Autore della sezione: Danielle J. Navarro and David R. Foxcroft
Confounders, artefacts and other threats to validity
If we look at the issue of validity in the most general fashion the two biggest worries that we have are confounders and artefacts. These two terms are defined in the following way:
Confounder: A confounder is an additional, often unmeasured variable[1] that turns out to be related to both the predictors and the outcome. The existence of confounders threatens the internal validity of the study because you can not tell whether the predictor causes the outcome, or if the confounding variable causes it.
Artefact: A result is said to be “artefactual” if it only holds in the special situation that you happened to test in your study. The possibility that your result is an artefact poses a threat to your external validity, because it raises the possibility that you can not generalise or apply your results to the actual population that you care about.
As a general rule confounders are a bigger concern for non-experimental studies, precisely because they are not proper experiments. By definition, you are leaving lots of things uncontrolled, so there is a lot of scope for confounders being present in your study. Experimental research tends to be much less vulnerable to confounders. The more control you have over what happens during the study, the more you can prevent confounders from affecting the results. With random allocation, for example, confounders are distributed randomly, and evenly, between different groups.
However, there are always swings and roundabouts and when we start thinking about artefacts rather than confounders the shoe is very firmly on the other foot. For the most part, artefactual results tend to be more of a concern for experimental studies than for non-experimental studies. To see this, it helps to realise that the reason that a lot of studies are non-experimental is precisely because what the researcher is trying to do is examine human behaviour in a more naturalistic context. By working in a more real-world context you lose experimental control (making yourself vulnerable to confounders), but because you tend to be studying human psychology “in the wild” you reduce the chances of getting an artefactual result. Or, to put it another way, when you take psychology out of the wild and bring it into the lab (which we usually have to do to gain our experimental control), you always run the risk of accidentally studying something different to what you wanted to study.
Be warned though. The above is a rough guide only. It is absolutely possible to have confounders in an experiment, and to get artefactual results with non-experimental studies. This can happen for all sorts of reasons, not least of which is experimenter or researcher error. In practice, it is really hard to think everything through ahead of time and even very good researchers make mistakes.
Although there is a sense in which almost any threat to validity can be characterised as a confounder or an artefact, they are pretty vague concepts. So let us have a look at some of the most common examples.
History effects
History effects refer to the possibility that specific events may occur during the study that might influence the outcome measure. For instance, something might happen in between a pre-test and a post-test. Or in-between testing participant 23 and participant 24. Alternatively, it might be that you are looking at a paper from an older study that was perfectly valid for its time, but the world has changed enough since then that the conclusions are no longer trustworthy. Examples of things that would count as history effects are:
You are interested in how people think about risk and uncertainty. You started your data collection in December 2010. But finding participants and collecting data takes time, so you are still finding new people in February 2011. Unfortunately for you (and even more unfortunately for others), the Queensland floods occurred in January 2011 causing billions of dollars of damage and killing many people. Not surprisingly, the people tested in February 2011 express quite different beliefs about handling risk than the people tested in December 2010. Which (if any) of these reflects the “true” beliefs of participants? I think the answer is probably both. The Queensland floods genuinely changed the beliefs of the Australian public, though possibly only temporarily. The key thing here is that the “history” of the people tested in February is quite different to people tested in December.
You are testing the psychological effects of a new anti-anxiety drug. So what you do is measure anxiety before administering the drug (e.g., by self-report, and taking physiological measures). Then you administer the drug, and afterwards you take the same measures. In the interim however, because your lab is in Los Angeles, there is an earthquake which increases the anxiety of the participants.
Maturation effects
As with history effects, maturational effects are fundamentally about change over time. However, maturation effects are not in response to specific events. Rather, they relate to how people change on their own over time. We get older, we get tired, we get bored, etc. Some examples of maturation effects are:
When doing developmental psychology research you need to be aware that children grow up quite rapidly. So, suppose that you want to find out whether some educational trick helps with vocabulary size among 3-year-olds. One thing that you need to be aware of is that the vocabulary size of children that age is growing at an incredible rate (multiple words per day) all on its own. If you design your study without taking this maturational effect into account, then you will not be able to tell if your educational trick works.
When running a very long experiment in the lab (say, something that lasts for three hours) it is very likely that people will begin to get bored and tired, and that this maturational effect will cause performance to decline regardless of anything else going on in the experiment
Repeated testing effects
An important type of history effect is the effect of repeated testing. Suppose I want to take two measurements of some psychological construct (e.g., anxiety). One thing I might be worried about is if the first measurement has an effect on the second measurement. In other words, this is a history effect in which the “event” that influences the second measurement is the first measurement itself! This is not at all uncommon. Examples of this include:
Learning and practice: e.g., “intelligence” at time 2 might appear to go up relative to time 1 because participants learned the general rules of how to solve “intelligence-test-style” questions during the first testing session.
