And for my next trick, I'll make this effect disappear!

In this week's New Yorker, Jonah Lehrer shows once again just how hard it is to do good science journalism if you are not yourself a scientist.

His target is the strange phenomenon that many high profile papers are failing to replicate. This has been very much a cause celebre lately, and Lehrer follows a series of scientific papers on the topic as well as an excellent Atlantic article by David Freedman. At this point, many of the basic facts are well-known: anecdotally, many scientists report repeated failures to replicate published findings. The higher-profile the paper, the less likely it is to replicate, with around 50% of the highest-impact papers in medicine failing to replicate. As Lehrer points out, this isn't just scientists failing to replicate each other's work, but scientists failing to replicate their own work: a thread running through the article is the story of Jonathan Schooler, a professor at UC-Santa Barbara who has been unable to replicate his own seminal graduate student work on memory.

Lehrer's focus in this article is shrinking effects.

No, not this one.

Some experimental effects seem to shrink steadily over time:

In 2001, Michael Jennions, a biologist at the Australian National University, set out to analyze "temporal trends" across a wide range of subjects in ecology and evolutionary biology. He looked at hundreds of papers and forty-four meta-analyses (that is, statistical syntheses of related studies), and discovered a consistent decline effect over time, as many of the theories seemed to fade into irrelevance.

As described, that's weird. But there is a good explanation for such effects, and Lehrer brings it up. Some results are spurious. It's just one of those things. Unfortunately, spurious results are also likely to be exciting. Let's say I run a study looking for a relationship between fruit-eating habits and IQ. I look at the effects of 20 different fruits. By chance, one of them will likely show a significant -- but spurious -- effect. So let's say I find that eating an apple every day leads to a 5-point increase in IQ. That's really exciting because it's surprising -- and the fact that it's not true is integral to what makes it surprising. So I get it published in a top journal (top journals prefer surprising results).

Now, other people try replicating my finding. Many, many people. Most will fail to replicate, but some -- again by chance -- will replicate. It is extremely difficult to get a failure to replicate published, so only the replications get published. After time, the "genius apple hypothesis" becomes part of established dogma. Remember that anything that challenges established dogma is exciting and surprising and thus easier to publish. So now failures to replicate are surprising and exciting and get published. When you look at effect-sizes in published papers over time, you will see a gradual but steady decrease in the "effect" of apples -- from 5 points to 4 points down to 0.

Where I get off the Bus

So far so good, except here's Lehrer again:

While the publication bias almost certainly plays a role in the decline effect, it remains an incomplete  explanation. For one thing, it fails to account for the initial prevalence of positive results among studies that never even get submitted to journals. It also fails to explaint eh experience of people like Schooler, who have been unable to replicate their initial data despite their best efforts.

Huh? Lehrer seems to be suggesting that it is publication that makes a result spurious. But that can't be right. Rather, there are just lots of spurious results out there. It happens that journals preferentially publish spurious results, leading to biases in the published record, and eventually the decline effect.

Some years ago, I had a bad habit of getting excited about my labmate's results and trying to follow them up. Just like a journal, I was interested in the most exciting results. Not surprisingly, most of these failed to replicate. The result was that none of them got published. Again, this was just a factor of some results being spurious -- disproportionately, the best ones. (Surprisingly, this labmate is still a friend of mine; personally, I'd hate me.)

The Magic of Point O Five

Some readers at this point might be wondering: wait -- people do statistics on their data and only accept a results that is extremely unlikely to have happened by chance. The cut-off is usually 0.05 -- a 5% chance of having a false positive. And many studies that turn out later to have been wrong pass even stricter statistical tests. Notes Lehrer:

And yet Schooler has noticed that many of the data sets that end up declining seem statistically solid--that is, they contain enough data that any regression to the mean shouldn't be dramatic. '"These are the results that pass all the tests," he says. "The odds of them being random are typically quite remote, like one in a million. This means that the decline effect should almost never happen. But it happens all the time!"

