Chapter 14: Single-Case Experimental Research Designs

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Okay, let's unpack this.

Imagine you're a researcher or maybe a clinician and you've got just one individual you're working with.

Right, like a student with some tricky behavior or a client facing a specific challenge.

Exactly.

And you want to try something new, an intervention.

But how do you really know, like scientifically, if that intervention is the thing causing a change in that one person?

Yeah, you can't just grab a control group of identical twins, can you?

It feels like a real puzzle.

It does.

Because most experiments we think about, they involve big groups, averages.

But so much real world work, especially in clinics or schools, it's about that single individual.

How do you bring scientific rigor to that?

That is precisely the question we're diving into today.

We are cracking open chapter 14 of Research Methods for the Behavioral Sciences, sixth ed.

And this chapter is all about the toolkit for single case experimental designs.

Our mission, really, is to explore this whole area.

What are these designs?

How on earth do they establish cause and effect without groups?

What are the specific techniques, the structures they use, and where do they fit in the big picture of research methods?

Think of it like learning how to run a super focused experiment where your one participant is basically their own control group, just measured carefully over time.

And to show this isn't just theoretical,

the chapter kicks off with a really neat example.

Remember the tootling intervention?

Oh yeah, in the classroom.

Instead of kids tattling, reporting bad stuff.

Right, they were taught to tootle, which meant reporting the positive things they saw classmates doing, like catching them being good.

And the researchers, they wanted to see if this whole tootling thing would actually reduce disruptive behavior in a few specific studios they were focusing on.

Exactly, and they didn't compare this class to another one, they just tracked the disruptive behavior for those individuals very closely before tootling, during, and after.

And the graphs showed it, didn't they?

A clear drop when tootling started for those kids.

That's the essence of it, that visible impact tied to the change for the individual.

So today, we'll break down the fundamental ideas, the building blocks, then look at the different design structures, and finally, weigh up when and why you'd choose this path.

Okay, so let's start right there.

What makes these single case designs unique, but still properly experimental?

The text defines them as, well, experimental designs, used with just one participant, or maybe a tiny group treated as one unit.

And the key goal is establishing that cause and effect link.

So yes, they focus on one person, which sounds a bit like a case study, but you're saying that word experimental is crucial.

What does it add?

Well, a simple case study is mostly descriptive, right?

You observe, you report what you see.

Single case designs, though, they involve active manipulation.

Ah, you're changing something on purpose.

And control.

You use specific strategies built into the design to try and rule out other reasons why the behavior might have changed.

It's not just observation.

Okay, so manipulation and control.

How do they compare to, say, time series designs?

Those also involve observations over time.

They do, but time series often just look for patterns or correlations.

They aren't always set up to prove causation in the same rigorous way.

Single case designs are structured as true experiments aiming for that causal conclusion.

Got it.

And the big comparison.

How do they stack up against traditional group designs?

Yeah.

You know, treatment group versus control group.

That's a fundamental difference in focus.

Group designs look at the average difference between groups.

You compare group A's average to group B's average.

Single case designs look within one individual.

They track changes in that person's behavior across many points in time as their conditions change.

It's intensive on the one, not extensive across the many.

Okay, that makes sense.

So even with just one person, you still need that manipulation and control.

Manipulation is introducing or removing the treatment.

How do you get control?

This is where the design structure is everything.

Control isn't from a separate group.

It's built right into the sequence of observations and changes.

And the first piece of that structure is the baseline.

Absolutely essential.

It's your starting point,

a clear objective measurement of the behavior before you do anything.

What does the behavior look like naturally?

That's your comparison point, your control condition in a way.

Exactly.

And you don't just measure it once.

You need repeated observations,

multiple measurements during the baseline phase and during every phase after that.

Why so many?

To see the pattern.

Is the behavior stable?

Is there a consistent level or maybe a trend if the data points are bouncing all over the place randomly?

Then you can't really tell if a change later on is meaningful or just more random bouncing.

Precisely.

You need that stability.

The data points need to form a consistent level or a clear trend before you can confidently introduce a change and see if it makes a difference.

So stability first.

Then what's the other key element for control?

You mentioned replication earlier.

Right, replication.

This is huge.

You need to show that the change in behavior happens reliably when the treatment is applied, preferably more than once.

