevention Research Synthesis Project with researchers and journal editors, and first published in the American Journal of Public Health in March 2004.9 The CDC describes it as “similar to the CONsolidated Standards Of Reporting Trials (CONSORT) statement developed for randomized controlled trials”.9 CONSORT is the wrong instrument for a study that did not randomise; TREND is the counterpart written for one that did not.
Common mistakes in designing a quasi-experimental study
Almost every one of these is settled before data collection, and none can be repaired by analysis afterwards.
| Mistake | Stage | What it costs | What to do instead |
|---|---|---|---|
| Picking the method before naming the counterfactual | Before design | A technique applied to a question it cannot answer; the assumptions are discovered at review | State in one sentence what the treated group would have looked like untreated, then let that choose the design1 |
| No baseline data | Before design | Rules out most of the stronger designs, permanently — baseline cannot be collected retrospectively1 | Secure baseline measurement before the intervention starts, even if the evaluation is not yet funded |
| Running a single-group before-after study | Design | Cannot separate the intervention from secular trend; “strongly discouraged” by Cochrane EPOC and excluded from its reviews2 | Find a comparison group or a time series; if neither exists, report it as uncontrolled rather than as evidence of effect |
| A controlled before-after study with one intervention site | Design | Excluded regardless of how well it was run — EPOC requires at least two intervention and two control sites2 | Two and two, measured contemporaneously and by identical methods2 |
| Clearing the time-points floor and assuming that is enough | Design | An eligible but underpowered interrupted time series | Three before and three after is an eligibility minimum;2 there is no fixed minimum for power, and few points “should be interpreted with caution as they may be underpowered”3 |
| Choosing the impact model after seeing the outcome data | Analysis | Can “produce spurious findings of effectiveness” — a result manufactured by model selection3 | Specify the shape of the expected effect a priori, before looking at the series3 |
| Never checking pre-intervention trends in a difference-in-differences | Analysis | If the groups were already diverging, the estimate measures the divergence, not the intervention1 | Plot and test the pre-period; the parallel trends assumption is an assumption to defend, not a default |
| Treating difference-in-differences as a fix for selection bias | Interpretation | Overstated causal claims — on its own it usually does not address selection bias1 | It removes fixed differences between groups. Say that, and address selection separately |
| Reading a regression discontinuity estimate as a population average | Interpretation | A conclusion applied far beyond where the design supports it — the estimate is local, with “fundamentally only a limited degree of external validity”4 | Report it as an effect at the cut-off, and for fuzzy designs among compliers there4 |
| Presenting a propensity match as though confounding were solved | Interpretation | A balanced love plot invites a reader to assume balance on everything, including what nobody measured7 | Balance applies to observed covariates only; state the no-unmeasured-confounders assumption and what might violate it1 |
| Appraising or reporting with the wrong instrument | Write-up | Signals the design was not understood; CONSORT is built for trials that randomised | ROBINS-I for appraisal,8 TREND’s 22-item checklist for reporting9 |
| Dropping the raw data from the results figure | Write-up | A fitted line without scatter hides whether the model was reasonable | Plot the observations as well as the fit, and show the counterfactual explicitly3 |
Nine of these twelve are decided before a single observation is recorded. That is the practical difference between a randomised trial and a quasi-experiment: the trial buys its validity with the allocation mechanism, while the quasi-experiment has to buy it with foresight about what will be comparable to what. The design conversation is worth having when the programme is being planned, not when the evaluation is commissioned.
Advantages and limitations
The advantages are real and specific: these designs can evaluate programmes that have already happened, work where randomisation is ethically or politically impossible, and avoid withholding a promising treatment by using pre-existing or self-selected groups.1
The limitation is singular rather than a list. As UNICEF states it, “the bias potentially of concern here is ‘selection’ bias”.1 Every technique above is an attempt to neutralise it, and each neutralises only part:
- Propensity score methods balance the measured baseline covariates between treated and untreated subjects,7 and rest on a no-unmeasured-confounders assumption; if unobserved characteristics affect participation, the estimate remains biased.1
- Difference-in-differences removes fixed group differences but rests on parallel trends, and usually does not address selection bias on its own.1
- Regression discontinuity is credible precisely where it is narrow — at the threshold, and for fuzzy designs only among compliers.4
- Interrupted time series can be undone by anything else that changed at the same moment, including how the data were recorded.3
- Ordinary least squares regression does not account for selection at all; instrumental variable and sample selection models are what do.1
Poor-quality data and missing baseline measurements are the practical barriers that most often decide which of these is available to you.1 Baseline data in particular cannot be collected retrospectively, which is why the design question is worth settling before a programme starts rather than after it ends.
