Translated from the Portuguese original. Read the original (Português)
Single-case designs are experiments in which the same person is followed over time and serves as their own control: their behavior is compared under conditions the researcher turns on and off on purpose, instead of comparing two different groups of people. This is not a case report or an anecdote — what makes them an experiment is the systematic manipulation of the intervention combined with repeated measurement of the behavior. The intervention is concluded to have caused the change when the same effect is demonstrated at least three times, at three different points in time. There are four classic families — withdrawal/reversal, multiple baseline, alternating treatments, and changing criterion — and choosing among them depends on the question one wants to answer and on clinical and ethical constraints, not on preference.
Single-case designs (also known as single-case experimental designs, SCED, or single-subject/within-subject designs) form a family of experimental designs in which the individual case — a person, a dyad, a classroom — is the unit of analysis and functions as its own control. The dependent variable is measured repeatedly over time while the independent variable is systematically manipulated by the researcher, alternating conditions (typically baseline and intervention). Experimental control doesn't come from comparison with a parallel group, but from replication within the case itself: a functional relation is considered documented when the effect is demonstrated at least three times — at three distinct points in time or, an alternative added by version 5.0 of the What Works Clearinghouse (WWC) standards, across three phase repetitions. The taxonomy established in the field's handbooks brings together four prototypical designs — withdrawal/reversal, multiple baseline, alternating treatments, and changing criterion — plus their combinations and variants; it is to these that the international SCRIBE 2016 reporting guideline applies.
How an experiment fits inside one person
The question group research answers is: on average, did people who received this treatment do better than people who didn't? It's an excellent question — and an insufficient one for someone facing a specific child, at a specific school, next Tuesday. The clinical question is different: is this procedure working for this person? Single-case designs were built to answer exactly that second question, with experimental rigor.
The trick is to swap the axis of comparison. In a group design, different people are compared at the same point in time. In a single-case design, the same person is compared at different points in time, under conditions the researcher controls. The "control group" is the person themselves when the intervention wasn't in effect.
That's where the biggest misunderstanding about these studies comes from. "N = 1" doesn't mean a single measurement: it means many measurements of a single case. A single-case study typically has dozens of data points — far more observations of the same behavior than a group trial collects per participant. It's worth separating three things common sense tends to blur together:
- Case report — describes what happened to someone. There is no planned manipulation and no systematic repeated measurement. It's useful for raising hypotheses; it doesn't test anything.
- Case series — several reports put together. More cases, same limitation: without a control condition, there's no way to attribute the change to the treatment.
- Single-case design — an experiment: the intervention is introduced, withdrawn, staggered, or alternated on purpose, at points chosen by the researcher, with continuous measurement of the behavior before, during, and after.
This tradition is neither new nor marginal. It grows out of the experimental analysis of the individual organism's behavior, was systematized by Murray Sidman in Tactics of Scientific Research (1960), and became the methodological backbone of Applied Behavior Analysis when Baer, Wolf, and Risley (1968) listed, among the field's dimensions, the requirement of being analytic — that is, of demonstrating experimental control over the behavior one proposes to change. Medicine has a close cousin: the n-of-1 trial, in which a single patient goes through multiple crossovers between treatment and comparator, generally in randomized, blinded fashion. In the Oxford levels of evidence (OCEBM, 2011), the randomized n-of-1 trial appears at level 1 for the question of treatment benefit — on the same rung as systematic reviews of randomized trials. It's worth noting the caveat the Oxford center itself makes: level 1 refers to randomized n-of-1 trials or to systematic reviews of randomized trials — not to systematic reviews of n-of-1 trials. That a single-patient design occupies that rung isn't generosity on the table's part: it's the recognition that, to decide about this patient, testing on that very patient is the most direct evidence available.
The mechanism: prediction, verification, and replication
Almost every single-case design is a setup built to carry out three tasks described in the logic of the baseline: predict what would happen without intervening, verify that the prediction was right, and replicate the effect to rule out coincidence. What distinguishes one design from another is how each one handles verification.