So if you introduce the treatment and see a change, that's good.

But if you can maybe remove it, see the behavior go back and then reintroduce it and see the same change again.

That's replication within the single participant.

It makes it much harder to argue the first change was just a coincidence, some random event that happened at the same time you started the treatment.

Okay, so the control comes from baseline comparison, stability within phases,

and replication of the effect across phase changes.

Now, how do you analyze this?

You said no stats.

Well, not traditional group statistics like t -tests.

The primary analysis method is visual inspection of a graph.

You literally plot the behavior data over time session by session and draw lines to show where the phases change.

So just looking at it, like a simple AB graph, baseline, then treatment.

You can plot it that way, sure.

But an AB design on its own, like the book shows in figure 14 .2, isn't strong enough to prove cause and effect.

You see a change from A to B, but you don't know why.

Could be anything really, some other factor.

Exactly, extraneous variables or just chance.

There's no replication within that simple AB structure to rule those out.

So the visual inspection needs to show more than just a change.

And it really hinges on that data stability you mentioned.

Absolutely.

If your data within a phase is unstable, just scattered randomly like in figure 14 .3C, it's almost impossible to visually determine the level or trend.

Let alone see if it changed significantly when you switched phases.

Right, stable data, whether it's a flat consistent level, figure 14 .3A, or a steady consistent trend, even if it's increasing or decreasing, figure 14 .3B gives you that clear visual baseline to compare against.

But what if you do have unstable data?

Say in your baseline, are you stuck?

No, not necessarily.

There are strategies.

Sometimes you just need to wait longer, let the person get used to being observed.

Maybe the behavior settles down.

That's a bituation.

Or you could try averaging data points.

Like instead of plotting every single observation, maybe you average the data from every two sessions or every three.

That can smooth out some of the random noise and reveal an underlying pattern, like figure 14 .4 shows.

Right, smoothing it out.

And importantly, you can try to identify and control what might be causing the instability.

The book gives that great example of the student whose disruptive behavior was inconsistent.

Oh yeah, the gym class.

Right, they figured out the behavior was lower on days when the student had gym right before the observation.

The physical activity was an uncontrolled variable messing with the pattern.

Once you know that, you can account for it.

Yeah, it makes a lot of sense.

Okay, so you've got your phases, you're aiming for stability.

Let's talk about phases and phase changes.

Okay, a phase is just a period where the conditions are the same.

You're observing the behavior under one specific condition.

Baseline A is the no treatment condition.

Right, then treatment B is when the intervention is active.

You might have modifications like B1 or a totally different treatment, C.

The letters are just labels for the different conditions.

And a phase changes when you deliberately switch conditions.

Exactly, you manipulate the independent variable,

introduce the treatment, take it away, change it.

That's the core experimental manipulation.

And the whole point is to see if the behavior pattern changes when the conditions change.

That's the logic.

Now deciding when to actually make that change, that's interesting too.

It's not always predetermined.

It depends on the data you're seeing.

Very much so.

This is where the flexibility comes in.

You generally wait until you see a clear, stable pattern in the current phase.

You need enough data points to be confident about that pattern.

How many is enough?

The book suggests a minimum of three, but usually you want more like five or six, maybe even more if the data is quite variable before you change phases.

You need that clear picture first.

What if during baseline, the behavior is already getting better on its own?

Then the text advises, you probably shouldn't introduce the treatment yet.

Clinically, maybe it's not needed.

Experimentally, you couldn't separate the treatment effect from the improvement that was already happening.

That makes sense.

What about safety?

If the baseline behavior is dangerous?

Ethics overrides everything there.

You'd intervene immediately.

You wouldn't wait for a stable baseline if someone is harming themselves or others.

Or if the treatment itself seems to be making things worse.

Same thing.

You'd change or stop it right away.

It highlights how these designs are often used in real world settings where the participant's wellbeing is paramount.

Okay, so you've got stable data, you make a phase change.

Now you're looking at the graph.

What specific things are you looking for in that visual inspection?

How do you judge if the change is convincing?

The chapter outlines four main things to look for when comparing adjacent phases.

First, is there a clear change in the average level?

Like in figure 14 .5, does the average score in phase B look distinctly different from the average in phase A?

