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001-experiments.qmd
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{{< include _setup.qmd >}}
# Experiments {#sec-experiments}
::: {.callout-note title="learning goals"}
* Define what an experiment is
* Contrast observational and experimental studies using causal graphs
* Understand the role of randomization in experiments
* Consider constraints on the generalizability of experiments
:::
Welcome to *Experimentology*! This book is about the art of running psychology experiments. Throughout, a simple idea will guide us:
> The purpose of experiments is to estimate the magnitude of causal effects.^[Perhaps you're already saying, "That's not what I thought experiments were for! I thought they were for testing hypotheses." Bear with us and we hope we'll convince you that our definition is a bit more general, and that testing a hypothesis is one thing you can do with a measurement.]
Starting from our core idea, we'll provide advice about how to navigate things like experimental design, measurement, sampling, and more. Our decisions about each of these will determine how precise our estimate is, and whether it is subject to bias. But before we get to those topics, let's start by thinking about *why* we might do an experiment, a topic that will intersect with our key themes of [bias reduction]{.smallcaps} and [generalizability]{.smallcaps}.
## Observational studies don't reveal causality
If you're reading this book, there's probably something about psychology you want to understand. How is language learned? How is it that we experience emotions like happiness and sadness? Why do humans sometimes work together and other times destroy one another? When psychologists study these centuries-old questions, they often transform them into questions about **causality**\indexC{causality}.^[Defining causality is one of the trickiest and oldest problems in philosophy, and we won't attempt to solve it here! But from a psychological perspective, we're fond of Lewis's [-@lewis1973] "counterfactual" analysis of causality. On this view, we can understand the claim that *money causes happiness* by considering a scenario where if people *hadn't* been given more money, they *wouldn't* have experienced an increase in happiness.]
### Describing causal relationships
Consider the age-old question: Does money make people happy? This question is---at its heart---a question about what interventions on the world we can make. Can I get more money and make myself happier? Can I *cause* happiness with money?
How could we test our hypothesized effect of money on happiness? Intuitively, many people think of running an **observational study**. We might survey people about how much money they make and how happy they are. The result of this study would be a pair of measurements for each participant: `[money, happiness]`.
Now, imagine your observational study found that money and happiness were related---statistically **correlated** with each another: people with more money tended to be happier. Can we conclude that money causes happiness? Not necessarily. The presence of a correlation does not mean that there is a causal relationship!
{#fig-experiments-money1 .column-margin fig-alt="A directed acyclic graph (DAG) with an arrow from money to happiness."}
Let's get a bit more precise about our causal hypothesis. To illustrate causal relationships, we use a tool called **directed acyclic graphs** [DAGs, @pearl1998]\indexC{directed acyclic graph (DAG)}. [Figure @fig-experiments-money1] shows an example DAG for money and happiness. The arrow represents our idea about the potential causal link between two variables: money and happiness.^[In this chapter, we're going to use the term "variables" without discussing why we study some variables and not others. In the next chapter, we'll introduce the term "construct," which indicates a psychological entity that we want to theorize about.] The direction of the arrow tells us which way we hypothesize that the causal relationship goes.
The correlation between money and happiness we saw in our observational study is consistent with the causal model in @fig-experiments-money1; however, it is also consistent with several alternative causal models, which we will illustrate with DAGs\indexC{directed acyclic graph (DAG)} below.
### The problems of directionality and confounding
{#fig-experiments-money2 .column-margin fig-alt="3 DAGs: 1. same as 1.1; 2. arrow from happiness to money; 3. arrows from friends to money and to happiness."}
@Fig-experiments-money2 uses DAGs\indexC{directed acyclic graph (DAG)} to illustrate several causal models that are consistent with the observed correlation between money and happiness. DAG 1 represents our hypothesized relationship---money causes people to be happy. But DAG 2 shows an effect in completely the opposite direction! In this DAG, being happy causes people to make more money.
