# Statistical tests, P values, confidence intervals, and power: a guide to misinterpretations

> An annotated edition of this paper on Fermat's Library, where scientists and readers explain its ideas, equations and history in the margins. Annotated edition: https://fermatslibrary.com/s/statistical-tests-p-values-confidence-intervals-and-power-a-guide-to-misinterpretations

- **Authors:** Sander Greenland et al.
- **Published:** 2016
- **Topic:** Biology
- **Original:** https://s3-us-west-1.amazonaws.com/fermatslibrary/uploads%2F1548602789706-oqn3n78cvb-46a0d8e53b8e1c2fe73aa38ab4e9edd6%2Fpvalue.pdf
- **Pages:** 14
- **Annotations:** 18 comments in 17 threads
- **Featured:** Fermat's Library Journal Club
- **Annotated edition:** https://fermatslibrary.com/s/statistical-tests-p-values-confidence-intervals-and-power-a-guide-to-misinterpretations

## Annotations

### Annotation 1 (page 1)

Beside the passage: “to misinterpretations”

**Annotation** by Stelios Serghiou (2019-02-04):

> For anyone interested in issues related to p-values, quality of research, open science and evidence-based practice, you may find the [Reddit community on meta-research](https://www.reddit.com/r/metaresearch/) of interest (disclaimer: I am one of the moderators of that community!)

### Annotation 2 (page 1)

Beside the passage: “Sander Greenland 1 • Stephen J. Senn 2 • Kenneth J. Rothman 3 • John B. Carlin 4 • Charles Poole 5 • Steven N. Goodman 6 • Douglas G. Altman 7”

**Annotation** by Stelios Serghiou (2019-01-28):

> These are heavyweight names in epidemiology/biostatistics. This paper represents the first time that I know of, where they united forces into writing an article, reflecting the importance of addressing these misinterpretations.

### Annotation 3 (page 1)

Beside the passage: “literature. In light of this problem, we provide deﬁnitions and a discussion of basic statistics that are more general and critical than typically found in traditional introductory expositions. Our goal is to provide a resource for instructors, researchers, and consumers of statistics whose knowledge of statistical …”

**Annotation** by Stelios Serghiou (2019-01-28):

> This same sentiment was expressed in the American Statistical Association's (ASA) [paper on p-values](https://amstat.tandfonline.com/doi/abs/10.1080/00031305.2016.1154108#.XE8wl89KjRY), to which this article served as a supplement. This was the first time ASA had ever produced such a statement of concern.

### Annotation 4 (page 1)

Beside the passage: “literature. In light of this problem, we provide deﬁnitions and a discussion of basic statistics that are more general and critical than typically found in traditional introductory expositions. Our goal is to provide a resource for instructors, researchers, and consumers of statistics whose knowledge of statistical …”

**Annotation** by Stelios Serghiou (2019-01-28):

> Another great resource for misinterpretations of p-values, which was also validated by one of the authors, can be found in Wikipedia's article [Misunderstandings of p-values](https://en.wikipedia.org/wiki/Misunderstandings_of_p-values).

### Annotation 5 (page 2)

Beside the passage: “Misinterpretation and abuse of statistical tests has been decried for decades, yet remains so rampant that some scientiﬁc journals discourage use of ‘‘statistical signiﬁcance’’ (classifying results as ‘‘signiﬁcant’’ or not based on a P value) [1]. One journal now bans all statistical tests and mathematically related …”

**Annotation** by Tymor Hamamsy (2019-02-04):

> In 2015, the journal "Basic and Applied Social Psychology" (BASP) declared the null hypothesis significance testing procedure invalid, and banned it for any studies appearing in its journal. For more: http://www.medicine.mcgill.ca/epidemiology/Joseph/courses/EPIB-621/BASP2015.pdf

### Annotation 6 (page 2)

Beside the passage: “There is also a serious problem of deﬁning the scope of a model, in that it should allow not only for a good representation of the observed data but also of hypothetical alternative data that might have been observed. The reference frame for data that ‘‘might have been observed’’ is often unclear, for example if …”

**Annotation** by Stelios Serghiou (2019-02-04):

> This is often known as data dredging or p-hacking - an excellent Wikipedia article on it can be found [here](https://en.wikipedia.org/wiki/Data_dredging). A MUST READ case that came to light last year is that of Brian Wansink, a Cornell professor, who inadvertently admitted p-hacking on his personal blog. Many of his papers are now retracted from the academic literature. You can read the original report about this case [here](https://www.buzzfeednews.com/article/stephaniemlee/brian-wansink-cornell-p-hacking).