So there's got to be something making these results look more unlikely than they really are. Lehrer suspects unconscious bias:

Theodore Sterling, in 1959 ... noticed that ninety-seven percent of all published psychological studies with statistically significant data found the effect they were looking for ... Sterling saw that if ninety-seven per cent of psychology studies were proving their hypotheses, either psychologists were extraordinarily lucky or they published only the outcomes of successful experiments

and again:

The problem seems to be one of subtle omissions and unconscious misperceptions, as researchers struggle to make sense of their results.

I expect that unconscious bias is a serious problem (I illustrate some reasons below), but this is pretty unsatisfactory, as he doesn't explain how unconscious bias would affect results, and the Schooler effect is a complete red herring. 

I wasn't around in 1959, so I can't speak to that time, but I suspect that the numbers are similar today ... but in fact Sterling was measuring the wrong thing. Nobody cares what our hypotheses were. They don't care what order the experiments were actually run in. They care about the truth, and they have very limited time to read papers (most papers are never read, only skimmed). Good scientific writing is clear and concise. The mantra is: Tell them what you're going to tell them. Tell them. And then tell them what you told them. No fishing excursions, no detours. When we write scientific papers, we're writing science, not history.

And this means we usually claim to have expected to find whatever it is that we found. It just makes for a more readable paper. So when a scientist reads the line, "We predicted X," we know that really means "We found X" -- what the author actually predicted is beside the point.

Messing with that Point O Five

So where do all the false positive come from, if they should be less than 5% of conducted studies? There seem to be a number of issues.

First, it should be pointed out that the purpose of statistical tests (and the magic .05 threshold for significance) is to make a prediction as to how likely it is that a particular result will replicate. A p-value of .05 means roughly that there is a 95% chance that the basic result will replicate (sort of; this is not technically true but is a good approximation for present purposes).

But statistics are estimates, not facts. They are based on a large number of idealizations (for instance, many require that measurement error is distributed normally

a normal distribution

meaning that the bulk of measurements are very close to the true measurement and a measurement is as likely to be larger than the true number as it is likely to be smaller. In fact, most data is heavily skewed, with measurements more likely to be too large than too smaller (or vice versa).

For instance, give someone an IQ test. IQ tests have some measurement error -- people will score higher or lower than their "true" score due to random factors such as guessing answers correctly (or incorrectly), being sleepy (or not), etc. But it's a lot harder to get an IQ score higher than your true score than lower, because getting a higher score requires a lot of good luck (unlikely) whereas there are all sorts of ways to get a low score (brain freeze, etc.). 

Most statistical tests make a number of assumptions (like normally distributed error) that are not true of actual data. That leads to incorrect estimates of how likely a particular result is to replicate. The truth is most scientists -- at the very least, most psychologists -- aren't experts in statistics, and so statistical tests are misapplied all the time.

I don't actually think that issues like the ones I just discussed lead to most of the difficulties (though I admit I have no data one way or another). I bring these issues up mainly to point out at that statistical tests are tools that are either used or misused according to the skill of the experimenter. And there are lots of nasty ways to misuse statistical tests. I discuss a few of them below:

Run enough experiments and...

Let's go back to my genius fruit experiment. I ask a group of people to eat an apple and then give them an IQ test. I compare their IQ scores with scores from a control group that didn't eat an apple. Now let's say in fact eating apples doesn't affect IQ scores. Assuming I do my statistics correctly and all the assumptions of the statistical tests are met, I should have only a 5% chance of finding a "significant" effect of apple-eating.

Now let's say I'm disappointed in my result. So I try the same experiment with kiwis. Again, I have only a 5% chance of getting a significant result for kiwis. So that's not very likely to happen either.

Next I try oranges....

