Section author: Danielle J. Navarro and David R. Foxcroft
Assessing the validity of a study¶
More than any other thing, a scientist wants their research to be “valid”. The conceptual idea behind validity is very simple. Can you trust the results of your study? If not, the study is invalid. However, whilst it’s easy to state, in practice it’s much harder to check validity than it is to check reliability. And in all honesty, there’s no precise, clearly agreed upon notion of what validity actually is. In fact, there are lots of different kinds of validity, each of which raises it’s own issues. And not all forms of validity are relevant to all studies. I’m going to talk about five different types of validity:
- Internal validity
- External validity
- Construct validity
- Face validity
- Ecological validity
First, a quick guide as to what matters here. (1) Internal and external validity are the most important, since they tie directly to the fundamental question of whether your study really works. (2) Construct validity asks whether you’re measuring what you think you are. (3) Face validity isn’t terribly important except insofar as you care about “appearances”. (4) Ecological validity is a special case of face validity that corresponds to a kind of appearance that you might care about a lot.
Internal validity refers to the extent to which you are able draw the correct conclusions about the causal relationships between variables. It’s called “internal” because it refers to the relationships between things “inside” the study. Let’s illustrate the concept with a simple example. Suppose you’re interested in finding out whether a university education makes you write better. To do so, you get a group of first year students, ask them to write a 1000 word essay, and count the number of spelling and grammatical errors they make. Then you find some third-year students, who obviously have had more of a university education than the first-years, and repeat the exercise. And let’s suppose it turns out that the third-year students produce fewer errors. And so you conclude that a university education improves writing skills. Right? Except that the big problem with this experiment is that the third-year students are older and they’ve had more experience with writing things. So it’s hard to know for sure what the causal relationship is. Do older people write better? Or people who have had more writing experience? Or people who have had more education? Which of the above is the true cause of the superior performance of the third-years? Age? Experience? Education? You can’t tell. This is an example of a failure of internal validity, because your study doesn’t properly tease apart the causal relationships between the different variables.
External validity relates to the generalisability or applicability of your findings. That is, to what extent do you expect to see the same pattern of results in “real life” as you saw in your study. To put it a bit more precisely, any study that you do in psychology will involve a fairly specific set of questions or tasks, will occur in a specific environment, and will involve participants that are drawn from a particular subgroup (disappointingly often it is college students!). So, if it turns out that the results don’t actually generalise or apply to people and situations beyond the ones that you studied, then what you’ve got is a lack of external validity.
The classic example of this issue is the fact that a very large proportion of studies in psychology will use undergraduate psychology students as the participants. Obviously, however, the researchers don’t care only about psychology students. They care about people in general. Given that, a study that uses only psychology students as participants always carries a risk of lacking external validity. That is, if there’s something “special” about psychology students that makes them different to the general population in some relevant respect, then we may start worrying about a lack of external validity.
That said, it is absolutely critical to realise that a study that uses only psychology students does not necessarily have a problem with external validity. I’ll talk about this again later, but it’s such a common mistake that I’m going to mention it here. The external validity of a study is threatened by the choice of population if (a) the population from which you sample your participants is very narrow (e.g., psychology students), and (b) the narrow population that you sampled from is systematically different from the general population in some respect that is relevant to the psychological phenomenon that you intend to study. The italicised part is the bit that lots of people forget. It is true that psychology undergraduates differ from the general population in lots of ways, and so a study that uses only psychology students may have problems with external validity. However, if those differences aren’t very relevant to the phenomenon that you’re studying, then there’s nothing to worry about. To make this a bit more concrete here are two extreme examples:
- You want to measure “attitudes of the general public towards psychotherapy”, but all of your participants are psychology students. This study would almost certainly have a problem with external validity.
- You want to measure the effectiveness of a visual illusion, and your participants are all psychology students. This study is unlikely to have a problem with external validity
Having just spent the last couple of paragraphs focusing on the choice of participants, since that’s a big issue that everyone tends to worry most about, it’s worth remembering that external validity is a broader concept. The following are also examples of things that might pose a threat to external validity, depending on what kind of study you’re doing:
- People might answer a “psychology questionnaire” in a manner that doesn’t reflect what they would do in real life.
- Your lab experiment on (say) “human learning” has a different structure to the learning problems people face in real life.