### Annotation 7 (page 2)

Beside the passage: “Despite such bans, we expect that the sta tistical methods at issue will be with us for many years to come. We thus think it imperative that basic teaching as well as general understanding of these methods be improved. Toward that end, we attempt to explain the meaning of signiﬁcance tests, conﬁdence intervals, and …”

**Annotation** by Stelios Serghiou (2019-02-04):

> Unfortunately, this terminology has led to a misconception and many primarily look at the p-value, rather than the magnitude and direction of the effect being measured, to understand its significance. Well known scientists, such as Harvard's Miguel Hernan, have vouched to stop using the terminology "statistically significant".

### Annotation 8 (page 3)

Beside the passage: “Much statistical teaching and practice has developed a strong (and unhealthy) focus on the idea that the main aim of a study should be to test null hypotheses. In fact most descriptions of statistical testing focus only on testing null hypotheses, and the entire topic has been called ‘‘Null Hypothesis Signiﬁcance …”

**Annotation** by Tymor Hamamsy (2019-02-04):

> R.A. Fisher created the concept of a "p value" and the "null hypothesis" (no relationship between two measured phenomena) when he published about statistical significance tests in 1925, later starting in 1928 Neyman and Pearson began introducing the terminology for null and alternative hypothesis testing that are regularly used today.
>
> For more: https://en.wikipedia.org/wiki/Null_hypothesis

**Reply** by Stelios Serghiou (2019-02-04):

> Fisher was in fact vehemently against the null hypothesis significance testing procedure introduced by Neyman and Pearson (which is the procedure most scientists use today). He was very concerned that we would turn the often complicated process of inferring from data into an automated decision algorithm; unfortunately, it turns out he was spot on. One of the classic papers in this space offers further historic details and was written by one of the authors of this paper in 1993 - it can be found [here](https://academic.oup.com/aje/article/137/5/485/50007), but it is behind a paywall...

### Annotation 9 (page 3)

Beside the passage: “Speciﬁcally, the distance between the data and the model prediction is measured using a test statistic (such as a t-statistic or a Chi squared statistic). The P value is then the probability that the chosen test statistic would have been at least as large as its observed value if every model assumption were correct, …”

**Annotation** by Tymor Hamamsy (2019-02-04):

> Multiple hypothesis testing is a huge problem in the sciences. Let's say you have 20 hypotheses that you want to test and are using a significance threshold of .05. The probability of one of these hypotheses being significant by random chance is 1 − (1 − 0.05) ^20 = 64% probability.
>
> For more: https://www.stat.berkeley.edu/~mgoldman/Section0402.pdf

### Annotation 10 (page 3)

Beside the passage: “Nowhere are these problems more rampant than in applications of a hypothetical frequency called the P value, also known as the ‘‘observed signiﬁcance level’’ for the test hypothesis. Statistical ‘‘signiﬁcance tests’’ based on this concept have been a central part of statistical analyses for centuries [75]. The focus …”

**Annotation** by Stelios Serghiou (2019-02-04):

> [Here's](https://fivethirtyeight.com/features/not-even-scientists-can-easily-explain-p-values/) a funny clip from FiveThirtyEight, where scientists actually working on research quality and p-values at Stanford (including one of the authors of this paper) are asked on the spot to explain p-values!

### Annotation 11 (page 4)

Beside the passage: “misinterpretations as a way of moving toward defensi ble interpretations and presentations. We adopt the format of Goodman [40] in providing a list of misinterpretations that can be used to critically evaluate conclusions offered by research reports and reviews. Every one of the bolded statements in our list has …”

**Annotation** by Stelios Serghiou (2019-02-04):

> This is an excellent short read in its own right!

### Annotation 12 (page 4)

Beside the passage: “Common misinterpretations of single P values”

**Annotation** by Stelios Serghiou (2019-02-04):

> Wikipedia has a fantastic and very accessible article on the [Misunderstandings of of p-values](https://en.wikipedia.org/wiki/Misunderstandings_of_p-values), as also indicated above.

### Annotation 13 (page 5)

Beside the passage: “substantively important relation has been detected. No! Especially when a study is large, very minor effects or small assumption violations can lead to statistically signiﬁcant tests of the null hypot hesis. Again, a small null P value simply ﬂags the data as being unusual if all the assumptions used to compute it …”

**Annotation** by Tymor Hamamsy (2019-02-04):

> If you've ever worked with a big data set, you'll know that it is very easy to selectively fish for significant p-values. If you're working with "big data", even the smallest differences might appear as "statistically significant"-> always put your results in context and inspect effect sizes. The more data you have, you probably want to try smaller significance levels, especially if you're testing multiple hypotheses (see Bonferonni correction).