In the withdrawal design, verification comes from turning the intervention off and watching the behavior return to its previous level. In multiple baseline, it comes from the series that haven't received anything yet and stay stable while the first one has already changed. In changing criterion, it comes from each prior step, which serves as the baseline for the next one. In all these cases, the conclusion only holds up when the pattern repeats — and a simple A-B design, with a single phase change, has no way to repeat anything.
The alternating treatments design is the interesting exception: it doesn't rely on an extended baseline from which to draw the prediction. In it, conditions are interleaved so many times that each new alternation is, at the same time, verification and replication — if the difference between conditions keeps reappearing session after session, regardless of the order they came in, that difference is neither chance nor the mere passage of time.
The four families
The field's handbooks converge on four prototypical designs — the same four covered by the SCRIBE 2016 reporting guideline — which answer different questions and have different blind spots. Explore each one:
Withdrawal and reversal — turning it on and off
This is the most straightforward design. A is the baseline, B is the intervention. B is introduced, withdrawn (returning to A), and reintroduced. The three demonstrations of the effect are exactly these three transitions: the behavior changes when the intervention comes in, returns to its previous level when it goes out, and changes again when it comes back.
- Answers: "did this intervention produce the change?"
- Requires a reversible behavior. It works for behaviors maintained by contingencies currently in effect; it's useless for learned skills — you can't "unteach" someone to read to prove the teaching worked.
- B-A-B variant: when the behavior is dangerous and there's no time for an initial baseline, you start with the intervention. You lose the description of the problem before treatment, and with only two phase changes, the arrangement falls short of the three demonstrations quality standards call for — which is why it's usually extended (B-A-B-A-B) or combined with another design.
- A note on terminology: part of the literature calls withdrawal simply turning the intervention off, and reserves reversal for inverting the contingency — for example, switching to reinforcing the incompatible behavior, as in differential reinforcement. In practice, the two terms circulate as synonyms for A-B-A-B.
- Blind spot: withdrawing a treatment that's working. That's a real cost to the person, and for behaviors that cause harm, it can be simply unacceptable.
An isolated A-B — measured before, intervened, measured after — is useful for tracking a case in the clinic, but it's not a complete experiment: there's a single phase change, no verification, and no replication.
Multiple baseline — staggering instead of withdrawing
Instead of turning the intervention off, three or more simultaneous series are measured at baseline, and the intervention is introduced in one series at a time, in staggered fashion. The series that haven't received anything yet do the job withdrawal would do: they show that the behavior would have stayed at the same level if the intervention hadn't arrived. It's one of the most frequent arrangements in applied research, and it was already described in Baer, Wolf, and Risley's founding 1968 paper.
- Three possible arrangements: across behaviors (several targets for the same person), across settings (the same behavior at home, at school, in therapy), or across participants (several people with the same target).
- Decisive advantage: no one loses the treatment. It works for skills that, once learned, don't come undone — and for situations where withdrawal would be unethical.
- Requires a delicate balance: the series need to be functionally independent (changing one shouldn't change the others) while also being similar enough to respond to the same intervention.
- Blind spot 1 — covariation: if the change "spills over" into series that haven't been treated yet, verification is lost. Clinically it's good news (generalization occurred); experimentally, it muddles attribution.
- Blind spot 2 — waiting too long: the last series can stay at baseline for a long time without getting help. Beyond the ethical cost, measuring repeatedly for too long can, by itself, alter the behavior.
- Variants addressing this problem: the multiple probe design, proposed by Horner and Baer in 1978, replaces continuous measurement with intermittent probes in the waiting series — designed for skills taught in sequence. There's also the delayed multiple baseline, in which new series enter the study after it has already begun.
Alternating treatments — comparing two options
Also called the multielement design, it rapidly alternates two or more conditions with the same person, in counterbalanced or randomized order — a morning session with procedure 1, an afternoon session with procedure 2, reversed the next day. The comparison isn't between long phases, but between conditions that are interleaved.
