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Weak Statistical Standards Implicated In Scientific Irreproducibility
ananyo writes "The plague of non-reproducibility in science may be mostly due to scientists' use of weak statistical tests, as shown by an innovative method developed by statistician Valen Johnson, at Texas A&M University. Johnson found that a P value of 0.05 or less — commonly considered evidence in support of a hypothesis in many fields including social science — still meant that as many as 17–25% of such findings are probably false (PDF). He advocates for scientists to use more stringent P values of 0.005 or less to support their findings, and thinks that the use of the 0.05 standard might account for most of the problem of non-reproducibility in science — even more than other issues, such as biases and scientific misconduct."
This would have the same problems, maybe even worse. The problem with statistics is usually that the model is wrong, and Bayesian stats offers two chances to fuck that up: in the prior, and in the generative model (=likelihood). Bayesian statistics still requires models (yes, you can do non-parametric Bayes, but you can do non-parametric frequentist stats also).
Contrary to the hype and buzzwords, Bayesian statistics is not some magical solution. It is incredibly useful when done right, of course.
That is because of the central limit theorem, (http://en.wikipedia.org/wiki/Central_limit_theorem), which indicated that for a large number of independent samples, it doesn't matter what the original distribution was, and we certainly can reliably use the normal distribution. It is NOT unfounded.
Five sigma is the standard of proof in Physics. The probability of a background fluctuation is a p-value of something like 0.0000006.
Such an admonishment is fine for the computational fields, where a few more permutations can net you a p-value of 0.0005 (assuming that you aren't crunching on a 4-month cluster problem). However, biological laborations are often very expensive and take a lot of time. Furthermore, additional tests are not always possible, since it can be damn hard to reproduce specific mutations or knockout sequences without altering the surrounding interactive factors.
So, should we go for a better p-value for the experiment and scrap any complicated endeavour, or should we allow for difficult experiments and take it with a grain of salt?
Truth is expensive.
The problem with frequentist statistics as used in the article is that its "recipe" character often results in people using statistics that do not understand its limitations (a good example is assuming a normal distribution when there is none). The bayesian approach does not suffer from this problem, also because it forces you to think a little bit more about the problem you are trying to solve compared to the frequentist approach. But that's also the problem with the cited article. Just remaining in the framework and going towards more discriminating thresholds is not really a solution of the problem that people do not understand their data analysis (a p-value based on the wrong distribution remains meaningless, even if you change your threshold...). Because it is more logical in its setup, the danger of making such mistakes is smaller in bayesian statistics. The telescoper over at http://telescoper.wordpress.com/2013/11/12/the-curse-of-p-values/ has a good discussion of these issues.
If we were to insist on statistically meaningful results 90% of our contemporary journals would cease to exist for lack of submissions.
Statistics does not, by any means, make that assumption. If it did, the entire field of statistics would have been completed by 1810.
Mediocre (actually, sub-mediocre) practitioners of statistics make that assumption.
It is true that many estimators tend to a normal distribution as the sample size gets large, but this is not the same as assuming that the data itself comes from the normal distribution.
Personally, I've considered results with p values between 0.01 and 0.05 as merely 'suggestive': "It may be worth looking into this more closely to find out if this effect is real." Between 0.01 and 0.001 I'd take the result as tentatively true - I'll accept it until someone refutes it.
If you take p=0.04 as demonstrating a result is true, you're being foolish and statistically naive. However, unless you're a compulsive citation follower (which I'm not) you are somewhat at the mercy of other authors. If Alice says "In Bob (1998) it was shown that ..." I'll tend to accept it without realizing that Bob (1998) was a p=0.04 result.
Obligatory XKCD
Quattuor res in hoc mundo sanctae sunt: libri, liberi, libertas et liberalitas.
http://xkcd.com/882/
No, statisticians certainly do not assume that. If everything in my field were normally distributed then my life would be a lot easier, but it's not, and we're aware that it's not.
Authors need to read this: http://www.deirdremccloskey.com/articles/stats/preface_ziliak.php
It explains quite clearly why a p value 0.05 is a fairly arbitrary choice as it cannot possibly the standard for every possible study out there. Or, put it another way, be very skeptical when one sole number (namely 0.05) is supposed to be a universal threshold to decide on the significance of all possible findings, in all possible domains of science. The context of any finding still matters for its significance.
Yes, I agree. If a p-value of 0.05 actually "means" 0.20 when evaluated, then any sane frequentist will tell you that things are fucked, since the limiting probability does not match the nominal probability (this is the definition of frequentism).