### Annotation 14 (page 6)

Beside the passage: “hypothesis, these assumptions include randomness in sampling, treatment assignment, loss, and missingness, as well as an assumption that the P value was not sel ected for presentation based on its size or some other aspect of the results. 10. If you reject the test hypothesis because P £ 0.05,”

**Annotation** by Stelios Serghiou (2019-02-04):

> Estimating the science-wide false discovery rate is an active area of research (and fight!). The journal Biostatistics published a fantastic issue of heavy-weight names weighing on this topic [here](https://academic.oup.com/biostatistics/issue/15/1). Unfortunately, reproducibility projects in psychology, cancer biology and economics, do not paint a particularly favorable picture for even the most prestigious of studies. This has led to what is known as the "reproducibility crisis."

### Annotation 15 (page 7)

Beside the passage: “populations and the resulting P values are on opposite sides of 0.05, the results are conﬂicting. No! Statistical tests are sensitive to many differences between study populations that are irrelevant to whether their results are in agreement, such as the sizes of compared groups in each population. As a consequence, …”

**Annotation** by Stelios Serghiou (2019-02-04):

> To appropriately combine evidence from more than one study, we need to use a statistical method, NOT compare p-values. The most commonly used such method in medicine is a meta-analysis. One of the famous success stories of meta-ananlyses is the discovery that administering corticosteroids to preterm babies substantially reduces complications; this was in contrast to all individual studies up to that point, which had not provided convincing evidence of such benefit. The main figure of that meta-analysis is now the logo of probably the most well-known consortium for evidence synthesis, Cochrane - more on this [here](https://www.ncbi.nlm.nih.gov/pubmed/16856047).

### Annotation 16 (page 8)

Beside the passage: “21. If two conﬁdence intervals overlap, the difference”

**Annotation** by Stelios Serghiou (2019-02-04):

> This is a misconception I have witnessed time and time again within the biosciences. Even the general guidelines given here, do not apply when comparing groups of very different sample size, which is often the case. The best written article on how to interpret comparisons between standard deviation error bars, standard error error bars and confidence intervals I have found so far, can be found [here](https://www.graphpad.com/support/faq/spanwhat-you-can-conclude-when-two-error-bars-overlap-or-dontspan/).

### Annotation 17 (page 11)

Beside the passage: “Meanwhile, in the hopes of minimizing harms of current practice, we can offer several guidelines for users and readers of statistics, and re-emphasize some key warnings from our list of misinterpretations:”

**Annotation** by Stelios Serghiou (2019-02-04):

> An additional recommendation that has attracted lots of supporters, and enemies, is that we lower the commonly accepted level of significance from 0.05 to 0.005. The paper proposing this change has been signed by some very big names and can be found [here](https://www.nature.com/articles/s41562-017-0189-z). The authors understand this proposal as an interim measure to curtail the "symptoms" of misunderstandings in statistical inference while working on the "cause."

## Full text

Extracted from the PDF. [Annotation N] marks where each annotation above sits.

#### Page 1

ESSAY

Statistical tests, P values, conﬁdence intervals, and power: a guide

to misinterpretations [Annotation 1]

Sander Greenland 1 • Stephen J. Senn 2 • Kenneth J. Rothman 3 • John B. Carlin 4 • Charles Poole 5 • Steven N. Goodman 6 • Douglas G. Altman 7 [Annotation 2]

Received: 9 April 2016 / Accepted: 9 April 2016 / Published online: 21 May 2016  The Author(s) 2016. This article is published with open access at Springerlink.com

Abstract Misinterpretation and abuse of statistical tests, conﬁdence intervals, and statistical power have been decried for decades, yet remain rampant. A key problem is that there are no interpretations of these concepts that are at once simple, intuitive, correct, and foolproof. Instead , correct use and interpretation of these statistics requires an attention to detail which seems to tax the patience of working scientists. This high cognitive demand has led to an epidemic of shortcut deﬁnitions and interpretations that are simply wrong, sometimes disastrously so—and yet these misinterpretations dominate much of the scientiﬁc

literature. In light of this problem, we provide deﬁnitions [Annotation 3] and a discussion of basic statistics that are more general and critical than typically found in traditional introductory expositions. Our goal is to provide a resource for instructors, researchers, and consumers of statistics whose knowledge of statistical theo ry and technique may be limited but who wish to avoid and spot misinterpretations. We emphasize how violation of often unstated analysis protocols (such as selecting analyses for presentation based on the P values they produce) can lead to small P values even if the declared test hypothesis is correct, and can lead to large P values even if that hypothesis is incorrect. We then provide an explanatory list of 25 misinterpretations of P values, conﬁdence intervals, and power. We conclude with guidelines for improving statistical interpretation and [Annotation 4] reporting.

