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I'm a grad student in psychology, and as I pursue more and more independent studies in statistics, I am increasingly amazed by the inadequacy of my formal training. Both personal and second hand experience suggests that the paucity of statistical rigor in undergraduate and graduate training is rather ubiquitous within psychology. As such, I thought it would be useful for independent learners like myself to create a list of "Statistical Sins", tabulating statistical practices taught to grad students as standard practice that are in fact either superseded by superior (more powerful, or flexible, or robust, etc) modern methods or shown to be frankly invalid. Anticipating that other fields might also experience a similar state of affairs, I propose a community wiki where we can collect a list of Statistical Sins across disciplines. Please submit one "sin" per answer.

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I'm aware that "sin" is possibly inflammatory and that that some aspects of statistical analysis are not black-and-white. My intention is to solicit cases where a given commonly-taught practice is pretty clearly inappropriate. –  Mike Lawrence Nov 15 '10 at 18:53
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You can also add biology/life sciences students to the mix if you like ;) –  nico Nov 15 '10 at 19:03
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@whuber There was some good answers, so I've merged them both. –  mbq Feb 6 '11 at 11:02

42 Answers 42

Most interpretations of p-values are sinful! The conventional usage of p-values is badly flawed; a fact that, in my opinion, calls into question the standard approaches to the teaching of hypothesis tests and tests of significance.

Haller and Krause have found that statistical instructors are almost as likely as students to misinterpret p-values. (Take the test in their paper and see how you do.) Steve Goodman makes a good case for discarding the conventional (mis-)use of the p -value in favor of likelihoods. The Hubbard paper is also worth a look.

Haller and Krauss. Misinterpretations of significance: A problem students share with their teachers. Methods of Psychological Research (2002) vol. 7 (1) pp. 1-20 (PDF)

Hubbard and Bayarri. Confusion over Measures of Evidence (p's) versus Errors (α's) in Classical Statistical Testing. The American Statistician (2003) vol. 57 (3)

Goodman. Toward evidence-based medical statistics. 1: The P value fallacy. Ann Intern Med (1999) vol. 130 (12) pp. 995-1004 (PDF)

Also see:

Wagenmakers, E-J. A practical solution to the pervasive problems of p values. Psychonomic Bulletin & Review, 14(5), 779-804.

for some clear cut cases where even the nominally "correct" interpretation of a p-value has been made incorrect due to the choices made by the experimenter.

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@Michael (+1) I added links to abstracts and ungated PDFs. Hope you don't mind. –  chl Nov 16 '10 at 10:24
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+1, but I would like to make some critical comments. Regarding the opening line, one could just as well say that "almost all" (in the measure theoretic sense) interpretations of any well-defined concept are incorrect, because only one is correct. Second, to what do you refer when you say "the conventional usage" and "standard approaches"? These vague references sound like a straw man. They do not accord with what one can find in the literature on statistics education, for example. –  whuber Nov 17 '10 at 13:43
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@Whuber Have a look at the Goodman paper. It accords pretty well with my experience in the field of pharmacology. Methods say "Results where P<0.05 were taken as statistical significant" and then results are presented with + for p<0.05, ++ for p<0.01 and +++ for p<0.0001. The statement implies the control of error rates a la Neyman and Pearson, but the use of different levels of p suggest Fisher's approach where the p value is an index of the strength of evidence against the null hypothesis. As Goodman points out, you cannot simultaneously control error rates and assess strength of evidence. –  Michael Lew Nov 18 '10 at 2:41
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@Michael There are alternative, more generous interpretations of that kind of reporting. For example, the author might be aware that readers might want to apply their own thresholds of significance and therefore do the flagging of p-values to help them out. Alternatively, the author might be aware of possible multiple-comparisons problems and use the differing levels in a Bonferroni-like adjustment. Perhaps some portion of the blame for misuse of p-values should be laid at the feet of the reader, not the author. –  whuber Nov 18 '10 at 14:04
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@Whuber I agree entirely, but only that what you suggest is true in some small fraction of cases (a restricted version of 'entirely'). There are some journals that specify that p values should be reported at one, two or three star levels rather than exact values, so those journals share some responsibility for the outcome. However, both that ill-considered requirement and the apparently naive use of p values might be a result of the lack of a clear explanation of the differences between error rates and evidence in the several introductory statistics texts that are on my shelves. –  Michael Lew Nov 19 '10 at 3:40

Failing to look at (plot) the data.