Hopefully you see where this is going. If I try only one fruit, I have a 5% chance of getting a significant result. If I try 2 fruits, I have a 1 - .95*.95 = 9.8% chance of getting a significant result for at least one of the fruits. If I try 4 fruits, now I'm up to a 1 - .95*.95*.95*.95 = 18.5% chance that I'll "discover" that one of these fruits significantly affects IQ. By the time I've tried 14 fruits, I've got a better than 50% chance of an amazing discovery. But my p-value for that one experiment -- that is, my estimate that these results won't replicate -- is less than 5%, suggesting there is only a 5% chance the results were due to chance.

While there are ways of statistically correcting for this increased likelihood of false positives, my experience suggests that it's relatively rare for anyone to do so. And it's not always possible. Consider the fact that there may be 14 different labs all testing the genius fruit hypothesis (it's suddenly very fashionable for some reason). There's a better than 50% chance that one of these labs will get a significant result, even though from the perspective of an individual lab, they only ran one experiment.

Data peaking

Many researchers peak at their data. There are good reasons for doing this. One is curiosity (we do experiments because we really want to know the outcome). Another is to make sure all your equipment is working (don't want to waste time collecting useless data). Another reason -- and this is the problematic one -- is to see if you can stop collecting data.

Time is finite. Nobody wants to spend longer on an experiment than necessary. Let's say you have a study where you expect to need -- based on intuition and past experience -- around 20 subjects. You might check your data after you've run 12, just in case that's enough. What usually happens is that if the results are significant, you stop running the study and move on. If they aren't, you run more subjects. Now maybe after you've got 20 subjects, you check your data. If it's significant, you stop the study; if not, you run some more. And you keep on doing this until either you get a significant result or you give up.

It's a little harder to do back-of-the-envelop calculations on the importance of this effect, but it should be clear that this habit has the unfortunate result of increasing the relative likelihood of a false positive, since false positives lead you to declare victory and end the experiment, whereas false negatives are likely to be corrected (since you keep on collecting more subjects until the false negative is overcome). I read a nice paper on this issue that actually crunched the numbers a while back (for some reason I can't find it at the moment), and I remember the result was a pretty significant increase in the expected number of false positives.

Data massaging

The issues I've discussed so real problems but are pretty common and not generally regarded as ethical violations. Data massaging is at the borderline.

Any dataset can be analyzed in a number of ways. Once again, if people get the result they were expecting with the first analysis they run, they're generally going to declare victory and start writing the paper. If you don't get the results you expect, you try different analysis methods. There are different statistical tests that be used. There are different covariates that could be factored out. You can through out "bad" subjects or items. This is going to significantly increase the rate of false positives.

It should be pointed out that interrogating your statistical model is a good thing. Ideally, researchers should check to see if there are bad subjects or items, check whether there are covariates to be controlled for, check whether different analysis techniques give different results. But doing this affects the interpretation of your p-value (the estimate of how likely it is that your results will replicate), and most people don't know how to appropriately control for that. And some are frankly more concerned with getting the results they want than doing the statistics properly (there is where the "borderline" comes in).

Better estimates

The problem, at least from where I stand, is one of statistics. We want our statistical tests to tell us how likely it is that our results will replicate. We have statistical tests which, if used properly, will give us just such an estimate. However, there are lots and lots of ways to use them incorrectly.

So what should we do? One possibility is to train people to use statistics better. And there are occasional revisions in standard practice that do result in better use of statistics.

Another possibility is to lower the p-value that is considered significant. The choice of p=0.05 as a cutoff was, as Lehrer notes, arbitrary. Picking a smaller number would decrease the number of false positives. Unfortunately, it also decreases the number of real positives by a lot. People who don't math can skip this next section.