- Answers: "among these two or three options, which works better for this person?" It's the design for choosing between procedures — two types of prompt, two teaching formats, two candidate reinforcers.
- Practical advantages: it doesn't require withdrawal, doesn't require a long baseline, and gives quick answers. It can even operate without a baseline phase, when the question is purely comparative.
- Blind spot — interference between treatments: conditions that alternate can contaminate each other. There are carryover effects (what was done in the previous session still acts on the next one) and sequence effects (the order conditions appear in changes the result). Counterbalancing the order, randomizing conditions, and spacing sessions apart reduces the problem but doesn't eliminate it — and the effect observed is always that of one condition in the context of alternating with the other.
- Watch the sample size: each condition needs enough data points on its own — too few sessions on either side can't sustain any comparison. The WWC's pilot single-case standards (2010) called for five points per condition for the top rating, and four for the rating with reservations.
Changing criterion — climbing step by step
Described by Hartmann and Hall in 1976 as a form of multiple baseline, this design doesn't turn the intervention on and off: instead, in successive steps, it changes the criterion the behavior needs to reach to produce reinforcement. Each subphase works as the baseline for the next, and the demonstration of the effect is the behavior tracking each new criterion — neither too far above nor too far below.
- Answers: "can I bring this behavior, gradually, up to the goal?"
- Indicated for behaviors already present in the repertoire that need to gradually increase or decrease: time spent on physical activity, number of tasks completed, academic fluency, reducing a habit. The original paper illustrated the design with two case studies, one of them on smoking reduction.
- Good practices: only move to the next step once the subphase has stabilized; vary the length of the subphases and the size of the criterion jumps, so the improvement can't be mistaken for a simple upward trend; and return to an earlier criterion at some point, which strengthens the demonstration considerably.
- Blind spot: if all the steps are the same size and the same length, any ordinary upward trend would mimic the expected result. And if the behavior shoots far past the criterion, control becomes hard to demonstrate.
Which design for which question
The choice isn't a matter of taste: each design buys an answer with a different currency. A quick map:
- "Does this intervention work?", and the behavior is reversible and not dangerous → A-B-A-B.
- "Does this intervention work?", but it's a new skill or withdrawal would be unacceptable → multiple baseline.
- "Which of the two works better?" → alternating treatments.
- "Can we get to the goal in stages?", with the behavior already in the repertoire → changing criterion.
- Dangerous behavior, no time for a baseline → B-A-B, or a deliberately brief initial baseline.
- Skills taught in sequence (steps of a chain, rungs of a curriculum) → multiple probe.
In applied practice, combinations are the rule, not the exception: a reinforcer assessment using alternating treatments precedes teaching evaluated with a multiple baseline across settings; a functional analysis is itself a single-case design — generally multielement — applied to the question "what function does this behavior serve?"
When a single case counts as evidenceAnyone reading a single-case study needs to check three things before the graph. Was the manipulation done by the researcher? Condition changes that simply happened — the school changed teachers, the family changed its routine — aren't a manipulated independent variable, and the study stops being experimental. Is the measure reliable? What Works Clearinghouse standards require more than one observer measuring the same behavior, with interobserver agreement calculated over at least 20% of the data and a floor of 0.80 percentage agreement or 0.60 Cohen's kappa. (Without this, there's no way to know whether what changed was the behavior or the eye of whoever was recording it.) It's worth noting the bar has moved: in the 2010 technical documentation, coordinated by Kratochwill and colleagues, that agreement was required in each condition; version 5.0 of the handbook (2022) began applying it to the study's data as a whole. Are the phases long enough? A phase only counts as an attempt at demonstration with at least three points, and the top rating calls for five or more per phase — a requirement version 5.0 raised to six or more in the initial baseline of reversal, multiple baseline, multiple probe, and changing criterion designs. Anyone about to read the graph that follows will find the roadmap in the visual analysis entry. And anyone writing up the study has the SCRIBE 2016 guideline (Tate and colleagues), with 26 reporting items — among them the design used, the sequence of phases, and the rules that decided when to change conditions.