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The most dangerous trap I encountered when working on a predictive model is not to reserve a test dataset early on so as to dedicate it to the "final" performance evaluation.

It's really easy to overestimate the predictive accuracy of your model if you have a chance to somehow use the testing data when tweaking the parameters, selecting the prior, selecting the learning algorithm stopping criterion...

To avoid this issue, before starting your work on a new dataset you should split your data as:

  • development set
  • evaluation set

Then split your development set as a "training development set" and "testing development set" where you use the training development set to train various models with different parameters and select the bests according to there performance on the testing development set. You can also do grid search with cross validation but only on the development set. Never use the evaluation set while model selection is not 100% done.

Once your are confident with the model selection and parameters, perform a 10 folds cross-validation on the evaluation set to have an idea of the "real" predictive accuracy of the selected model.

Also if your data is temporal, it is best to choose the development / evaluation split on a time code: "It's hard to make predictions - especially about the future."

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I agree with this in principle but in the case of a small data set (I often have only 20-40 cases) use of a separate evaluation set is not practical. Nested cross-validation can get around this but may lead to pessimistic estimates on small data sets –  BGreene Jul 24 '12 at 16:39
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In general it takes an enormous dataset for data splitting to be reliable. That's why stringent internal validation with the bootstrap is so attractive. –  Frank Harrell Jun 15 '13 at 15:53

Reporting p-values when you did data-mining (hypothesis discovery) instead of statistics (hypothesis testing).

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Testing the hypotheses $H_0: \mu=0$ versus $H_1: \mu\neq 0$ (for example in a Gaussian setting)

to justify that $\mu=0$ in a model (i.e mix "$H_0$ is not rejected" and "$H_0$ is true").

A very good example of that type of (very bad) reasoning is when you test whether the variances of two Gaussians are equal (or not) before testing if their mean are equal or not with the assumption of equal variance.

Another example occurs when you test normality (versus non normality) to justify normality. Every statistician has done that in is life ? it is baaad :) (and should push people to check robustness to non Gaussianity)

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The same logic (taking "absence of evidence in favor H1" as "evidence of absence of H1") essentially underlies all goodness-of-fit tests. The reasoning also often crops up when people state "the test was non significant, we can therefore conclude there is no effect of factor X / no influence of variable Y". I guess the sin is less severe if accompanied by reasoning about the test's power (e.g., a-priori estimation of sample size to reach a certain power given a certain relevant effect size). –  caracal Nov 16 '10 at 23:07

Dichotomization of a continuous predictor variable to either "simplify" analysis or to solve for the "problem" of non-linearity in the effect of the continuous predictor.

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I don't think this is really a "sin" as the results obtained are not wrong. However, it does throw away a lot of useful information so is not good practice. –  Rob Hyndman Nov 15 '10 at 22:51
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Along these lines, using extreme groups designs over-estimates effect sizes whereas the use of a mean or median split under-estimates effect sizes. –  rpierce Nov 16 '10 at 2:47
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This isn't even a sin if there are two or more distinct populations. Suppose you have separable classes or sub-populations, then it can make sense to discretize. A very trivial example: Would I rather use indicators for site/location/city/country or lat/long? –  Iterator Aug 9 '11 at 23:38

Not really answering the question, but there's an entire book on this subject:

Phillip I. Good, James William Hardin (2003). Common errors in statistics (and how to avoid them). Wiley. ISBN 9780471460688

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+1 I made sure to read this book shortly after it came out. I get plenty of opportunities to make statistical mistakes so I'm always grateful to have them pointed out before I make them! –  whuber Dec 12 '10 at 23:02

interpreting Probability(data | hypothesis) as Probability(hypothesis | data) without the application of Bayes' theorem.