The power of Bayesian stats is largely in being able to easily represent hierarchical models, which are very powerful for modeling dependence in the data through latent variables. But it's not the Bayesianism per se that fixes things, it's the breadth of models it allows. A mediocre modeler using Bayesian statistics will still create mediocre models, and if they use a bad prior, then things will be worse than they would be for a frequentist.
Consider that if Bayesian statisticians are doing a better job than frequentists at the moment, it may be because Bayesian stats hasn't yet been drilled into the minds of the mediocre, as frequentist stats has been for decades. People doing Bayesian stats tend to be better modelers to begin with.
Unreliable research
Trouble at the lab
Scientists like to think of science as self-correcting. To an alarming degree, it is not
Oct 19th 2013 |From the print edition
The Economist
First, the statistics, which if perhaps off-putting are quite crucial. Scientists divide errors into two classes. A type I error is the mistake of thinking something is true when it is not (also known as a “false positive”). A type II error is thinking something is not true when in fact it is (a “false negative”). When testing a specific hypothesis, scientists run statistical checks to work out how likely it would be for data which seem to support the idea to have come about simply by chance. If the likelihood of such a false-positive conclusion is less than 5%, they deem the evidence that the hypothesis is true “statistically significant”. They are thus accepting that one result in 20 will be falsely positive—but one in 20 seems a satisfactorily low rate.
In 2005 John Ioannidis, an epidemiologist from Stanford University, caused a stir with a paper showing why, as a matter of statistical logic, the idea that only one such paper in 20 gives a false-positive result was hugely optimistic. Instead, he argued, “most published research findings are probably false.” As he told the quadrennial International Congress on Peer Review and Biomedical Publication, held this September in Chicago, the problem has not gone away.
Dr Ioannidis draws his stark conclusion on the basis that the customary approach to statistical significance ignores three things: the “statistical power” of the study (a measure of its ability to avoid type II errors, false negatives in which a real signal is missed in the noise); the unlikeliness of the hypothesis being tested; and the pervasive bias favouring the publication of claims to have found something new.
http://www.economist.com/news/briefing/21588057-scientists-think-science-self-correcting-alarming-degree-it-not-trouble
Unless of course we happen to be working in a chaotic system where strange attractors mean there can be no centrality to the data.
Chaos theory is a lot younger than the central limit theorem. The situation might be similar to the way Einstein's theory of relativity has moved Newton's three laws from a position of central importance in all physics to something that works well enough in a small subset. A subset that is extremely important in our daily life, but still a subset.
Some portions of a chaotic system will be consistent with what the central limit theorem would predict. Other data sets from the same system, uh, no.
An important question I do not believe has been answered yet (I am an armchair follower of this stuff, neither expert nor student) is whether all the systems we work with where the CLT does seem to hold are merely subsets of larger systems. A related question would be whether there is any test that can be applied to a discrete data set that rule out its being a subset of a larger chaotic process.
Will
http://www.youtube.com/watch?v=HtMX_0jDsrw
So it gives you a very valid excuse to assume that the value distribution of some quantity occurring in nature will follow a Normal distribution when you know nothing else about it.
But there's the crux: it remains an assumption; a hypothesis, and fortunately it's usually a *testable* hypothesis. It's the responsibility of a researcher to check if it holds, and to see how problematic it is when it doesn't.
If something has a normal distribution, its square or its square root (or another power) doesn't have a Normal distribution. Take for example the diameter, surface area, and volume of berries. The diameter (goes with the radius, r), the surface area (goes with r^2), and the volume of berries (goes with r^3). They cannot all be Normally distributed at the same time, so assuming any of them is starts you out on shaky foundation.
Okay, here's the real problem with scientific studies.
All science is data compression, and all studies are are intended to compress data so that we can make future predictions. If you want to predict the trajectory of a cannonball, you don't need an almanac cross referencing cannonball weights, powder loads, and cannon angles - you can calculate the arc to any desired accuracy with a set of equations that fit on half a page. The half-page compresses the record of all prior experience with cannonball arcs, and allows us to predict future arcs.
Soft science studies typically make a set of observations which relate two measurable aspects. When plotted, the data points suggest a line or curve, and we accept the linear-regression (line or polynomial) as the best approximation for the data. The theory being that the underlying mechanism is the regression, and unrelated noise in the environment or measurement system causes random deviations of observation.
This is the wrong method. Regression is based on minimizing squared error, which was chosen by Laplace for no other reason that it is easy to calculate. There's lots of "rationalization" explanations of why it works and why it's "just the best possible thing to do", but there's no fundamental logic that can be used to deduce least squares from from fundamental assumptions.