Familiarity with the testing situation: e.g., if people are nervous at time 1, this might make performance go down. But after sitting through the first testing situation they might calm down a lot precisely because they have seen what the testing looks like.
Auxiliary changes caused by testing: e.g., if a questionnaire assessing mood is boring then mood rating at measurement time 2 is more likely to be “bored” precisely because of the boring measurement made at time 1.
Selection bias
Selection bias is a pretty broad term. Suppose that you are running an experiment with two groups of participants where each group gets a different “treatment”, and you want to see if the different treatments lead to different outcomes. However, suppose that, despite your best efforts, you have ended up with a gender imbalance across groups (say, group A has 80% females and group B has 50% females). It might sound like this could never happen but, trust me, it can. This is an example of a selection bias, in which the people “selected into” the two groups have different characteristics. If any of those characteristics turns out to be relevant (say, your treatment works better on females than males) then you are in a lot of trouble.
Differential attrition
When thinking about the effects of attrition, it is sometimes helpful to distinguish between two different types. The first is homogeneous attrition, in which the attrition effect is the same for all groups, treatments or conditions. In the example I gave above, the attrition would be homogeneous if (and only if) the easily bored participants are dropping out of all of the conditions in my experiment at about the same rate. In general, the main effect of homogeneous attrition is likely to be that it makes your sample unrepresentative. As such, the biggest worry that you will have is that the generalisability of the results decreases. In other words, you lose external validity.
The second type of attrition is heterogeneous attrition, in which the attrition effect is different for different groups. More often called differential attrition, this is a kind of selection bias that is caused by the study itself. Suppose that, for the first time ever in the history of psychology, I manage to find the perfectly balanced and representative sample of people. I start running “Danielle’s incredibly long and tedious experiment” on my perfect sample but then, because my study is incredibly long and tedious, lots of people start dropping out. I can not stop this. Participants absolutely have the right to stop doing any experiment, any time, for whatever reason they feel like, and as researchers we are morally (and professionally) obliged to remind people that they do have this right. So, suppose that “Danielle’s incredibly long and tedious experiment” has a very high drop out rate. What do you suppose the odds are that this drop out is random? Answer: zero. Almost certainly the people who remain are more conscientious, more tolerant of boredom, etc., than those who leave. To the extent that (say) conscientiousness is relevant to the psychological phenomenon that I care about, this attrition can decrease the validity of my results.
Here is another example. Suppose I design my experiment with two conditions. In the “treatment” condition, the experimenter insults the participant and then gives them a questionnaire designed to measure obedience. In the “control” condition, the experimenter engages in a bit of pointless chitchat and then gives them the questionnaire. Leaving aside the questionable scientific merits and dubious ethics of such a study, let us have a think about what might go wrong here. As a general rule, when someone insults me to my face I tend to get much less co-operative. So, there is a pretty good chance that a lot more people are going to drop out of the treatment condition than the control condition. And this drop out is not going to be random. The people most likely to drop out would probably be the people who do not care all that much about the importance of obediently sitting through the experiment. Since the most bloody minded and disobedient people all left the treatment group but not the control group, we have introduced a confounder: the people who actually took the questionnaire in the treatment group were already more likely to be dutiful and obedient than the people in the control group. In short, in this study insulting people does not make them more obedient. It makes the more disobedient people leave the experiment! The internal validity of this experiment is completely shot.
Non-response bias
Non-response bias is closely related to selection bias and to differential attrition. The simplest version of the problem goes like this. You mail out a survey to 1000 people but only 300 of them reply. The 300 people who replied are almost certainly not a random subsample. People who respond to surveys are systematically different to people who do not. This introduces a problem when trying to generalise from those 300 people who replied to the population at large, since you now have a very non-random sample. The issue of non-response bias is more general than this, though. Among the (say) 300 people that did respond to the survey, you might find that not everyone answers every question. If (say) 80 people chose not to answer one of your questions, does this introduce problems? As always, the answer is maybe. If the question that was not answered was on the last page of the questionnaire, and those 80 surveys were returned with the last page missing, there is a good chance that the missing data is not a big deal; probably the pages just fell off. However, if the question that 80 people did not answer was the most confrontational or invasive personal question in the questionnaire, then almost certainly you have got a problem. In essence, what you are dealing with here is what is called the problem of missing data. If the data that is missing was “lost” randomly, then it is not a big problem. If it is missing systematically, then it can be a big problem.