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A few mistakes that bother me:

  1. Assuming unbiased estimators are always better than biased estimators.

  2. Assuming that a high $R^2$ implies a good model, low $R^2$ implies a bad model.

  3. Incorrectly interpreting/applying correlation.

  4. Reporting point estimates without standard error.

  5. Using methods which assume some sort of Multivariate Normality (such as Linear Discriminant Analysis) when more robust, better performing, non/semiparametric methods are available.

  6. Using p-value as a measure of strength between a predictor and the response, rather than as a measure of how much evidence there is of some relationship.

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Would you break these out into separate options? –  rpierce Dec 12 '10 at 21:27

Ritualized Statistics.

This "sin" is when you apply whatever thing you were taught, regardless of its appropriateness, because it's how things are done. It's statistics by rote, one level above letting the machine choose your statistics for you.

Examples are Intro to Statistics-level students trying to make everything fit into their modest t-test and ANOVA toolkit, or any time one finds oneself going "Oh, I have categorical data, I should use X" without ever stopping to look at the data, or consider the question being asked.

A variation on this sin involves using code you don't understand to produce output you only kind of understand, but know "the fifth column, about 8 rows down" or whatever is the answer you're supposed to be looking for.

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Unfortunately, if you aren't interested in statistical inference, or are scarce on time and/or resources, the ritual does seem very appealling... –  probabilityislogic Mar 9 '12 at 5:32

Being exploratory but pretending to be confirmatory. This can happen when one is modifying the analysis strategy (i.e. model fitting, variable selection and so on) data driven or result driven but not stating this openly and then only reporting the "best" (i.e. with smallest p-values) results as if it had been the only analysis. This also pertains to the point if multiple testing that Chris Beeley made and results in a high false positive rate in scientific reports.

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Analysis of rate data (accuracy, etc) using ANOVA, thereby assuming that rate data has Gaussian distributed error when it's actually binomially distributed. Dixon (2008) provides a discussion of the consequences of this sin and exploration of more appropriate analysis approaches.

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How much does this decrease the power of the analysis? In what conditions is it most problematic? In many cases deviations from the assumptions of ANOVA do not substantially affect the outcomes to an important extent. –  Michael Lew Nov 16 '10 at 7:48
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But in short, it is most problematic when probabilities observed are low or high as the range of values are constricted and unable to meet Gaussian assumptions. –  rpierce Nov 17 '10 at 15:14

Something I see a surprising amount in conference papers and even journals is making multiple comparisons (e.g. of bivariate correlations) and then reporting all the p<.05s as "significant" (ignoring the rightness or wrongness of that for the moment).

I know what you mean about psychology graduates, as well- I've finished a PhD in psychology and I'm still only just learning really. It's quite bad, I think psychology needs to take quantitative data analysis more seriously if we're going to use it (which, clearly, we should)

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This is particularly important. I remember reading a study about whether Ramadan was bad for babies whose mothers were fasting. It looked plausible (less food, lower birth weight), but then I looked at the appendix. Thousands of hypotheses, and a few percent of them were in the "significant" range. You get weird "conclusions" like "it's bad for the kid if Ramadan is the 2nd, 4th or 6th month". –  Carlos Jan 31 '11 at 13:06

Especially in epidemiology and public health - using arithmetic instead of logarithmic scale when reporting graphs of relative measures of association (hazard ratio, odds ratio or risk ratio).

More information here.

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Not to mention not labeling them at all xkcd.com/833 –  radek Dec 13 '10 at 22:18

The one that I see quite often and always grinds my gears is the assumption that a statistically significant main effect in one group and a non-statistically significant main effect in another group implies a significant effect x group interaction.

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Correlation implies causation, which is not as bad as accepting the Null Hypothesis.