Construct validity is basically a question of whether you’re measuring what you want to be measuring. A measurement has good construct validity if it is actually measuring the correct theoretical construct, and bad construct validity if it doesn’t. To give a very simple (if ridiculous) example, suppose I’m trying to investigate the rates with which university students cheat on their exams. And the way I attempt to measure it is by asking the cheating students to stand up in the lecture theatre so that I can count them. When I do this with a class of 300 students 0 people claim to be cheaters. So I therefore conclude that the proportion of cheaters in my class is 0%. Clearly this is a bit ridiculous. But the point here is not that this is a very deep methodological example, but rather to explain what construct validity is. The problem with my measure is that while I’m trying to measure “the proportion of people who cheat” what I’m actually measuring is “the proportion of people stupid enough to own up to cheating, or bloody minded enough to pretend that they do”. Obviously, these aren’t the same thing! So my study has gone wrong, because my measurement has very poor construct validity.
Face validity simply refers to whether or not a measure “looks like” it’s doing what it’s supposed to, nothing more. If I design a test of intelligence, and people look at it and they say “no, that test doesn’t measure intelligence”, then the measure lacks face validity. It’s as simple as that. Obviously, face validity isn’t very important from a pure scientific perspective. After all, what we care about is whether or not the measure actually does what it’s supposed to do, not whether it looks like it does what it’s supposed to do. As a consequence, we generally don’t care very much about face validity. That said, the concept of face validity serves three useful pragmatic purposes:
- Sometimes, an experienced scientist will have a “hunch” that a particular measure won’t work. While these sorts of hunches have no strict evidentiary value, it’s often worth paying attention to them. Because often times people have knowledge that they can’t quite verbalise, so there might be something to worry about even if you can’t quite say why. In other words, when someone you trust criticises the face validity of your study, it’s worth taking the time to think more carefully about your design to see if you can think of reasons why it might go awry. Mind you, if you don’t find any reason for concern, then you should probably not worry. After all, face validity really doesn’t matter very much.
- Often (very often), completely uninformed people will also have a “hunch” that your research is crap. And they’ll criticise it on the internet or something. On close inspection you may notice that these criticisms are actually focused entirely on how the study “looks”, but not on anything deeper. The concept of face validity is useful for gently explaining to people that they need to substantiate their arguments further.
- Expanding on the last point, if the beliefs of untrained people are critical (e.g., this is often the case for applied research where you actually want to convince policy makers of something or other) then you have to care about face validity. Simply because, whether you like it or not, a lot of people will use face validity as a proxy for real validity. If you want the government to change a law on scientific psychological grounds, then it won’t matter how good your studies “really” are. If they lack face validity you’ll find that politicians ignore you. Of course, it’s somewhat unfair that policy often depends more on appearance than fact, but that’s how things go.
Ecological validity is a different notion of validity, which is similar to external validity, but less important. The idea is that, in order to be ecologically valid, the entire set up of the study should closely approximate the real world scenario that is being investigated. In a sense, ecological validity is a kind of face validity. It relates mostly to whether the study “looks” right, but with a bit more rigour to it. To be ecologically valid the study has to look right in a fairly specific way. The idea behind it is the intuition that a study that is ecologically valid is more likely to be externally valid. It’s no guarantee, of course. But the nice thing about ecological validity is that it’s much easier to check whether a study is ecologically valid than it is to check whether a study is externally valid. A simple example would be eyewitness identification studies. Most of these studies tend to be done in a university setting, often with a fairly simple array of faces to look at, rather than a line up. The length of time between seeing the “criminal” and being asked to identify the suspect in the “line up” is usually shorter. The “crime” isn’t real so there’s no chance of the witness being scared, and there are no police officers present so there’s not as much chance of feeling pressured. These things all mean that the study definitely lacks ecological validity. They might (but might not) mean that it also lacks external validity.
Confounds, 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 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’t 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 describes a threat to your external validity, because it raises the possibility that you can’t 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’re not proper experiments. By definition, you’re leaving lots of things uncontrolled, so there’s 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 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’s 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’s really hard to think everything through ahead of time and even very good researchers make mistakes.
Although there’s a sense in which almost any threat to validity can be characterised as a confounder or an artefact, they’re pretty vague concepts. So let’s have a look at some of the most common examples.
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’re 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’re 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’re 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’re 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 middle however, because your lab is in Los Angeles, there’s an earthquake which increases the anxiety of the participants.
As with history effects, maturational effects are fundamentally about change over time. However, maturation effects aren’t 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 won’t be able to tell if your educational trick works.
- When running a very long experiment in the lab (say, something that goes for 3 hours) it’s 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’ve 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 is a pretty broad term. Suppose that you’re 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’ve 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’re in a lot of trouble.