Regression to the mean
Regression to the mean refers to any situation where you select data based on an extreme value on some measure. Because the variable has natural variation it almost certainly means that when you take a subsequent measurement the later measurement will be less extreme than the first one, purely by chance.
Here is an example. Suppose I am interested in whether a psychology education has an adverse effect on very smart kids. To do this, I find the 20 psychology I students with the best high school grades and look at how well they are doing at university. It turns out that they are doing a lot better than average, but they are not topping the class at university even though they did top their classes at high school. What is going on? The natural first thought is that this must mean that the psychology classes must be having an adverse effect on those students. However, while that might very well be the explanation, it is more likely that what you are seeing is an example of “regression to the mean”. To see how it works, let us take a moment to think about what is required to get the best mark in a class, regardless of whether that class be at high school or at university. When you have got a big class there are going to be lots of very smart people enrolled. To get the best mark you have to be very smart, work very hard, and be a bit lucky. The exam has to ask just the right questions for your idiosyncratic skills, and you have to avoid making any dumb mistakes (we all do that sometimes) when answering them. And that is the thing, whilst intelligence and hard work are transferable from one class to the next, luck is not. The people who got lucky in high school will not be the same as the people who get lucky at university. That is the very definition of “luck”. The consequence of this is that when you select people at the very extreme values of one measurement (the top 20 students), you are selecting for hard work, skill and luck. But because the luck does not transfer to the second measurement (only the skill and work), these people will all be expected to drop a little bit when you measure them a second time (at university). So their scores fall back a little bit, back towards everyone else. This is regression to the mean.
Regression to the mean is surprisingly common. For instance, if two very tall people have kids their children will tend to be taller than average but not as tall as the parents. The reverse happens with very short parents. Two very short parents will tend to have short children, but nevertheless those kids will tend to be taller than the parents. It can also be extremely subtle. For instance, there have been studies done that suggested that people learn better from negative feedback than from positive feedback. However, the way that people tried to show this was to give people positive reinforcement whenever they did good, and negative reinforcement when they did bad. And what you see is that after the positive reinforcement people tended to do worse, but after the negative reinforcement they tended to do better. But notice that there is a selection bias here! When people do very well, you are selecting for “high” values, and so you should expect, because of regression to the mean, that performance on the next trial should be worse regardless of whether reinforcement is given. Similarly, after a bad trial, people will tend to improve all on their own. The apparent superiority of negative feedback is an artefact caused by regression to the mean (see Kahneman & Tversky, 1973 for a discussion).
Experimenter bias
Experimenter bias can come in multiple forms. The basic idea is that the experimenter, despite the best of intentions, can accidentally end up influencing the results of the experiment by subtly communicating the “right answer” or the “desired behaviour” to the participants. Typically, this occurs because the experimenter has special knowledge that the participant does not, for example the right answer to the questions being asked or knowledge of the expected pattern of performance for the condition that the participant is in. The classic example of this happening is the case study of “Clever Hans”, which dates back to 1907 (Pfungst, 1911; Hothersall, 2004). Clever Hans was a horse that apparently was able to read and count and perform other human like feats of intelligence. After Clever Hans became famous, psychologists started examining his behaviour more closely. It turned out that, not surprisingly, Hans did not know how to do maths. Rather, Hans was responding to the human observers around him, because the humans did know how to count and the horse had learned to change its behaviour when people changed theirs.
The general solution to the problem of experimenter bias is to engage in double blind studies, where neither the experimenter nor the participant knows which condition the participant is in or knows what the desired behaviour is. This provides a very good solution to the problem, but it is important to recognise that it is not quite ideal, and hard to pull off perfectly. For instance, the obvious way that I could try to construct a double blind study is to have one of my Ph.D. students (one who does not know anything about the experiment) run the study. That feels like it should be enough. The only person (me) who knows all the details (e.g., correct answers to the questions, assignments of participants to conditions) has no interaction with the participants, and the person who does all the talking to people (the Ph.D. student) does not know anything. Except for the reality that the last part is very unlikely to be true. In order for the Ph.D. student to run the study effectively they need to have been briefed by me, the researcher. And, as it happens, the Ph.D. student also knows me and knows a bit about my general beliefs about people and psychology (e.g., I tend to think humans are much smarter than psychologists give them credit for). As a result of all this, it is almost impossible for the experimenter to avoid knowing a little bit about what expectations I have. And even a little bit of knowledge can have an effect. Suppose the experimenter accidentally conveys the fact that the participants are expected to do well in this task. Well, there is a thing called the “Pygmalion effect”, where if you expect great things of people they will tend to rise to the occasion. But if you expect them to fail then they will do that too. In other words, the expectations become a self-fulfilling prophecy.