Even more puzzling, there could be a correlation but no causal relationship between money and happiness in either direction. Instead, a third variable---often referred to as a **confound**---may be causing increases in both money and happiness. For example, maybe having more friends causes people to both be happier and make more money (DAG 3)\indexC{directed acyclic graph (DAG)}. In this scenario, happiness and money would be correlated even though one does not cause the other.
A confound (or several) may entirely explain the relationship between two variables (as in DAG 3)\indexC{directed acyclic graph (DAG)}, but it can also just *partly* explain the relationship. For example, it could be that money does increase happiness, but the causal effect is rather small, and only accounts for a small portion of the observed correlation between them, with the friendship confound (and perhaps others) accounting for the remainder.
In this case, because of the confounds, we say that the observed correlation between money and happiness is a **biased** estimate of the causal effect of money on happiness. The amount of bias introduced by the confounds can vary in different scenarios---it may only be small or it may be so strong that we conclude there's a causal relationship between two variables when there isn't one at all. The state of affairs summarized in @fig-experiments-money2 is why we say "correlation doesn't imply causation." A correlation between two variables *is consistent with* a causal relationship between them, but it's also consistent with other relationships.^[People sometimes ask whether *causation implies correlation* (the opposite direction). The short answer is "also no." A causal relationship between two variables often means that they will be correlated in the data, but not always. For example, imagine you measured the speed of a car and the pressure on the gas pedal / accelerator. In general, pressure and speed will be correlated, consistent with the causal relationship between the two. But now imagine you only measured these two variables when someone was driving the car up a hill---now the speed would be constant, but the pressure might be increasing, reflecting the driver's attempts to keep their speed up. So there would be no correlation between the two variables in that dataset, despite the continued causal relationship.]
You can still learn about causal relationships from observational studies, but you have to take a more sophisticated approach. You can't just measure correlations and leap to causal conclusions. The "causal revolution" in the social sciences has been fueled by the development of statistical methods for reasoning about causal relationships from observational datasets.^[In fact, DAGs\indexC{directed acyclic graph (DAG)} are one of the key tools that social scientists use to reason about causal relationships. DAGs guide the creation of statistical models to estimate particular causal effects from observational data. We won't talk about these methods here, but if you're interested, check out the suggested readings at the end of this chapter.] As interesting as these methods are, however, they are only applicable in certain specific circumstances. In contrast, the experimental method *always* works to reduce bias due to confounding (though of course there are certain experiments that we can't do for ethical or practical reasons).
## Experiments help us answer causal questions
Imagine that you (a) created an exact replica of our world, (b) gave \$1,000 to everybody in the replica world, and then (c) found a few years later that everyone in the replica world was happier than their matched self in the original world. This experiment would provide strong evidence that money makes people happier. Let's think through why.
Consider a particular person---if they are happier in the replica that in the original world, what could explain that difference? Since we have replicated the world exactly but made only one change---money---then that change is the only factor that could explain the difference in happiness. We can say that we *held all variables constant* except for money, which we **manipulated** experimentally, observing its effect on some **measure**---happiness. This idea---holding all variables constant except for the specific experimental manipulation---is the basic logic that underpins the experimental method [as articulated by @mill1869].^[Another way to reason about why we can infer causality\indexC{causality} here follows the counterfactual logic we described in an earlier footnote. If the definition of causality is counterfactual ("What would have happened if the cause had been different?"), then this experiment fulfills that definition. In our impossible experiment, we can literally *see* the counterfactual: if the person had \$1,000 more, here's how much happier they would be!]
Let's think back to our observational study of money and happiness. One big causal inference problem was the presence of "third-variable" confounds like having more friends. More friends could cause you to have more money and also cause you to be happier. The idea of an experiment is to hold everything else constant---including the number of friends that people have---so we can measure the effect of money on happiness. By holding the number of friends constant, we would be severing the causal links between friends and both money and happiness. This move is graphically conveyed in @fig-experiments-money3, where we "snip away" the friend confound.