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google makes $65B a year not caring about the difference... –  Neil McGuigan Dec 3 '10 at 7:41
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I agree with your points and they all are valid. But does Google's profit imply: correlation => causation? –  suncoolsu Dec 3 '10 at 7:53
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Google makes all that money not caring about causation at all. Indeed, why would it? Prediction is the thing... –  conjugateprior Mar 30 '12 at 14:56

While I can relate to much of what Michael Lew says, abandoning p-values in favor of likelihood ratios still misses a more general problem--that of overemphasizing probabilistic results over effect sizes, which are required to give a result substantive meaning. This type of error comes in all shapes and sizes and I find it to be the most insidious statistical mistake. Drawing on J. Cohen and M. Oakes and others, I've written a piece on this at http://integrativestatistics.com/insidious.htm .

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I'm actually unclear as to how a likelihood ratio (LR) does not achieve everything that an effect size achieves, while also employing an easily interpretable scale (the data contains X times more evidence for Y than for Z). An effect size is usually just some form of ratio of explained to unexplained variability, and (in the nested case) the LR is the ratio of unexplained variability between a model that has an effect and one that doesn't. Shouldn't there at least be a strong correlation between effect size and LR, and if so, what is lost by moving to the likelihood ratio scale? –  Mike Lawrence Jan 6 '11 at 19:54

A current popular one is plotting 95% confidence intervals around the raw performance values in repeated measures designs when they only relate to the variance of an effect. For example, a plot of reaction times in a repeated measures design with confidence intervals where the error term is derived from the MSE of a repeated measures ANOVA. These confidence intervals don't represent anything sensible. They certainly don't represent anything about the absolute reaction time. You could use the error term to generate confidence intervals around the effect but that is rarely done.

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Failing to test the assumption that error is normally distributed and has constant variance between treatments. These assumptions aren't always tested, thus least-squares model fitting is probably often used when it is actually inappropriate.

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What's inappropriate about least squares estimation when the data are non-normal or heteroskedastic? It is not fully efficient, but it is still unbiased and consistent. –  Rob Hyndman Nov 16 '10 at 3:18
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If the data are heteroscedastic you can end up with very innacurate out of sample predictions because the regression model will try too hard to minimise the error on samples in areas with high variance and not hard enough on samples from areas of low variance. This means you can end up with a very badly biased model. It also means that the error bars on the predictions will be wrong. –  Dikran Marsupial Nov 16 '10 at 9:31
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No, it is unbiased, but the variance is larger than if you used a more efficient method for the reasons you explain. Yes, the prediction intervals are wrong. –  Rob Hyndman Nov 16 '10 at 12:39
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Yes (I was using biased in a colloquial rather than a statistical sense to mean the model was systematically biased towards observations in high-variance regions of the feature space - mea culpa!) - it would be more accurate to say that the higher variance means there is an increased chance of getting a poor model using a finite dataset. That seems a reasonable answer to your question. I don't really view unbiasedness as being that much of a comfort - what is important is that the model should give good predictions on the data I actually have and often the variance is more important. –  Dikran Marsupial Nov 16 '10 at 22:18

My intro psychometrics course in undergrad spent at least two weeks teaching how to perform a stepwise regression. Is there any situation where stepwise regression is a good idea?

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"Good idea" depends on the situation. When you want to maximize prediction it isn't a horrible idea - though it may lead to over fitting. There are some rare cases where it is inevitable - where there is no theory to guide the model selection. I wouldn't count stepwise regression as a "sin" but using it when theory is sufficient to drive model selection is. –  rpierce Nov 16 '10 at 2:52
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Perhaps the sin is doing statistical tests on a model obtained via stepwise regression. –  Rob Hyndman Nov 16 '10 at 3:19

Maybe stepwise regression and other forms of testing after model selection.

Selecting independent variables for modelling without having any a priori hypothesis behind the existing relationships can lead to logical fallacies or spurious correlations, among other mistakes.