Editor’s note This article has been published online as supplementary material with an article of Wasserstein RL, Lazar NA. The ASA’s statement on p-values: context, process and purpose. The American Statistician 2016.

Albert Hofman, Editor-in-Chief EJE.

& Sander Greenland

lesdomes@ucla.edu Stephen J. Senn stephen.senn@lih.lu John B. Carlin john.carlin@mcri.edu.au Charles Poole cpoole@unc.edu Steven N. Goodman steve.goodman@stanford.edu Douglas G. Altman doug.altman@csm.ox.ac.uk

1 Department of Epidemiology and Department of Statistics, University of California, Los Angeles, CA, USA 2 Competence Center for Methodology and Statistics, Luxembourg Institute of Health, Strassen, Luxembourg

3 RTI Health Solutions, Research Triangle Institute, Research Triangle Park, NC, USA 4 Clinical Epidemiology and Biostatistics Unit, Murdoch Children’s Research Institute, School of Population Health, University of Melbourne, Melbourne, VIC, Australia 5 Department of Epidemiology, Gillings School of Global Public Health, University of North Carolina, Chapel Hill, NC, USA 6 Meta-Research Innovation Center, Departments of Medicine and of Health Research and Policy, Stanford University School of Medicine, Stanford, CA, USA 7 Centre for Statistics in Medicine, Nufﬁeld Department of Orthopaedics, Rheumatology and Musculoskeletal Sciences, University of Oxford, Oxford, UK

123

Eur J Epidemiol (2016) 31:337–350 DOI 10.1007/s10654-016-0149-3

#### Page 2

Keywords Conﬁdence intervals  Hypothesis testing  Null testing  P value  Power  Signiﬁcance tests  Statistical testing

Introduction

Misinterpretation and abuse of statistical tests has been decried for decades, yet remains so rampant that some scientiﬁc journals discourage use of ‘‘statistical signiﬁcance’’ (classifying results as ‘‘signiﬁcant’’ or not based on a P value) [1]. One journal now bans all statistical tests and mathematically related procedures such as conﬁden ce [Annotation 5] intervals [2], which has led to considerable discussion and debate about the merits of such bans [3, 4].

Despite such bans, we expect that the sta tistical methods at issue will be with us for many years to come. We thus think it imperative that basic teaching as well as general understanding of these methods be improved. Toward that end, we attempt to explain the meaning of signiﬁcance tests, conﬁdence intervals, and statistical powe r in a more general and critical way than is traditionally done, and then review 25 common misconceptions in light of our explanations. We also discuss a few more subtle but nonetheless pervasive problems, explaining why it is important to examine and synthesize all results relating to a scientiﬁc question, rather than focus on individual ﬁndings. We further explain why statistical tests should never constitute the sole input to inferences or decisions about associations or effects. Among the many reasons are that, in most sci- [Annotation 7] entiﬁc settings, the arbitrary classiﬁcation of results into ‘‘signiﬁcant’’ and ‘‘non-signiﬁcant’’ is unnecessary for and often dam aging to valid interpretation of data; and that estimation of the size of effects and the uncertainty surrounding our estimates will be far more important for scientiﬁc inference and sound judgment than any such classiﬁcation.

More detailed discussion of the general issues can be found in many articles, chapters, and books on statistical methods and their interpretation [5–20]. Speciﬁc issues are covered at length in these sources and in the many peer-reviewed articles that critique common misinterpretations of null-hypothesis testing and ‘‘statistical signiﬁcance’’ [1, 12, 21–74].

Statistical tests, P values, and conﬁdence intervals: a caustic primer

Statistical models, hypotheses, and tests

Every method of statistical inference depends on a complex web of assumptions about how data were collected and

analyzed, and how the analysis results were selected for presentation. The full set of assumptions is embodied in a statistical model that underpins the method. This model is a mathematical representation of data variability, and thus ideally would capture accurately all sources of such variability. Many problems arise however because this statistical model often incorporates unrealistic or at best unjustiﬁed assumptions. This is true even for so-called ‘‘non-parametric’’ methods, which (like other methods) depend on assumptions of random sampling or randomization. These assumptions are often deceptively simple to write down mathematically, yet in practice are difﬁcult to satisfy and verify, as they may depend on successful completion of a long sequence of actions (such as identifying, contacting, obtaining consent from, obtaining cooperation of, and following up subjects, as well as adherence to study protocol s for treatment allocation, masking, and data analysis).