Demand characteristics and reactivity
When talking about experimenter bias, the worry is that the experimenter’s knowledge or desires for the experiment are communicated to the participants, and that these can change people’s behaviour (Rosenthal, 1966). However, even if you manage to stop this from happening, it is almost impossible to stop people from knowing that they are part of a psychological study. And the mere fact of knowing that someone is watching or studying you can have a pretty big effect on behaviour. This is generally referred to as reactivity or demand characteristics. The basic idea is captured by the Hawthorne effect: people alter their performance because of the attention that the study focuses on them. The effect takes its name from a study that took place in the “Hawthorne Works” factory outside of Chicago (see Adair, 1984). This study, from the 1920s, looked at the effects of factory lighting on worker productivity. But, importantly, change in worker behaviour occurred because the workers knew they were being studied, rather than any effect of factory lighting.
To get a bit more specific about some of the ways in which the mere fact of being in a study can change how people behave, it helps to think like a social psychologist and look at some of the roles that people might adopt during an experiment but might not adopt if the corresponding events were occurring in the real world:
The good participant tries to be too helpful to the researcher. He or she seeks to figure out the experimenter’s hypotheses and confirm them.
The negative participant does the exact opposite of the good participant. He or she seeks to break or destroy the study or the hypothesis in some way.
The faithful participant is unnaturally obedient. He or she seeks to follow instructions perfectly, regardless of what might have happened in a more realistic setting.
The apprehensive participant gets nervous about being tested or studied, so much so that his or her behaviour becomes highly unnatural, or overly socially desirable.
Placebo effects
The placebo effect is a specific type of demand characteristic that we worry a lot about. It refers to the situation where the mere fact of being treated causes an improvement in outcomes. The classic example comes from clinical trials. If you give people a completely chemically inert drug and tell them that it is a cure for a disease, they will tend to get better faster than people who are not treated at all. In other words, it is people’s belief that they are being treated that causes the improved outcomes, not the drug.
However, the current consensus in medicine is that true placebo effects are quite rare and most of what was previously considered placebo effect is in fact some combination of natural healing (some people just get better on their own), regression to the mean and other quirks of study design. Of interest to psychology is that the strongest evidence for at least some placebo effect is in self-reported outcomes, most notably in treatment of pain (Hróbjartsson & Gøtzsche, 2010).
Situation, measurement and sub-population effects
In some respects, these terms are a catch-all term for “all other threats to external validity”. They refer to the fact that the choice of sub-population from which you draw your participants, the location, timing and manner in which you run your study (including who collects the data) and the tools that you use to make your measurements might all be influencing the results. Specifically, the worry is that these things might be influencing the results in such a way that the results will not generalise to a wider array of people, places and measures.
Fraud, deception and self-deception
It is difficult to get a man to understand something,when his salary depends on his not understanding it.—Upton Sinclair
There is one final thing I feel I should mention. While reading what the textbooks often have to say about assessing the validity of a study I could not help but notice that they seem to make the assumption that the researcher is honest. I find this hilarious. While the vast majority of scientists are honest, in my experience at least, some are not.[2] Not only that, as I mentioned earlier, scientists are not immune to belief bias. It is easy for a researcher to end up deceiving themselves into believing the wrong thing, and this can lead them to conduct subtly flawed research and then hide those flaws when they write it up. So you need to consider not only the (probably unlikely) possibility of outright fraud, but also the (probably quite common) possibility that the research is unintentionally “slanted”. I opened a few standard textbooks and did not find much of a discussion of this problem, so here is my own attempt to list a few ways in which these issues can arise:
Data fabrication. Sometimes, people just make up the data. This is occasionally done with “good” intentions. For instance, the researcher believes that the fabricated data do reflect the truth, and may actually reflect “slightly cleaned up” versions of actual data. On other occasions, the fraud is deliberate and malicious. Some high-profile examples where data fabrication has been alleged or shown include Cyril Burt (a psychologist who is thought to have fabricated some of his data), Andrew Wakefield (who has been accused of fabricating his data connecting the MMR vaccine to autism), and Hwang Woo-suk (who falsified a lot of his data on stem cell research).
Hoaxes. Hoaxes share a lot of similarities with data fabrication, but they differ in the intended purpose. A hoax is often a joke, and many of them are intended to be (eventually) discovered. Often, the point of a hoax is to discredit someone or some field. There is quite a few well known scientific hoaxes that have occurred over the years (e.g., Piltdown man) and some were deliberate attempts to discredit particular fields of research (e.g., the Sokal affair).