{#fig-experiments-money3 .column-margin fig-alt="A DAG with scissored arrows from friends to money and to happiness, experimental intervention arrow from money to happiness."}
### We can't hold people constant
This all sounds great in theory, you might be thinking, but we can't actually create replica worlds where everything is held constant, so how do we run experiments in the real world? If we were talking about experiments on baking cakes, it's easy to see how we could hold all of the ingredients constant and just vary one thing, like baking temperature. Doing so would allow us to conduct an experimental test of the effect of baking temperature. But how can we "hold something constant" when we're talking about people? People aren't cakes. No two people are alike, and, as every parent with multiple children knows, even if you try to "hold the ingredients constant," they don't come out the same!
If we take two people and give one money, we're comparing two *different* people, not two instances of the same person with everything held constant. It wouldn't work to *make* the first person have more or fewer friends so they match the second person---that's not holding anything constant; instead it's another (big, difficult, and potentially unethical) intervention that might itself cause lots of effects on happiness.
You may be wondering: Why don't we just ask people how many friends they have and use this information to split them into equal groups? You could do that, but this kind of strategy only allows you to control for the confounds you know of. For example, you may split people equally based on their number of friends but not their educational attainment. If educational attainment also impacts both money and happiness, you still have a confound. You may then try to split people by both their number of friends and their education. But perhaps there's another confound you've missed: sleep quality! Similarly, it also doesn't work to select people who have the same number of friends---that only holds the friends variable constant and not everything *else* that's different between the two people. So what do we do instead?^[Many researchers who have seen regression models used in the social sciences assume that "controlling for lots of stuff" is a good way to improve causal inference. Not so! In fact, inappropriately controlling for a variable in the absence of a clear causal justification can actually make your effect estimate *more* biased [@wysocki2022].]
### Randomization saves the day
{#fig-experiments-money4 .column-margin fig-alt="The same DAG as 1.3 with additional scissored arrows from education to money and education to happiness."}
The answer is **randomization**. If you randomly split a large roomful of people into two groups, the groups will, on average, have a similar number of friends. Similarly, if you randomly pick who in your experiment gets to receive money, you will find that the money and no-money groups, on average, have a similar number of friends. In other words, through randomization, the confounding role of friends is controlled. But the most important thing is that it's not *just* the role of friends that's controlled; educational attainment, sleep quality, and all the other confounds are controlled as well. If you randomly split a large group of people into groups, the groups will, on average, be equal in every way (@fig-experiments-money4).
So, here's our simple experimental design: we randomly assign some people to a money group and some people to a no-money control group (we sometimes call these groups **conditions**\indexC{control condition}). Then we measure the happiness of people in both groups. The basic logic of randomization is that, if money causes happiness, we should see more happiness---on average---in the money group.^[You may already be protesting that this experiment could be done better. Maybe we could measure happiness before and after randomization, to increase precision. Maybe we need to give a small amount of money to participants in the control condition to make sure that participants in both conditions interact with an experimenter, and hence, that the conditions are as similar as possible. We agree! These are important parts of experimental design, and we'll touch on them in subsequent chapters.]
Randomization is a powerful tool, but there is a caveat: it doesn't work every time. *On average*, randomization will ensure that your money and no-money groups will be equal with respect to confounds like number of friends, educational attainment, and sleep quality. But just as you can flip a coin and sometimes get heads nine out of ten times, sometimes you use randomization and still get more highly educated people in one condition than the other. When you randomize, you guarantee that, on average, all confounds are controlled. Hence, there is no systematic bias in your estimate from these confounds. But there will still be some noise from random variation.
In sum, randomization is a remarkably simple and effective way of holding everything constant besides a manipulated variable. In doing so, randomization allows experimental psychologists to make unbiased estimates of causal relationships. Importantly, randomization works both when you do have control of every aspect of the experiment---like when you are baking a cake---and even when you don't---like when you are doing experiments with people.^[There's an important caveat to this discussion: you don't always have to randomize *people*. You can use an experimental design called a **within-participants** design\indexC{experimental design!within-participants}, in which the same people are in multiple conditions. This type of design has a different set of unknown confounds, this time centering around *time*. So, to get around them, you have to randomize the order in which your manipulation is delivered. This randomization works very well for some kinds of manipulations but not so well for others. We'll talk more about these kinds of designs in @sec-design.]