There is also a serious problem of deﬁning the scope of a model, in that it should allow not only for a good representation of the observed data but also of hypothetical alternative data that might have been observed. The reference frame for data that ‘‘might have been observed’’ is often unclear, for example if multiple outcome measures or multiple predictive factors have been measured, and many [Annotation 6] decisions surrounding analysis choices have been made after the data were collected—as is invariably the case [33].

The difﬁculty of understanding and assessing underlying assumptions is exacerbated by the fact that the statistical model is usually presented in a highly compressed and abstract form—if presented at all. As a result, many assumptions go unremarked and are often unrecognized by users as well as consumers of statistics. Nonetheless, all statistical methods and interpretations are premised on the model assumptions; that is, on an assumption that the model provides a valid representation of the variation we would expect to see across data sets, faithfully reﬂecting the circumstances surrounding the study and phenomena occurring within it.

In most applications of statistical testing, one assumption in the model is a hypothesis that a particular effect has a speciﬁc size, and has been targeted for statistical analysis. (For simplicity, we use the word ‘‘effect’’ when ‘‘association or effect’’ would arguably be better in allowing for noncausal studies such as most surveys.) This targeted assumption is called the study hypothesis or test hypothesis, and the stati stical methods used to evaluate it are called statistical hypothesis tests. Most often, the targeted effect size is a ‘‘null’’ value representing zero effect (e.g., that the study treatment makes no difference in average outcome), in which case the test hypothesis is called the null hypothesis. Nonetheless, it is als o possible to test other

338 S. Greenland et al.

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effect sizes. We may also test hypot heses that the effect does or does not fall within a speciﬁc range; for example, we may test the hypothesis that the effect is no greater than a particular amount, in which case the hypothesis is said to be a one-sided or dividing hypothesis [7, 8].

Much statistical teaching and practice has developed a strong (and unhealthy) focus on the idea that the main aim of a study should be to test null hypotheses. In fact most descriptions of statistical testing focus only on testing null hypotheses, and the entire topic has been called ‘‘Null Hypothesis Signiﬁcance Testing’’ (NHST). This exclusive focus on null hypotheses contributes to misunderstanding of tests. Adding to the misunderstanding is that many authors (including R.A. Fisher) use ‘‘null hypothesis’’ to [Annotation 8] refer to any test hypothesis, even though this usage is at odds with other authors and with ordinary English deﬁnitions of ‘‘null’’—as are statistical usages of ‘‘signiﬁcance’’ and ‘‘conﬁdence.’’

Uncertainty, probability, and statistical signiﬁcance

A more reﬁned goal of statistical anal ysis is to provide an evaluation of certainty or uncertainty regarding the size of an effect. It is natural to express such certainty in terms of ‘‘probabilities’’ of hypotheses. In conventional statistical methods, however, ‘‘probability’’ refers not to hypotheses, but to quantities that are hypothetical frequencies of data patterns under an assumed statistical model. These methods are thus calle d frequentist methods, and the hypothetical frequencies they predict are called ‘‘frequency probabilities.’’ Despite considerable training to the contrary, many statistically educated scientists revert to the habit of misinterpreting these frequency probabilities as hypothesis probabilities. (Even more confusingly, the term ‘‘likelihood of a parameter value’’ is reserved by statisticians to refer to the probability of the observed data given the parameter value; it does not refer to a probability of the parameter taking on the given value.)

Nowhere are these problems more rampant than in applications of a hypothetical frequency called the P value, [Annotation 10] also known as the ‘‘observed signiﬁcance level’’ for the test hypothesis. Statistical ‘‘signiﬁcance tests’’ based on this concept have been a central part of statistical analyses for centuries [75]. The focus of traditional deﬁnitions of P values and statistical signiﬁcance has been on null hypotheses, treating all other assumptions used to com pute the P value as if they were known to be correct. Recognizing that these other assumptions are often questionable if not unwarranted, we will adopt a more general view of the P value as a statistical summary of the compatibility between the observed data and what we would predict or expect to see if we knew the entire statistical model (all the assumptions used to compute the P value) were correct.

Speciﬁcally, the distance between the data and the model prediction is measured using a test statistic (such as a t-statistic or a Chi squared statistic). The P value is then the probability that the chosen test statistic would have been at least as large as its observed value if every model assumption were correct, including the test hypothesis. This deﬁnition embodies a crucial point lost in traditional deﬁnitions: In logical terms, the P value tests all the assumptions about how the data were generated (the entire model), not just the targeted hypothesis it is supposed to test (such as a null hypothesis). Furthermore, these assumptions include far more than what are traditionally presented as modeling or probability assumptions—they include assumptions about the conduct of the analysis, for example that intermediate analysis results were not used to determine which analyses would be presented. [Annotation 9]

It is true that the smaller the P value, the more unusual the data would be if every single assumption were correct; but a very small P value does not tell us which assumption is incorrect. For example, the P value may be very small because the targeted hypothesis is false; but it may instead (or in addition) be very small because the study protocols were violated, or because it was selected for pres entation based on its small size. Convers ely, a large P value indicates only that the data are not unusual under the model, but does not imply that the model or any aspect of it (such as the targeted hypothesis) is correct; it may instead (or in addition) be large becau se (again) the study protocols were violated, or because it was selected for presentation based on its large size.