Take-home message
A quasi-experiment is an experiment missing random assignment, so selection bias is the one problem every design choice is trying to solve. Pick the design your data can actually support, plan to clear the published minimums — three data points either side for an interrupted time series, two intervention and two control sites for a controlled before-after study — and report it against TREND.
How to apply this to your work
- Establish whether anyone assigns the intervention. If someone does, but not at random, you have a quasi-experiment. If nobody does, it is an observational study and this framework does not apply.2
- Name your counterfactual before choosing a method. Decide what you are claiming the treated group would have looked like untreated; the design follows from that answer, not the reverse.1
- Check the minimums while you can still change the design. Three data points before and three after for an interrupted time series; two intervention and two control sites for a controlled before-after study.2
- Specify the impact model in advance. Choosing it after seeing the outcome data can produce spurious findings of effectiveness.3
- Secure baseline data. It cannot be collected later, and its absence rules out most of the stronger designs.1
- Read the seven ROBINS-I domains at the design stage. Confounding, selection, classification, deviations, missing data, measurement and selective reporting are all fixable now and none are fixable at review.8
- Write up against TREND, not CONSORT. The 22-item checklist is the one built for nonrandomised evaluations.9
Common questions
Is a quasi-experimental design the same as an observational study?
No. In both quasi-experimental and randomised designs an investigator allocates the intervention — EPOC calls both “an experimental study”, differing only in whether allocation uses “methods that are random”.2 In an observational study nobody allocates anything; exposure is recorded as it happens.
Can a quasi-experimental study support a causal claim?
It can support one, but a weaker one. UNICEF states plainly that causal conclusions from these designs are “less definitive” than those from a well-conducted randomised trial.1 The strength of the claim depends on how convincingly selection bias has been addressed, which is why the method and its assumptions have to be argued explicitly rather than asserted.
How many measurements does an interrupted time series need?
Cochrane EPOC requires “at least three data points before and three after the intervention”, along with “a clearly defined point in time when the intervention occurred”.2 That is an eligibility floor, not a target: the published tutorial on the method says there is no fixed minimum, that power increases with more time points, and that studies with few points may be underpowered.3
Does propensity score matching remove selection bias?
Only the part you measured. The propensity score is “the probability of treatment assignment conditional on observed covariates”,7 so if unobserved characteristics also affect who participates, the estimate stays biased.1 A matched analysis should be reported alongside an argument about what might remain unobserved, not presented as though the problem has been solved.
What is the difference between sharp and fuzzy regression discontinuity?
In a sharp design “the assignment Wi is a deterministic function of one of the covariates” — everyone past the cut-off is treated and nobody before it is. A fuzzy design “allows for a smaller jump in the probability of assignment to the treatment at the threshold”, so crossing it changes the chance of treatment without determining it.4 The fuzzy estimate applies only to compliers at the cut-off.
Which quasi-experimental design is strongest?
The question is better put as which design the available data can support. A regression discontinuity with a genuinely enforced threshold is close to a trial at the cut-off,4 but it needs a real threshold. An interrupted time series needs a clearly dated intervention and enough repeated measurements.2 A difference-in-differences needs a comparison group whose trend would plausibly have tracked yours.1 Design strength is a property of the match between method and situation, not a ranking.
Declared interest: Pubrica provides study design, statistical analysis and manuscript support commercially. Nothing on this page should be read as evidence that any design choice, or paid assistance with one, improves the likelihood of publication — no claim of that kind is made here.