\clearpage
::: {.callout-note title="depth"}
### Unhappy randomization? {-}
As we've been discussing, random assignment removes confounding by ensuring that---on average---groups are equivalent with respect to all of their characteristics. Equivalence for any *particular* random assignment is more likely the larger your sample is, however. Any individual experiment may be affected by **unhappy randomization**\indexC{unhappy randomization}, when a particular confound is unbalanced between groups by chance.
Unhappy randomization\indexC{unhappy randomization} is much more common in small experiments than larger ones. To see why, we use a technique called **simulation**. In simulations, we invent data randomly following a set of assumptions: we make up a group of participants and generate their characteristics and their condition assignments. By varying the assumptions we use, we can investigate how particular choices might change the structure of the data.
To look at unhappy randomization,\indexC{unhappy randomization} we created many simulated versions of our money-happiness experiment, in which an experimental group receives money and the control group receives none, and then happiness is measured for both groups. We assume that each participant has a set number of friends, and that the more friends they have, the happier they are. So, when we randomly assign them to experimental and control groups, we run the risk of unhappy randomization---sometimes one group will have substantially more friends than the other.
```{r experiments-randomization}
#| output: false
#| fig-width: 5.5
#| fig-height: 4.5
set.seed(40)
n_sims <- 100
happiness_data <- expand_grid(n_per_group = c(1, 3,10,30,100,300,1000,3000),
sim_num = 1:n_sims) |>
rowwise() |>
mutate(condition = list(c(rep("experimental", n_per_group),
rep("control", n_per_group))),
friends = list(rpois(n_per_group * 2, 5)),
happiness = list(rnorm(n_per_group * 2) + .3 * friends +
as.numeric(as.factor(condition)))) |>
unnest(cols = c(condition, friends, happiness)) |>
group_by(n_per_group, sim_num, condition) |>
summarise(happiness = mean(happiness),
friends = mean(friends)) |>
summarise(effect = diff(happiness),
friend_asym = friends[1]/friends[2])
ggplot(happiness_data,
aes(x = n_per_group, y = effect, color = log(friend_asym))) +
geom_jitter(width = .05, size = 0.7) +
scale_x_log10() +
geom_hline(yintercept = 0, linetype = "dotted", color = pal$grey) +
geom_hline(yintercept = 1, linetype = "dashed", color = pal$grey) +
labs(x = "N per group", y = "Happiness (experimental - control)",
color = "Asymmetry in number of friends (log ratio)") +
theme(legend.position = "bottom")
```
::: {#fig-experiments-randomization}
::: {.content-visible when-format="html"}
{width=60% fig-alt="A plot with vertical cluster of points around a horizontal dashed line, which get narrow in height over the horizontal axis."}
:::
::: {.content-visible when-format="pdf"}
{width=60%}
:::
Simulated data from our money-happiness experiment. Each dot represents the measured happiness effect (vertical position) for an experiment with a set number of participants in each group (horizontal position). The dot color shows how uneven friendship is between the groups. The dashed line shows the true effect.
:::
@Fig-experiments-randomization shows the results of this simulation. Each dot is an experiment, representing one estimate of the happiness effect (how much happiness is gained for the amount of money given to the experimental group). For very small experiments (e.g., with one or three participants per group), dots are very far from the dashed line showing the true effect---meaning these estimates are extremely noisy! And the reason is unhappy randomization.\indexC{unhappy randomization} The upper and lower points are those in which one group had far more friends than the other.
There are three things to notice about this simulation. First, the noise overall goes down as the sample sizes get bigger: larger experiments yield estimates closer to the true effect. Second, the unhappy randomization\indexC{unhappy randomization} decreases dramatically as well with larger samples. Although individuals still differ just as much in large experiments, the *group* average number of friends is virtually identical for each condition in the largest groups.