The general deﬁnition of a P value may help one to understand why statistical tests tell us much less than what many think they do: Not only does a P value not tell us whether the hypothesis targeted for testing is true or not; it says nothing speciﬁcally related to that hypothesis unless we can be completely assured that every other assumption used for its computation is correct—an assurance that is lacking in far too many studies.

Nonetheless, the P value can be viewed as a continuous measure of the compatibility between the data and the entire model used to compute it, ranging from 0 for complete incompatibility to 1 for perf ect compatibility, and in this sense may be viewed as measuring the ﬁt of the model to the data. Too often, however, the P value is degraded into a dichotomy in which results are declared ‘‘statistically signiﬁcant’’ if P falls on or below a cut-off (usually 0.05) and declared ‘‘nonsigniﬁcant’’ otherwise. The terms ‘‘signiﬁcance level’’ and ‘‘alpha level’’ (a) are often used to refer to the cut-off; however, the term ‘‘signiﬁcance level’’ invites confusion of the cut-off with the P value itself. Their difference is profound: the cut-off value a is supposed to be ﬁxed in advance and is thus part of the study design, unchanged in light of the data. In contrast, the

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P value is a number computed from the data and thus an analysis result, unknown until it is computed.

Moving from tests to estimates

We can vary the test hypothesis while leaving other assumptions unchanged, to see how the P value differs across competing test hypotheses. Usually, these test hypotheses specify different sizes for a targeted effect; for example, we may test the hypothesis that the average difference between two treatment groups is zero (the null hypothesis), or that it is 20 or -10 or any size of interest. The effect size whose test produced P = 1 is the size most compatible with the data (in the sense of predicting what was in fact observed) if all the othe r assumptions used in the test (the statistical model) were correct, and provides a point estimate of the effect under those assumptions. The effect sizes whose test produced P [ 0.05 will typically deﬁne a range of sizes (e.g., from 11.0 to 19.5) that would be considered more compatible with the data (in the sense of the observations being closer to what the model predicted) than sizes outside the range—again, if the statistical model were correct. This range corresponds to a 1 - 0.05 = 0.95 or 95 % conﬁdence interval, and provides a convenient way of summarizing the results of hypothesis tests for many effect sizes. Conﬁdence int ervals are examples of interval estimates.

Neyman [76] proposed the construction of conﬁdence intervals in this way because they have the following property: If one calculates, say, 95 % conﬁdence intervals repeatedly in valid applications, 95 % of them, on average, will contain (i.e., include or cover) the true effect size. Hence, the speciﬁed conﬁdence level is called the coverage probability. As Neyman stressed repeatedly, this coverage probability is a property of a long sequence of conﬁdence intervals computed from valid models, rather than a property of any single conﬁden ce interv al.

Many journals now require conﬁdence intervals, but most textbooks and studies discuss P values only for the null hypothesis of no effect. This exclusive focus on null hypotheses in testing not only contributes to misunderstanding of tests and underappreciation of estimation, but also obscures the close relationship between P values and conﬁdence intervals, as well as the weaknesses they share.

What P values, conﬁdence intervals, and power calculations don’t tell us

Much distortion arises from basic misunderstanding of what P values and their relatives (such as conﬁdence intervals) do not tell us. Therefore, based on the articles in our reference list, we review prevalent P value

misinterpretations as a way of moving toward defensi ble interpretations and presentations. We adopt the format of Goodman [40] in providing a list of misinterpretations that [Annotation 11] can be used to critically evaluate conclusions offered by research reports and reviews. Every one of the bolded statements in our list has contributed to statistical distortion of the scientiﬁc literature, and we add the emphatic ‘‘No!’’ to underscore statements that are not only fallacious but also not ‘‘true enough for practical purposes.’’