Okay, the overall level shifts.

Second, is there an immediate change in level?

Look right at the point where the phase changes.

Is there a jump or drop between the last point of the old phase and the very first point of the new one?

Figure 14 .5 shows this too.

A quick change is more convincing.

Makes sense, what else?

Third, look for a change in trend.

As shown in figure 14 .6, maybe the baseline was flat, but the treatment phase shows a clear upward or downward slope.

Or maybe an existing trend reverses direction or slope.

So the direction or steepness of the data points changes.

Exactly.

And fourth, consider the latency of the change.

How soon after the phase change did the behavior shift?

An immediate shift, like in figure 14 .7, strongly suggests the phase change caused it.

If there's a long delay, the link is weaker.

So you're looking for these visual cues, changes in level, trend, immediacy, ideally seeing several of them together.

Right, when you see a clear, immediate, and maybe even replicated change in level and or trend, that's when visual inspection becomes powerful evidence for a treatment effect.

Okay, we've got the building blocks down.

Baseline, stability, replication,

phases,

visual inspection.

Now, how do these come together in specific designs?

Let's start with the classic, the reversal design, often called ABA.

Right, the ABAB design is maybe the most fundamental single case experimental design.

It follows that clear sequence.

A, baseline, B, treatment.

A, withdraw treatment, return to baseline.

B, reintroduce treatment.

The logic here is showing the behavior tracks the treatment.

Exactly, you're demonstrating that the behavior changes from A to B.

Then, critically, it reverts back towards the baseline level or trend when you go back to A.

So removing the treatment reverses the effect.

Hopefully, and then when you reintroduce the treatment in this second B phase, the behavior changes again in the same direction as the first time.

So the effect turns on, turns off, and turns back on again right alongside the treatment.

Precisely, that pattern change, reversal change again, is very strong evidence against coincidence.

It makes it really unlikely that some random outside event just happened to occur twice, exactly when you introduced the treatment.

Figure 14 .8A shows this with level changes, 14 .8B with trend changes.

And the tootling example fits this perfectly right.

Behavior dropped,

went back up when tootling stopped, dropped again when it restarted.

Yes, that's a classic ABA demonstration.

It sounds very convincing when it works.

But what are the catches, the limitations?

Well, the biggest one is built right into the name, reversal.

The design relies on the treatment effect being reversible.

Meaning the behavior has to actually go back towards baseline when you stop the treatment.

Right, but what if your treatment teaches a skill or permanently solves a problem?

Like if you successfully teach a child to read,

stopping the reading lessons won't make them unable to read again.

The behavior doesn't reverse.

The person is essentially cured in that respect.

Exactly, which is fantastic clinically.

But for the ABA design, it's a problem.

If the behavior doesn't revert in that second A phase, you lose the reversal part of your evidence.

You can't demonstrate that removing the treatment caused the behavior to go back.

So ABA works best for treatments with more temporary effects

or behaviors likely to revert.

Generally, yes.

Or when you're testing if a treatment is maintaining a behavior.

Now, the other tricky part you alluded to earlier,

the ethics of withdrawal.

Removing a treatment that's working.

Yeah, that's a major consideration.

If the treatment is effectively reducing harmful behavior or helping someone significantly deliberately stopping it even temporarily for the second A phase can be ethically problematic.

How do researchers justify it?

Sometimes it's argued that it's only temporary and demonstrating the effect rigorously is important for future use.

Or perhaps the withdrawal phase is seen as a test will the improvement maintain without constant intervention.

But it requires careful thought, especially balancing the research goals with the individual's well -being.

It's a key reason why other designs were developed.

Are there variations, more complex sequences?

Oh, definitely.

ABA is just the basic form.

You might see designs like ABA, baseline treatment baseline, or more complex series like ABCB or C is a different treatment.

Or maybe ABB1C where B1 is a modified version of B.

Like in that peak example with the holiday decorations that look complex.

Exactly.

Figure 14 .10, the mid -year study.

That was an ABCBC design testing different interventions.

The core principle even in complex designs like figure 14 .9A remains the same.

You need to show a clear change linked to a specific phase introduction or change.

And ideally you need to demonstrate replication of a specific treatments effect at least once like the convincing replication in figure 14 .9B to make a strong causal claim.