Finally, although the small experiments are individually very noisy, the *average effect* across all of the small experiments is still very close to the true effect. This last point illustrates what we mean when we say that randomized experiments remove confounds. Even though friendship is still an important factor determining happiness in our simulation, the average effect across experiments is correct and each individual estimate is unbiased.
:::
## Generalizability
When we are asking questions about psychology, it's important to think about who we are trying to study. Do we want to know if money increases happiness in *all people*? In people who live in materialistic societies? In people whose basic needs are not being met? We call the group we are trying to study our **population of interest**\indexC{population of interest} and the people who actually participate in our experiment our **sample**. The process of **sampling** is then what we do to recruit people into our experiment.
Sometimes researchers sample from one population but make a claim about another (usually broader) population. For example, they may run their experiment with a particular sample of US college students but then generalize to all people (their intended population of interest).\indexC{population of interest} The mismatch of sample and population is not always a problem, but quite often causal relationships are different for different populations.
Unfortunately, psychologists pervasively assume that research on US and European samples generalizes to the rest of the world, and it often does not. To highlight this issue, @henrich2010 coined the acronym WEIRD.\indexC{WEIRD (Western, Educated, Industrialized, Rich, and Democratic)} This catchy name describes the oddness of making generalizations about all of humanity from experiments on a sample that is quite unusual because it is Western, Educated, Industrialized, Rich, and Democratic. Henrich and colleagues argue that seemingly "fundamental" psychological functions like visual perception, spatial cognition, and social reasoning all differ pervasively across populations---hence, any generalization from an effect estimated with a WEIRD subpopulation may be unwarranted.
In the early 2000s, researchers found that gratitude interventions---like writing a brief essay about something nice that somebody did for you---increased happiness in studies conducted in Western countries. Based on these findings, some psychologists believed that gratitude interventions could increase happiness in all people. But it seems they were wrong. A few years later, @layous2013culture ran a gratitude experiment in two locations: the United States and South Korea. Surprisingly, the gratitude intervention decreased happiness in the South Korean sample. The researchers attributed this negative effect to feelings of indebtedness that people in South Korea more prominently experienced when reflecting on gratitude. In this example, we would say that the findings obtained with the US sample may not **generalize** to people in South Korea.
Issues of generalizability extend to all aspects of an experiment, not just its sample. For example, even if our hypothetical cash intervention experiment resulted in gains in happiness, we might not be warranted in generalizing to different ways of providing money. Perhaps there was something special about the amount of money we gave or the way we provided it that led to the effect we observed. Without testing multiple different intervention types, we can't make a broad claim. As we'll see in @sec-models and @sec-design, this issue has consequences for both our statistical analyses and our experimental designs [@yarkoni2020].
Questions of generalizability are pervasive, but the first step is to simply acknowledge and reason about them. Perhaps all papers should have a Constraints on Generality statement, where researchers discuss whether they expect their findings to generalize across different samples, experimental stimuli, procedures, and historical and temporal features [@simons2017]. This kind of statement would at least remind researchers to be humble: experiments are a powerful tool for understanding how the world works, but there are limits to what any individual experiment can teach us.
## Anatomy of a randomized experiment
{#fig-experiments-anatomy .margin-caption width=70% fig-alt="A DAG with sample within population pointing to manipulation (experimental/control) then to measure (outcome)."}
\clearpage
Now is a good time for us to go back and consolidate the anatomy of an experiment, since this anatomy is used throughout the book. @Fig-experiments-anatomy shows a simple two-group experiment like our possible money-happiness intervention. A sample is taken from a larger population, and participants in the sample are randomly assigned to one of two conditions (the manipulation)---either the experimental condition,\indexC{experimental condition} in which money is provided, or the control condition,\indexC{control condition} in which none is given. Then an outcome measure---happiness---is recorded for each participant.
We'll have a lot more to say about all of these components in subsequent chapters. We'll discuss measures in @sec-measurement, because good measurement is the foundation of a good experiment. Then in @sec-design, we'll discuss the different kinds of experimental designs that are possible and their pros and cons. Finally, we'll cover the process of sampling in @sec-sampling.