Common misinterpretations of single P values [Annotation 12]

1. The P value is the probability that the test

hypothesis is true; for example, if a test of the null hypothesis gave P = 0.01, the null hypothesis has only a 1 % chance of being true; if instead it gave P = 0.40, the null hypothesis has a 40 % chance of being true. No! The P value assumes the test hypothesis is true—it is not a hypothesis probability and may be far from any reasonable probability for the test hypot hesis. The P value simply indicates the degree to which the data conform to the pattern predicted by the test hypothesis and all the other assumptions used in the test (the underlying statistical model). Thus P = 0.01 would indicate that the data are not very close to what the statistical mode l (including the test hypothesis) predicted they should be, while P = 0.40 would indicate that the data are much closer to the model prediction, allowing for chance variation . 2. The P value for the null hypothesis is the probability

that chance alone produced the observed assoc iation; for example, if the P value for the null hypothesis is 0.08, there is an 8 % probability that chance alone produced the association. No! This is a common variation of the ﬁrst fallacy and it is just as false. To say that chance alone produced the observed association is logically equivalent to asserting that every assumption used to compute the P value is correct, including the null hypothesis. Thus to claim that the null P value is the probability that chance alone produced the observed association is completely backwards: The P value is a probability computed assuming chance was operating alone. The absurdity of the common backwards interpretation might be appreciated by pondering how the P value, which is a probability deduced from a set of assumptions (the statistical model), can possibly refer to the probability of those assumptions. Note: One often sees ‘‘alone’’ dropped from this description (becoming ‘‘the P value for the null hypothesis is the probability that chance produced the observed association’’), so that the statement is more ambiguous, but just as wrong.

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3. A signiﬁcant test result (P £ 0.05) means that the

test hypothesis is false or should be rejected. No! A small P value simply ﬂags the data as being unusual if all the assumptions used to compute it (including the test hypothesis) were correct; it may be small because there was a large random error or because some assumption other than the test hypothesis was violated (for example, the assumption that this P value was not selected for presentation because it was below 0.05). P B 0.05 only means that a discrepancy from the hypothesis prediction (e.g., no difference between treatment groups) would be as large or larger than that observed no more than 5 % of the time if only chance were creating the discrepancy (as opposed to a violation of the test hypothesis or a mistaken assumption). 4. A nonsigniﬁcant test result (P > 0.05) means that

the test hypothes is is true or should be accepted. No! A large P value only suggests that the data are not unusual if all the assumptions used to compute the P value (including the test hypothesis) were correct. The same data would also not be unusual under many other hypotheses. Furthermore, even if the test hypothesis is wrong, the P value may be large because it was inﬂated by a large random error or because of some other erroneous assumption (for example, the assumption that this P value was not selected for presentation because it was above 0.05). P [ 0.05 only mea ns that a discrepancy from the hypothesis prediction (e.g., no difference between treatment groups) would be as large or larger than that observed more than 5 % of the time if only chance were creating the discrepancy. 5. A large P value is evidence in favor of the test

hypothesis. No! In fact, any P value less than 1 implies that the test hypothesis is not the hypothesis most compatible with the data, because any other hypothesis with a larger P value would be even more compatible with the data. A P value cannot be said to favor the test hypothesis except in relation to those hypotheses with smaller P values. Furthermore, a large P value often indicates only that the data are incapable of discriminating among many competing hypotheses (as would be seen immediately by examining the range of the conﬁdence interval). For example, many authors will misinterpret P = 0.70 from a test of the null hypothesis as evidence for no effect, when in fact it indicates that, even though the null hypothesis is compatible with the data under the assumptions used to compute the P value, it is not the hypothesis most compatible with the data—that honor would belong to a hypothesis with P = 1. But even if P = 1, there

will be many other hypotheses that are highly consistent with the data, so that a deﬁnitive conclusion of ‘‘no association’’ cannot be deduced from a P value, no matter how large. 6. A null-hyp othesis P value greater than 0.05 means

that no effect was observed, or that absence of an effect was shown or demonstrated. No! Observing P [ 0.05 for the null hypothesis only means that the null is one among the many hypotheses that have P [ 0.05. Thus, unless the point estimate (observed association) equals the null value exactly, it is a mistake to conclude from P [ 0.05 that a study found ‘‘no association’’ or ‘‘no evidence’’ of an effect. If the null P value is less than 1 some association must be present in the data, and one must look at the point estimate to determine the effect size most compatible with the data under the assumed model. 7. Statistical signiﬁcance indicates a scientiﬁcally or

substantively important relation has been detected. No! Especially when a study is large, very minor effects or small assumption violations can lead to statistically signiﬁcant tests of the null hypot hesis. [Annotation 13] Again, a small null P value simply ﬂags the data as being unusual if all the assumptions used to compute it (including the null hypothesis) were correct; but the way the data are unusual might be of no clinical interest. One must look at the conﬁdence interval to determine which effect sizes of scient iﬁc or other substantive (e.g., clinical) importanc e are relatively compatible with the data, given the model. 8. Lack of statistical signiﬁcance indicates that the