Okay, so reversal designs are powerful but have limits.

What if reversal isn't an option ethically or practically?

That brings us to multiple baseline designs.

Yes, these are a fantastic alternative because they establish control without needing to withdraw a treatment.

The logic shifts from reversal to staggered introduction.

Staggered introduction.

How does that work?

You start by establishing baselines for two or more different things simultaneously.

These things could be different people, different behaviors in the same person or the same behavior in different settings.

Okay, multiple baselines running at the same time.

Right.

Then the key is you introduce the treatment at different times for each baseline.

You start the treatment for baseline one while continuing to monitor the others in their baseline phase.

Then later you introduce the treatment for baseline two and so on.

Ah, so you start the intervention for person A, wait a bit, then start it for person B, wait a bit, then maybe person C.

Exactly, that's a multiple baseline across subjects design.

The college athletes texting example in figure 14 .12 is perfect, lateness dropped for each athlete.

But only after the texting intervention started for that specific athlete.

Precisely.

If some external event caused the drop, like a sudden change in team policy, you'd expect all the athletes' lateness to change around the same time.

But the fact that the change is staggered, lining up perfectly with when each athlete's individual intervention began,

provides the evidence.

It rules out those coincidences.

That's clever.

So the staggered timing is the control mechanism.

It is, and you can do this not just across subjects, but also across behaviors.

For the same person.

Yes, if you have one person exhibiting several different independent problem behaviors,

you target behavior one with the treatment, wait, then target behavior two, wait, then behavior three.

If each behavior only changes after the treatment is applied specifically to it, that's your evidence.

Assuming the behaviors are genuinely independent.

That's a key assumption, yes.

And the third type is across situations or settings.

Like targeting the same behavior at home, then later at school.

Correct.

You start the intervention in one setting while monitoring the other, then introduce it in the second setting later, again, looking for that staggered effect.

So the big strength here is definitely avoiding reversal.

Great for permanent changes or sensitive situations.

Absolutely.

What are the potential downsides or weaknesses?

Well, as you hinted, with the across behaviors design, you need those behaviors to be truly independent.

If treating behavior one somehow causes behavior two to improve before you target it.

The treatment effect kind of generalized or spilled over.

Right, and that weakens the staggered logic.

You need the baselines to remain stable until the intervention is directly applied.

Makes sense.

Any other issues?

Like reversal designs, they rely on clear visual patterns.

If there's a lot of variability within each baseline, or if the different baselines themselves are very different from each other in level or trend.

It can make the visual interpretation harder.

Exactly.

The math highlighting example in figure 14 .1 team shows this well.

Two participants showed clear effects, but the third had a very unstable baseline, making their results much less convincing.

Inconsistency across the baselines can weaken the overall conclusion.

So powerful, flexible, avoids reversal, but still needs careful selection of baselines and relies on clear data patterns.

That sums it up well.

Okay, one more design type mentioned.

Component analysis designs.

What's the specific job of these?

These are used when you have an intervention that's actually a package of different parts, and you want to figure out which parts are really doing the heavy lifting.

So disentangling a complex treatment,

trying to find the active ingredients.

Precisely.

Is it the whole package or just one or two key elements?

You might start with the full treatment and systematically take away components one by one in different phases, seeing if effectiveness drops.

Or you could build it up.

Yes, you could start with baseline and add components incrementally phase by phase, seeing which addition produces the desired change.

Can you use the logic of reversal or multiple baseline for this?

You can structure it either way.

You might add and remove components in a sequence, like a reversal, or you might introduce components in a staggered way across different participants or behaviors using a multiple baseline framework.

Is there an example in the text?

Yes, the toilet training study by Greer and colleagues, figure 14 .13.

They used a multiple baseline across participants, but within that structure, they were testing different components,

like using cotton underwear, having scheduled dense sitting on the toilet, using differential reinforcement.

By varying when these were introduced for different kids, they could analyze the contribution of each component to successful training.

Wow, okay, so that lets you really refine treatments and understand why they work.

It's incredibly useful for optimizing interventions.

Moving beyond just does it work to what part of it works best?

Hmm, we've covered a huge amount of ground here, the basic ideas, the controls, visual analysis and the main designs, ADA, multiple baseline component analysis.