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’ll 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 “Dani’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’t 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 “Dani’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 that 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’s 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’s 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’s 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 isn’t going to be random. The people most likely to drop out would probably be the people who don’t 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’ve introduced a confound: 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 doesn’t 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 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 don’t. 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 wasn’t answered was on the last page of the questionnaire, and those 80 surveys were returned with the last page missing, there’s a good chance that the missing data isn’t a big deal; probably the pages just fell off. However, if the question that 80 people didn’t answer was the most confrontational or invasive personal question in the questionnaire, then almost certainly you’ve got a problem. In essence, what you’re dealing with here is what’s called the problem of missing data. If the data that is missing was “lost” randomly, then it’s not a big problem. If it’s 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’s an example. Suppose I’m 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’re doing at university. It turns out that they’re doing a lot better than average, but they’re not topping the class at university even though they did top their classes at high school. What’s 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’s more likely that what you’re seeing is an example of “regression to the mean”. To see how it works, let’s 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’ve 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’s the thing, whilst intelligence and hard work are transferable from one class to the next, luck isn’t. The people who got lucky in high school won’t be the same as the people who get lucky at university. That’s 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’re selecting for hard work, skill and luck. But because the luck doesn’t 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’s a selection bias here! When people do very well, you’re 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 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 didn’t 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’s important to recognise that it’s 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 doesn’t 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) doesn’t 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’s 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’s a thing called the “Pygmalion effect”, where if you expect great things of people they’ll tend to rise to the occasion. But if you expect them to fail then they’ll do that too. In other words, the expectations become a self-fulfilling prophesy.
Demand effects 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’s almost impossible to stop people from knowing that they’re 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 effects. 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.
The placebo effect is a specific type of demand effect 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’s a cure for a disease, they will tend to get better faster than people who aren’t 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 won’t 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.
There’s 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 couldn’t 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. Not only that, as I mentioned earlier, scientists are not immune to belief bias. It’s 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 didn’t find much of a discussion of this problem, so here’s 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’s 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’s much more common in my experience to see data being misrepresented. When I say this I’m not referring to newspapers getting it wrong (which they do, almost always). I’m referring to the fact that often the data don’t actually say what the researchers think they say. My guess is that, almost always, this isn’t 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’s 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’s 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’re feeling like dabbling in a bit of fraud yourself, is to design an experiment in which it’s obvious to the participants what they’re “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 won’t 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 won’t be obvious to the reader. What’s obvious to the participant when they’re in the experimental context isn’t always obvious to the person reading the paper. Of course, the way I’ve described this makes it sound like it’s always fraud. Probably there are cases where this is done deliberately, but in my experience the bigger concern has been 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 & post-hoc hypothesising. Another way in which the authors of a study can more or less misrepresent the data is by engaging in what’s 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’ll discuss later, if you keep trying to analyse your data in lots of different ways, you’ll eventually find something that “looks” like a real effect but isn’t. 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’s becoming very common. Data mining per se isn’t “wrong”, but the more that you do it the bigger the risk you’re 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’s 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 that you’ve done. If you acknowledge that you did it then other researchers are able to take your behaviour into account. If you don’t, then they can’t. And that makes your behaviour deceptive. Bad!
- Publication bias & self-censoring. Finally, a pervasive bias is “non-reporting” of negative results. This is almost impossible to prevent. Journals don’t 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 doesn’t, which one do you think is going to get published? Obviously, it’s the one study that did find that Finnegans Wake causes insanity. This is an example of a publication bias. Since no-one ever published the 19 studies that didn’t 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 aren’t 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’s 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’d also suggest taking a look at work by Kühberger et al. (2014) presenting statistical evidence that this actually happens in psychology.
There’s probably a lot more issues like this to think about, but that’ll 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 assumes that everyone else is honest and impartial. Actual scientists aren’t 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.
|||The reason why I say that it’s unmeasured is that if you have measured it, then you can use some fancy statistical tricks to deal with the confounder. Because of the existence of these statistical solutions to the problem of confounders, we often refer to a confounder that we have measured and dealt with as a covariate. Dealing with covariates is a more advanced topic, but I thought I’d mention it in passing since it’s kind of comforting to at least know that this stuff exists.|
|||Some people might argue that if you’re not honest then you’re not a real scientist. Which does have some truth to it I guess, but that’s disingenuous (look up the “No true Scotsman” fallacy). The fact is that there are lots of people who are employed ostensibly as scientists, and whose work has all of the trappings of science, but who are outright fraudulent. Pretending that they don’t exist by saying that they’re not scientists is just muddled thinking.|
|||Clearly, the real effect is that only insane people would even try to read Finnegans Wake.|