Data misrepresentation. While fraud gets most of the headlines, it is much more common in my experience to see data being misrepresented. When I say this I am not referring to newspapers getting it wrong (which they do, almost always). I am referring to the fact that often the data do not actually say what the researchers think they say. My guess is that, almost always, this is not the result of deliberate dishonesty but instead is due to a lack of sophistication in the data analyses. For instance, think back to the example of Simpson’s paradox that I discussed in the beginning of this book. It is very common to see people present “aggregated” data of some kind and sometimes, when you dig deeper and find the raw data yourself you find that the aggregated data tell a different story to the disaggregated data. Alternatively, you might find that some aspect of the data is being hidden, because it tells an inconvenient story (e.g., the researcher might choose not to refer to a particular variable). There is a lot of variants on this, many of which are very hard to detect.
Study “misdesign”. Okay, this one is subtle. Basically, the issue here is that a researcher designs a study that has built-in flaws and those flaws are never reported in the paper. The data that are reported are completely real and are correctly analysed, but they are produced by a study that is actually quite wrongly put together. The researcher really wants to find a particular effect and so the study is set up in such a way as to make it “easy” to (artefactually) observe that effect. One sneaky way to do this, in case you are feeling like dabbling in a bit of fraud yourself, is to design an experiment in which it is obvious to the participants what they are “supposed” to be doing, and then let reactivity work its magic for you. If you want you can add all the trappings of double blind experimentation but it will not make a difference since the study materials themselves are subtly telling people what you want them to do. When you write up the results the fraud will not be obvious to the reader. What is obvious to the participant when they are in the experimental context is not always obvious to the person reading the paper. Of course, the way I have described this makes it sound like it is always fraud. Probably there are cases where this is done deliberately, but in my experience the bigger concern is with unintentional misdesign. The researcher believes and so the study just happens to end up with a built-in flaw, and that flaw then magically erases itself when the study is written up for publication.
Data mining and post-hoc hypothesising. Another way in which the authors of a study can more or less misrepresent the data is by engaging in what is referred to as “data mining” (see Gelman & Loken, 2014, for a broader discussion of this as part of the “garden of forking paths” in statistical analysis). As we will discuss later, if you keep trying to analyse your data in lots of different ways, you will eventually find something that “looks” like a real effect but is not. This is referred to as “data mining”. It used to be quite rare because data analysis used to take weeks, but now that everyone has very powerful statistical software on their computers it is becoming very common. Data mining per se is not “wrong”, but the more that you do it the bigger the risk you are taking. The thing that is wrong, and I suspect is very common, is unacknowledged data mining. That is, the researcher runs every possible analysis known to humanity, finds the one that works, and then pretends that this was the only analysis that they ever conducted. Worse yet, they often “invent” a hypothesis after looking at the data to cover up the data mining. To be clear. It is not wrong to change your beliefs after looking at the data, and to reanalyse your data using your new “post-hoc” hypotheses. What is wrong (and I suspect common) is failing to acknowledge what you have done. If you acknowledge that you did it then other researchers are able to take your behaviour into account. If you do not, then they can not. And that makes your behaviour deceptive.
Publication bias and self-censoring. Finally, a pervasive bias is “non-reporting” of negative results. This is almost impossible to prevent. Journals do not publish every article that is submitted to them. They prefer to publish articles that find “something”. So, if 20 people run an experiment looking at whether reading Finnegans Wake causes insanity in humans, and 19 of them find that it does not, which one do you think is going to get published? Obviously, it is the one study that did find that Finnegans Wake causes insanity.[3] This is an example of a publication bias. Since no-one ever published the 19 studies that did not find an effect, a naive reader would never know that they existed. Worse yet, most researchers “internalise” this bias and end up self-censoring their research. Knowing that negative results are not going to be accepted for publication, they never even try to report them. As a friend of mine says “for every experiment that you get published, you also have 10 failures”. And she is right. The catch is, while some (maybe most) of those studies are failures for boring reasons (e.g., you stuffed something up) others might be genuine “null” results that you ought to acknowledge when you write up the “good” experiment. And telling which is which is often hard to do. A good place to start is a paper by Ioannidis (2005) with the depressing title “Why most published research findings are false”. I would also suggest taking a look at work by Kühberger et al. (2014) presenting statistical evidence that this actually happens in psychology.
There is probably a lot more issues like this to think about, but that will do to start with. What I really want to point out is the blindingly obvious truth that real-world science is conducted by actual humans, and only the most gullible of people automatically assume that everyone else is honest and impartial. Actual scientists are not usually that naive, but for some reason the world likes to pretend that we are, and the textbooks we usually write seem to reinforce that stereotype.