::: {.callout-note title="accident report"}
### An experiment with very unclear causal inferences {-}
The Stanford Prison Experiment\indexC{Stanford Prison Experiment} is one of the most famous studies in the history of psychology. Participants were randomly assigned to play the role of "guards" and "prisoners" in a simulation of prison life inside the Stanford Department of Psychology building [@zimbardo1972]. Designed to run for two weeks, the simulation had to be ended after six days due to the cruelty of the participants acting as guards, who apparently engaged in a variety of dehumanizing behaviors toward the simulated prisoners. This result is widely featured in introductory psychology textbooks and is typically interpreted as showing the power of situational factors: in the right context, even undergraduate students at Stanford could quickly be convinced to act out the kind of inhumane behaviors found in the worst prisons in the world [@griggs2014].
In the years since the study was initially reported, a variety of information has surfaced that makes the causal interpretation of its situational manipulation much less clear [@le-texier2019]. Guards were informed of the objectives of the experiment and given instructions on how to achieve these objectives. The experimenters themselves suggested some harsh punishments whose later use was given as evidence for the emergence of dehumanizing behaviors. Further, both guards and prisoners were coached extensively by the experimenter throughout the study. Some participants have reported that their responses during the study were exaggerated or fabricated [@blum2018]. All of these issues substantially undermine the idea that the assignment of participants' roles (the ostensible experimental manipulation) was the sole cause of the observed behaviors.
The conduct of the study was also unethical. In addition to the question of whether such a study---with all of its risks to the participants---would be ethical at all, a number of features of the study clearly violate the guidelines that we'll learn about in @sec-ethics. Participants were prevented from exiting the study voluntarily. The guards were deceived into believing that they were research assistants, rather than participants in the study. And to top it off, the study was reported inaccurately, with reports emphasizing the organic emergence of behaviors, the immersive nature of the simulation, and the extensive documentation of the experiment. In fact, the participants were instructed extensively, the simulation was repeatedly interrupted by mundane details of the research environment, and relatively little of the experiment was captured on video and analyzed.
The Prison Experiment\indexC{Stanford Prison Experiment} is a fascinating and problematic episode in the history of psychology, but it provides very little causal evidence about the human mind.
:::
## Chapter summary: Experiments
In this chapter, we defined an experiment as a combination of a manipulation and a measure. When combined with randomization, experiments allow us to make strong causal inferences, even when we are studying people (who are hard to hold constant). Nonetheless, there are limits to the power of experiments: there are always constraints on the sample, experimental stimuli, and procedure that limit how broadly we can generalize.
\vfill
::: {.callout-note title="discussion questions"}
1. Imagine that you run a survey and find that people who spend more time playing violent video games tend to be more aggressive (i.e., that there is a positive correlation between violent video games and aggression). Following @fig-experiments-money2, list three reasons why these variables may be correlated.
2. Suppose you wanted to run an experiment testing whether playing violent video games causes increases in aggression. What would be your manipulation, and what would be your measure? How would you deal with potential confounding by variables like age?
3. Consider an experiment designed to test people's food preferences. The experimenter randomly assigns thirty US preschoolers to be served either asparagus or chicken tenders and then asks them how much they enjoyed their meal. Overall, children enjoyed the meat more; the experimenter writes a paper claiming that humans prefer meat over vegetables. List some constraints on the generalizability of this study. In light of these constraints, is this study (or some modification) worth doing at all?
4. Consider the Milgram study, another classic psychology study (and our [case study]{.smallcaps} in @sec-ethics). Does this study meet our definition of an experiment?
:::
::: {.callout-note title="readings"}
* A basic introduction to causal inference from a social science perspective: Huntington-Klein, Nick. [-@huntington2021]. *The Effect: An Introduction to Research Design and Causality.* Chapman & Hall/CRC. Available free online at <https://theeffectbook.net>.
* A slightly more advanced treatment, focusing primarily on econometrics: Cunningham, Scott. [-@cunningham2021]. *Causal Inference: The Mixtape.* Yale University Press. Available free online at <https://mixtape.scunning.com>.
:::