References and sources
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- Cochrane Effective Practice and Organisation of Care (EPOC). What study designs can be considered for inclusion in an EPOC review and what should they be called? EPOC Resources for review authors; 2017. read 20 October 2026.View on Cochrane EPOC
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- Imbens GW, Lemieux T. Regression discontinuity designs: a guide to practice. Journal of Econometrics. doi:10.1016/j.jeconom.2007.05.001 read 20 October 2026, from the author-hosted copy dated 2007; the version of record carries the DOI above.View the author-hosted PDF
- Card D, Krueger AB. Minimum wages and employment: a case study of the fast-food industry in New Jersey and Pennsylvania. American Economic Review. 1994;84(4):772–793. read 20 October 2026, from the author-hosted copy.View the author-hosted PDF
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- Sterne JAC, Hernán MA, Reeves BC, Savović J, Berkman ND, Viswanathan M, et al. ROBINS-I: a tool for assessing risk of bias in non-randomised studies of interventions. BMJ. 2016;355:i4919. doi:10.1136/bmj.i4919 read 20 October 2026, via the National Collaborating Centre for Methods and Tools registry entry.View on NCCMT
- Des Jarlais DC, Lyles C, Crepaz N, and the TREND Group. Improving the reporting quality of nonrandomized evaluations of behavioral and public health interventions: the TREND statement. Am J Public Health. 2004;94(3):361. doi:10.2105/AJPH.94.3.361 read 20 October 2026, via the CDC TREND statement page.View on CDC
- Campbell DT, Stanley JC. Experimental and Quasi-Experimental Designs for Research. Boston: Houghton Mifflin; 1963. Pre-experimental designs, p. 6; the static-group comparison, pp. 12–13. read 20 October 2026.View the full text
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- Koo HY, Lee BR. Development and evaluation of a pediatric nursing competency-building program for nursing students in South Korea: a quasi-experimental study. Child Health Nursing Research. 2022;28(3):167–175. doi:10.4094/chnr.2022.28.3.167 read 20 October 2026.View the record on DOAJ
- Çingöl N, Karakaş M. Effect of the management in nursing course on students’ time management and career planning attitudes: a single-group pre-test post-test study. Nurse Education Today. 2023;125:105797. doi:10.1016/j.nedt.2023.105797 read 20 October 2026 from the author institution’s repository.View in the institutional repository
- Moon SH, Jeong H, Choi MJ. Integrating mixed reality preparation into acute coronary syndrome simulation for nursing students: a single-group pretest-posttest study. BMC Nursing. 2024;23:468. doi:10.1186/s12912-024-02110-9 read 20 October 2026.View on BMC Nursing
- Arcand J-L, Djimeu Wouabe E. Teacher training and HIV/AIDS prevention in West Africa: regression discontinuity design evidence from the Cameroon. Health Economics. 2010;19(S1):36–54. doi:10.1002/hec.1643 bibliographic record and abstract read 20 October 2026; the publisher full text is paywalled.View the record on RePEc
- Kitchen SA, McGrail K, Wickham ME, Law MR, Hohl CM. Emergency department-based medication review on outpatient health services utilization: interrupted time series. BMC Health Services Research. 2020;20:254. doi:10.1186/s12913-020-05108-6 read 20 October 2026.View the full text
- Bauer SR, Sacha GL, Reddy AJ. Mortality, morbidity, and costs after implementation of a vasopressin guideline in medical intensive care patients with septic shock: an interrupted time series analysis. Annals of Pharmacotherapy. 2020;54(4):314–321. doi:10.1177/1060028019886306 read 20 October 2026.View on SAGE Journals
- Penfold RB, Zhang F. Use of interrupted time series analysis in evaluating health care quality improvements. Academic Pediatrics. 2013;13(6 Suppl):S38–S44. A methods tutorial rather than an empirical study. read 20 October 2026; no DOI was printed on the copies reached.View the record and full text
How to cite this article
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This article is written to be learned from. Cite it if you are referring to what it says; if you are using the evidence behind it, cite the sources listed above instead.
Settle these before data collection starts.
[ ] Someone assigns the intervention — otherwise it is observational [ ] The counterfactual is stated in one sentence [ ] Baseline data will exist for both groups [ ] Design chosen from what the data can support, not preference [ ] ITS: at least 3 data points before and 3 after [ ] ITS: the intervention date is clearly defined [ ] ITS: impact model specified a priori, not after seeing the data [ ] CBA: at least 2 intervention sites and 2 control sites [ ] CBA: data collected contemporaneously, by identical methods [ ] Outcomes specified in advance, in writing [ ] Assumptions named — parallel trends, threshold, unobserved confounders [ ] TREND 22-item checklist used for the write-up
We help you choose a design the available data can actually support, check it against the published eligibility minimums before collection starts, and specify the analysis and assumptions so the study holds up when it is appraised.