Where these designs slip up
No design is good at everything. The four traps below are the ones that show up most often in studies and in clinical follow-up. Flip the cards:
What a single case doesn't prove
Well conducted, a single-case design has high internal validity: it gives a strong answer about what caused the change in that case. What it doesn't deliver for free is external validity — the guarantee that the same procedure would work with another person, in another setting, with another implementer. That guarantee comes from replication: repeating the study with similar participants (direct replication) and deliberately varying procedures and conditions (systematic replication).
That's how the field accumulates knowledge. Dozens of single-case studies on the same procedure can be pulled together in systematic reviews, and it's from that sum — not from a single isolated graph — that recommendations for evidence-based practice emerge. It's worth noting that the best-known evidence hierarchies were designed to rank evidence about populations, which is why they favor the randomized clinical trial — with the exception already mentioned of the Oxford table, which makes room on its top rung for the n-of-1 trial. For the question "is this treatment working for this person, right now?", the single-case design is the right tool — and both types of question are necessary.
Finally, reading these graphs has its own method and requires training: it's visual analysis. And even with flawless experimental control, there remains a question no graph answers — does the change matter in the person's life? That's the question of social validity, and it isn't settled by the design, but by whoever lives with the result.
The design is an ethical decision, not just a technical oneTwo points call for care. Withdrawing an intervention that's working produces the cleanest demonstration of all — and temporarily hands the person back the problem that had been solved. When the behavior carries a risk of harm, that withdrawal can be simply unacceptable, and the right choice is a design that verifies without turning anything off. Prolonging baselines carries the same cost from the opposite direction: the last series in a multiple baseline can wait many sessions to get help. There are technical workarounds — intermittent probes, brief withdrawals, delayed entry of new series — but the rule that organizes them is simple: experimental rigor doesn't authorize keeping someone without the treatment they need. In research, these decisions go through an ethics committee and through consent and assent; in the clinic, through that same honest conversation with the family.
Test your understanding
Quick quiz
Three questions to lock in the concept. You'll see the explanation right away.
Further reading
- Cooper, J. O., Heron, T. E. & Heward, W. L. Applied Behavior Analysis. 3rd ed. Pearson, 2020 — chapters on reversal and multielement designs, multiple baseline, and changing criterion.
- Kratochwill, T. R. et al. Single-Case Designs Technical Documentation. What Works Clearinghouse / Institute of Education Sciences, 2010 — design standards, interobserver agreement, and demonstration of effect.
- What Works Clearinghouse Procedures and Standards Handbook, version 5.0. Institute of Education Sciences, 2022 — current standards, including the changes in interobserver agreement and initial baseline length.
- Tate, R. L. et al. “The Single-Case Reporting Guideline In BEhavioural Interventions (SCRIBE) 2016 Statement”, 2016 — a 26-item reporting guideline, published simultaneously in several journals in the field.
- Baer, D. M.; Wolf, M. M.; Risley, T. R. “Some current dimensions of applied behavior analysis”. Journal of Applied Behavior Analysis, 1(1), 91–97, 1968.
- Horner, R. D. & Baer, D. M. “Multiple-probe technique: a variation of the multiple baseline”. Journal of Applied Behavior Analysis, 11, 189–196, 1978.
- Hartmann, D. P. & Hall, R. V. “The changing criterion design”. Journal of Applied Behavior Analysis, 9, 527–532, 1976.
- Sidman, M. Tactics of Scientific Research: Evaluating Experimental Data in Psychology. Basic Books, 1960.
- Kazdin, A. E. Single-Case Research Designs: Methods for Clinical and Applied Settings. 3rd ed. Oxford University Press, 2020.
This entry is educational and does not replace assessment, diagnosis or treatment by a qualified health professional. Every person is unique — for a specific case, seek individual guidance.