Useful references (from a biological/biostatistical perspective):

  1. Kozak, M., & Azevedo, R. a. (2011). Does using stepwise variable selection to build sequential path analysis models make sense? Physiologia plantarum, 141(3), 197–200. doi:10.1111/j.1399-3054.2010.01431.x

  2. Whittingham, M. J., Stephens, P. a, Bradbury, R. B., & Freckleton, R. P. (2006). Why do we still use stepwise modelling in ecology and behaviour? The Journal of animal ecology, 75(5), 1182–9. doi:10.1111/j.1365-2656.2006.01141.x

  3. Frank Harrell, Regression Modeling Strategies, Springer 2001.

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My old stats prof had a "rule of thumb" for dealing with outliers: If you see an outlier on your scatterplot, cover it up with your thumb :)

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That the p-value is the probability that the null hypothesis is true and (1-p) is the probability that the alternative hypothesis is true, of that failing to reject the null hypothesis means the alternative hypothesis is false etc.

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Interestingly, Atkin shows thhe pvalue is the posterior probability that the likelihood ratio is less than $1$ (for the fixed data that was observed) –  probabilityislogic May 5 '12 at 1:36
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(here you go)[ece.uvic.ca/~bctill/papers/mocap/Aitkin_1997.pdf] personally, while I do find it interesting, I struggle with the question of why the posterior distribution of the likelihood ratio is the quantity of interest. –  probabilityislogic May 6 '12 at 0:08

(With a bit of luck this will be controversial.)

Using a Neyman-Pearson approach to statistical analysis of scientific experiments. Or, worse, using an ill-defined hybrid of Neyman-Pearson and Fisher.

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Using pie charts to illustrate relative frequencies. More here.

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In similar vein to @dirkan - The use of p-values as a formal measure of evidence of the null hypothesis being true. It does have some good heuristic and intuitively good features, but is essentially an incomplete measure of evidence because it makes no reference to the alternative hypothesis. While the data may be unlikely under the null (leading to a small p-value), the data may be even more unlikely under the alternative hypothesis.

The other problem with p-values, which also relates to some styles of hypothesis testing, is there is no principle telling you which statistic you should choose, apart from the very vague "large value" $\rightarrow$ "unlikely if null hypothesis is true". Once again, you can see the incompleteness showing up, for you should also have "large value" $\rightarrow$ "likely if alternative hypothesis is true" as an additional heuristic feature of the test statistic.

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Using statistics/probability in hypothesis testing to measure the "absolute truth". Statistics simply cannot do this, they can only be of use in deciding between alternatives, which must be specified from "outside" the statistical paradigm. Statements such as "the null hypothesis is proved true by the statistics" are just incorrect; statistics can only tell you "the null hypothesis is favoured by the data, compared to the alternative hypothesis". If you then assume that either the null hypothesis or the alternative must be true, you can say "the null proved true", but this is only a trivial consequence of your assumption, not anything demonstrated by the data.

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This may be more of a pop-stats answer than what you're looking for, but:

Using the mean as an indicator of location when data is highly skewed.

This isn't necessarily a problem, if you and your audience knows what you're talking about, but this generally isn't the case, and the median is often likely to give a better idea of what's going on.

My favourite example is mean wages, which are usually reported as "average wages". Depending on the income/wealth inequality in a country, this can be vastly different from the median wage, which gives a much better indicator for where people are at in real life. For example, in Australia, where we have relatively low inequality, the median is 10-15% lower than the mean. In the US the difference is much starker, the median is less than 70% of the mean, and the gap is increasing.

Reporting on the "average" (mean) wage results in a rosier picture than is warranted, and could also give a large number of people the false impression that they aren't earning as much as "normal" people.

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In psychology, the cardinal sin (for me) is the use of principal components analysis to examine the hypothesised latent structure underlying a psychometric test.

Not testing for normality before using tests which assume this.

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Repeating the same or similar experiment over 20 times on the same data and then reporting a statistically significant result with $\alpha = 0.05$. Incidentally there is a comic about this one.

And similarly to (or almost the same as) @ogrisel's answer, performing a Grid search and reporting only the best result.

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