Least squares introduces several problems:
1) Outliers will skew the values, and there is no computable way to detect or deal with outliers (source).
2) There is no computable way to determine whether the data represent a line or a curve - it's done by "eye" and justified with statistical tests.
3) The resultant function frequently looks "off" to the human eye, humans can frequently draw better matching curves; meaning: curves which better predict future data points.
4) There is no way to measure the predictive value of the results. Linear regression will always return the best line to fit the data, even when the data is random.
The right way is to show how much the observation data is compressed. If the regression function plus data (represented as offsets from the function) take fewer bits than the data alone, then you can say that the conclusions are valid. Further, you can tell how relevant the conclusions are, and rank and sort different conclusions (linear, curved) by their compression factor and choose the best one.
Scientific studies should have a threshold of "compresses data by N bits", rather than "1-in-20 of all studies are due to random chance".
Having quickly skimmed the paper, I'll give an example of the problem. .54 .65 .74 .83 .88 .96 .94 .98
I couldn't quickly find a real data set that was easy to interpret, so I'm going to make up some data.
Chance to die before reaching this age
Age woman man
80
85
90
95
We have a person who is 90 years old. Taking the null hypothesis to be that this person is a man, we can reject the hypothesis that this is a man with greater than 95 percent confidence (p=0.04). However, if we do a Bayesian analysis assuming prior probabilities of 50 percent for the person being a man or a woman, we find that there is a 25 percent chance that the person is a man after all (as women are 3 times more likely to reach age 90 than men are.)
(Having 11 percent signs in my post seems to have given /. indigestion so I've had to edit them out.)
Quattuor res in hoc mundo sanctae sunt: libri, liberi, libertas et liberalitas.
At one level, they are right that unreproducible results are usually not fraud, but are simply fluctuations that make a study look promising leading to publication. But raising the standard of statistical significance will not really improve the situation. The most important uncertainties in most scientific studies are not random. You can't quantify them assuming a gaussian distribution. There are all kind of choices made in acquiring, processing, and presenting data. The incentives that scientists have are all pushing them to look for ways to obtain a high profile result. We make our best guesses trying to be honest, but when a set of guesses leads to a promising result we publish it and trust further study to determine whether our guesses were fully justified. There is one step that would improve the situation. We need to provide a mechanism to receive career credit for reproducing earlier results or for disproving earlier results. At the moment, you get no credit for doing this. And you will never get funding to do it. The only way to be successful is to spit out a lot of papers and have some of them turn out to be major results that others build on. The number of papers that turn out to be wrong is of no consequence. No one even notices except a couple of researchers who try to build on your result, fail, and don't publish. In their later papers they will probably carefully dance around the error so as not to incur the wrath of a reviewer. If reproducing earlier results was a priority, then we would know earlier which results were wrong and could start giving negative career credit to people who publish a lot of errors.
This is a geek website, not a "research" website so stop talking a bunch of crap about a bunch of crap. I'm providing silly examples so don't focus upon them. Most researchers suck at stats and my attempt at explaining should either help out or show that I don't know what I'm talking about. Take your pick.
"p=.05" is a stat that reflects the likelihood of rejecting a true null hypothesis. So, lets say that my hypothesis is that "all cats like dogs" and my null hypothesis is "not all cats like dogs." If I collect a whole bunch of imaginary data, run it through a program like SPSS, and the results turn out that my hypothesis is correct then I have a .05 percent chance that the software is wrong. In that particular imaginary case, I would have committed a Type I Error. This error has a minimal impact because the only bad thing that would happen is some dogs get clawed on the nose and a few cats get eaten.
Now, on a typical experiment, we also have to establish beta which is the likelihood of committing a type II error, that is, accepting a false null hypothesis. So let's say that my hypothesis is that "Sex when desired makes men happy" and my null hypothesis is "Sex only when women want it makes men happy." It's not a bad thing if #1 is accepted but the type II error will make many men unhappy.
Now, this is a give and take relationship. Every time that we make p smaller (.005, .0005, .00005, etc.) for "accuracy," then the risk of committing a type II error increases. A type II error when determining what games 15 year olds like to play doesn't really matter if we are wrong but if we start talking about drugs and false positives then the increased risk of a type II error really can make things ugly.