Let's try and zoom out now.

What's the big picture comparison?

Single case versus group designs.

The text points out three really fundamental differences.

Right, first, obviously the number of participants, one or a few versus many.

Second, flexibility.

Yeah, single case designs can be really adaptive.

You can change things based on how the individual is responding in real time.

Group designs have to be standardized and stick to the plan once they start.

And third?

Continuous assessment.

Single case involves tons of observations over time for that one person, giving a really detailed picture.

Group designs often just measure people once or twice, maybe pre and post treatment.

Okay, so given those core differences, what are the main advantages of choosing a single case approach?

Well, the headline advantage is establishing cause and effect with a single participant.

That's huge.

It makes research highly compatible with clinical practice.

You can actually do research while treating someone.

Exactly, a practitioner can use these methods to see if what they're doing is actually working for that specific client, bringing empirical evidence right into the session essentially.

It provides a kind of accountability then.

Yes, for the clinician.

And the flexibility is a major practical advantage.

You can tweak the intervention if it's not working or if something unexpected happens without invalidating the study.

Which allows for much more individualized treatment.

Definitely, you're tailoring it to the person, not forcing everyone into the same box.

So you get the rich detail of the case study, but with the experimental rigor to actually infer causality.

Bridging science and practice at the individual level.

That's the goal.

All right, but no method is perfect.

What are the main disadvantages or limitations?

The biggest, most often cited limitation is external validity,

generalizability.

Meaning, just because it works for this one person, how do we know it will work for others?

Exactly, the results might be very specific to that individual and their unique circumstances.

Now, the text notes this is often mitigated because single case studies don't usually exist in a vacuum.

Right, there might be other research, maybe group studies or theory, suggesting the intervention should work more broadly.

Yes, the single case study provides strong evidence of internal validity proof it worked for that person.

And you look to other sources to support the external validity, the generalizability.

Replication across multiple single case studies with different individuals also helps build external validity.

Okay, so external validity is a caution.

What else?

There can be threats to internal validity too, ironically.

Just the act of continuous observation could cause reactivity.

The person might change their behavior just because they know they're being watched so closely, not because of the treatment itself.

The measurement affects the measured.

Potentially.

And then there's the reliance on visual inspection, the absence of statistical controls.

Which means interpretation can be subjective.

It can be.

Two people might look at the same graph and disagree about whether the change is convincing enough, especially if the effects aren't massive or the data has some noise.

And because you need those visually obvious effects, you might miss smaller, but potentially still real treatment effects that a statistical analysis in a large group study might pick up.

That's true.

Single case designs are inherently biased towards detecting practical significance effects that are large enough to be obvious and meaningful in a real world sense.

They might overlook effects that are statistically significant, but perhaps too small to matter clinically or educationally.

So it's a trade -off.

You get strong evidence for clear practical effects at the individual level, but maybe less sensitivity to subtle effects and questions about generalizability that need other evidence.

That's a good way to put it.

You get rigor, individual focus, clinical relevance and flexibility, but you trade off statistical power for detecting small effects and easy generalizability.

It sounds like an incredibly valuable set of tools though, especially in fields like applied behavior analysis, special education, clinical psychology, anywhere focused on changing individual behavior.

Absolutely vital in those areas.

Okay, so we've really done a deep dive into chapter 14.

We look at the challenge of single subject cause and effect, the building blocks like baseline, stability, replication, visual inspection.

We explored ABM reversals, the different multiple baseline designs, component analysis, and weigh the overall pros and cons against group designs.

It's clear how these methods provide a rigorous way to study intervention effects at the individual level.

It really is a complete framework for understanding change one person at a time.

So here's something to think about as we wrap up.

We all kind of do informal single case experiments in our own lives, right?

You notice a pattern in your own habits or maybe in someone else's behavior.

You try changing something, your routine, how you respond to them, and you watch to see what happens.

Yeah, we're constantly observing and adjusting based on perceived cause and effect.

So think about that.

How much of what you conclude in your daily life is based on just one observation, like a simple AB,

versus seeing a consistent pattern over time, or maybe even seeing something change back when you stop doing whatever you tried?

After hearing about these designs, what stands out to you about how we determine cause and effect for individuals?