Let's assume we're running studies with a single dependent variable and one manipulation, and that we're going to test for significance with a t-test. Let's say the manipulation really should work -- that is, it really does have an effect on our dependent measure. Let's say that the effect size is large-ish (Cohen's d of .8, which is large by psychology standards) and that we run 50 subjects. The chance of actually finding a significant effect at the p=.05 level is 79%. For people who haven't done power analyses before, this might seem low, but actually an 80% chance of finding an effect is pretty good. Dropping our significant threshold to p=.01 drops the chance of finding the effect to 56%. To put this in perspective, if we ran 20 such studies, we'd find 16 significant effects at the p=.05 level but only 11 at the p=.01 level. (If you want to play around with these numbers yourself, try this free statistical power calculator.)

Now consider what happens if we're running studies where the manipulation shouldn't have an effect. If we run 20 such studies, 1 of them will nonetheless give us a false positive at the p=.05 level, whereas we probably won't get any at the p=.01 level. So we've eliminated one false positive, but at the cost of nearly 1/3 of our true positives.

No better prediction of replication than replication

Perhaps the easiest method is to just replicate studies before publishing them. The chances of getting the same spurious result twice in a row are vanishingly small. Many of the issues I outlined above -- other than data massaging -- won't increase your replication rate. Test 14 different fruits to see if any of them increase IQ scores, and you have over a 50% chance that one of them will spuriously do so. Test that same fruit again, and you've only got a 5% chance of repeating the effect. So replication decreases your false positive rate 20-fold. Similarly, data massaging may get you that coveted p.05, but the chances of the same massages producing the same result again are very, very low.

True positives aren't nearly so affected. Again, a typical power level is B=0.80 -- 80% of the time that an effect is really there, you'll be able to find it. So when you try to replication a true positive, you'll succeed 80% of the time. So replication decreases your true positives by only 20%.

So let's say the literature has a 30% false positive rate (which, based on current estimates, seems quite reasonable). Attempting to replicate every positive result prior to publication -- and note that it's extremely rare to publish a null result (no effect), so almost all published results are positive results -- should decrease the false positives 20-fold and the true positives by 20%, leaving us with a 2.6% false positive rate. That's a huge improvement.

So why not replicate more?

So why don't people replicate before publishing? If 30% of your own publishable results are false positives, and you eliminate them, you've just lost 30% of your potential publications. You've also lost 20% of your true positives as well, btw, which means overall you've decreased your productivity by 43%. And that's without counting the time it takes to run the replication. Yes, it's nice that you've eliminated your false positives, but you also may have eliminated your own career!

When scientists are ranked, they're largely ranked on (a) number of publications, (b) number of times a publication is cited, and (c) quality of journal that the publications are in. Notice that you can improve your score on all of these metrics by publishing more false positives. Taking the time to replicate decreases your number of publications and eliminates many of the most exciting and surprising results (decreasing both citations and quality of journal). Perversely, even if someone publishes a failure to replicate your false positive, that's a citation and another feather in your cap.

I'm not saying that people are cynically increasing their numbers of bogus results. Most of us got into science because we actually want to know the answers to stuff. We care about science. But there is limited time in the day, and all the methods of eliminating false positives take time. And we're always under incredible pressure to pick up the pace of research, not slow it down.

I'm not sure how to solve this problem, but any solution I can think of involves some way of tracking not just how often a researcher publishes or how many citations those publications get, but how often those publications are replicated. Without having a way of tracking which publications replicate and which don't, there is no way to reward meticulous researchers or hold sloppy researchers to account.

Also, I think a lot of people just don't believe that false positives are that big a problem. If you think that only 2-3% of published papers contain bogus results, there's not a lot of incentive to put in a lot of hard work learning better statistical techniques, replicating everything, etc. If you think the rate is closer to 100%, you'd question the meaning of your own existence. As long as we aren't keeping track of replication rates, nobody really knows for sure where we are on this continuum.

That's my conclusion. Here's Lehrer's:

The decline effect is troubling because it reminds us how difficult it is to prove anything. We like to pretend that our experiments define the truth for us. But that's often not the case. Just because an idea is true doesn't mean it can be proved. And just because an idea can be proved doesn't mean it's true. When the experiments are done, we still have to chose what to believe.

I say it again: huh?