Next, there are guideline for determining a how many participants are needed for lower p (alpha) values. Social sciences (hold back your Sheldon jokes) that do studies on students might need lets say 35 subjects/people per treatment group at p=.05 whereas with a .005 might need 200 or 300 per treatment group. I don't have a stats book in front of me but .0005 could be in the thousands. Every adjustment impacts a different item in a negative fashion. You can have your Death Star or you can have Luke Skywalker. Can't have 'em both.
Finally, there is a statistical concept of power, that is, there are stats for measuring the impact of a treatment. Basically, how much of the variance between the group A and group B can be assigned to the experimental treatment. This takes precedence in many peoples minds over simply determining if we have a correct or incorrect hypothesis. Assigning p does not answer this.
Anyways, I'm going to go have another beer. Discard this article and move onto greener pastures.
The problem with frequentist statistics as used in the article is that its "recipe" character often results in people using statistics that do not understand its limitations (a good example is assuming a normal distribution when there is none). The bayesian approach does not suffer from this problem, also because it forces you to think a little bit more about the problem you are trying to solve compared to the frequentist approach.
If only. The number of people who think "sprinkle a little Bayes on it" is the solution to everything is frighteningly large, and growing exponentially AFAICT. There's now a Bayesian recipe counterpart to just about every non-Bayesian recipe, and the only difference between them, as a practical matter, is that the people using the former think they're doing something special and better. One might say that their prior is on the order of P(correct|Bayes) = 1, which makes it very hard to convince them otherwise ...
The correlation between ignorance of statistics and using "correlation is not causation" as an argument is close to 1.
The CLT is one of the most elegant and powerful results in all of mathematics, and can be used, quite appropriately, to justify normal models for all sorts of measurements. That being said, its usefulness has led to the dumbed-down idea of "the bell curve" being the appropriate model for all sorts of things where it's clearly not--I don't know how many times I've seen a normal curve superimposed on a histogram or kernel density estimation of data that are clearly non-normal. As another poster pointed out, there are simple and well-understood tests for normality, and failure to apply them when constructing a normal model is just ridiculous.
The correlation between ignorance of statistics and using "correlation is not causation" as an argument is close to 1.
A P-value of 0.05 means by definition that there is a 0.05, or 5%, or 1 in 20, probability that the result could be obtained by chance even though there's no actual relationship.
Tom Swiss | the infamous tms | my blog
You cannot wash away blood with blood
First of all, recommending that hypothesis tests be conducted with smaller tolerances for Type I error almost invariably imply a large decrease in power. There is no free lunch. There are many experimental designs for which the importance of making a positive inference (i.e., accepting the alternative hypothesis) is so great that you do need to set the alpha level very small. But if the test is to have any power, that means the data you must gather must be much, much more extensive. So, to simply say "alpha = 0.05 is too large because it admits too many irreproducible claims by random chance" sort of misses the basic point. A test conducted at such a level still has at most a 1 in 20 chance of observing a test statistic that would reject the null hypothesis even if the null is true. So a p-value of 0.04, for example, would merit further investigation. That's not so much a flaw of the frequentist methods as it is a flaw in interpretation, due to the natural tendency of investigators or clinicians to want a straightforward "yes/no" answer.
Bayesian methods, then, don't really offer intrinsically more meaning than frequentist methods. The main difference is that Bayesian methods, by their construction, force the investigator to draw an inference that is not characterized by a "yes/no" answer--in fact, it becomes a bit of a contrivance (e.g., Bayes factors and the calculation of cumulative posterior distributions) to try to interpret Bayesian analyses in this way. Don't get me wrong, that is an appealing and advantageous characteristic, whereas more care is needed to interpret the frequentist approach. But Bayesian methods also suffer from their own problems, many of which arise from the necessity of imposing some kind of prior distribution (so, for instance, Bayes factors are not monotone in the hypothesis).
The takeaway here is that in statistics, there is no magic bullet, no single approach that is supposed to be the "best" or "optimal" for inferential purposes. It is the role of scientists and investigators to perform the necessary follow-up analyses and meta-analyses to improve the credibility of a claim. So in a sense, the state of statistical methods in scientific research is NOT broken. It is working as intended, where people find enough evidence to stimulate further investigation, and it is through this process that previous claims are tested further. The only part that concerns me is how policymakers lacking in sufficient statistical background might put too much credence in a particular analysis--this idea that "oh, we found significance so this MUST be true"--or how the non-statistically informed public or media all too often distort the meaning of an analysis to the point of absurdity. But I argue that this is not a weakness of statistics. It is a deficiency in understanding brought about the human desire to act upon perceived certainties in a fundamentally uncertain world.