effect size is small. No! Especially when a study is small, even large effects may be ‘‘drowned in noise’’ and thus fail to be detected as statistically signiﬁcant by a statistical test. A large null P value simply ﬂags the data as not being unusual if all the assumptions used to compute it (including the test hypothesis) were correct; but the same data will also not be unusual under many other models and hypotheses besides the null. Again, one must look at the conﬁdence interval to determine whether it includes effect sizes of importance. 9. The P value is the chance of our data occurring if

the test hypothesis is true; for example, P = 0.05 means that the observed association would occur only 5 % of the time under the test hypothesis. No! The P value refers not only to what we observed, but also observations more extreme than what we observed (where ‘‘extremity’’ is measured in a particular way). And again, the P value refers to a data frequency when all the assumptions used to compute it are correct. In addition to the test

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hypothesis, these assumptions include randomness in sampling, treatment assignment, loss, and missingness, as well as an assumption that the P value was not sel ected for presentation based on its size or some other aspect of the results. 10. If you reject the test hypothesis because P £ 0.05, [Annotation 14]

the chance you are in error (the chance your ‘‘signiﬁcant ﬁnding’’ is a false positive) is 5 %.No! To see why this description is false, suppose the test hypothesis is in fact true. Then, if you reject it, the chance you are in error is 100 %, not 5 %. The 5 % refers only to how often you would reject it, and therefore be in error, over very many uses of the test across different studies when the test hypothesis and all other assumptions used for the test are true. It does not refer to your single use of the test, which may have been thrown off by assumption violations as well as random errors. This is yet another version of misinterpretation #1. 11. P = 0.05 and P £ 0.05 mean the same thing. No!

This is like saying reported height = 2 m and reported height B2 m are the same thing: ‘‘height = 2 m’’ would include few people and those people would be considered tall, whereas ‘‘height B2 m’’ would include most people including small children. Similarly, P = 0.05 would be considered a borderline result in terms of statistical signiﬁcance, whereas P B 0.05 lumps borderline results together with results very incompatible with the model (e.g., P = 0.0001) thus rendering its meaning vague, for no good purpose. 12. P values are properly reported as inequalities (e.g.,

report ‘‘P < 0.02’’ when P = 0.015 or report ‘‘P > 0.05’’ when P = 0.06 or P = 0.70). No! This is bad practice because it makes it difﬁcult or impossible for the reader to accurately interpret the statistical result. Only when the P value is very small (e.g., under 0.001) does an inequality become justiﬁable: There is little practical difference among very small P values when the assumptions used to compute P values are not known with enough certainty to justify such precision, and most methods for computing P values are not numerically accurate below a certain point. 13. Statistical signiﬁcance is a property of the phe-

nomenon being studied, and thus statistical tests detect signiﬁcance. No! This misinterpretation is promoted when researcher s state that they have or have not found ‘‘evidence of’’ a statistically sign iﬁcant effect. The effect being tested either exists or does not exist. ‘‘Statistical signiﬁcance’’ is a dichotomous description of a P value (that it is below the chosen cut-off) and thus is a property of a result of a statistical test; it is not a property of the effect or population being studied.

14. One should always use two-sided P values. No! Two-sided P values are designed to test hypotheses that the targeted effect measure equals a speciﬁc value (e.g., zero), and is neither above nor below this value. When, however, the test hypothesis of scientiﬁc or practical interest is a one-sided (dividing) hypothesis, a onesided P value is appropriate. For example, consider the practical question of whether a new drug is at least as good as the standard drug for increasing survival time. This question is one-sided, so testing this hypothesis calls for a one-sided P value. Nonetheless, because two-sided P values are the usual default, it will be important to note when and why a one-sided P value is being used instead.

There are other interpretations of P values that are controversial, in that whether a categorical ‘‘No!’’ is warranted depends on one’s philosophy of statistics and the precise meaning given to the terms involved. The disputed claims deserve recognition if one wishes to avoid such controversy.

For example, it has been argued that P values overstate evidence against test hypotheses, based on directly comparing P values against certain quantities (likelihood ratios and Bayes factors) that play a central role as evidence measures in Bayesian analysis [37, 72, 77–83]. Nonetheless, many other statisticians do not accept these quant ities as gold standards, and instead point out that P values summarize crucial evidence needed to gauge the error rates of decisions based on statistical tests (even though they are far from sufﬁcient for making those decisions). Thus, from this frequentist perspective, P valu es do not overstate evidence and may even be considered as measuring one aspect of evidence [7, 8, 84–87], with 1 - P measuring evidence against the model used to compute the P value. See also Murtaugh [ 88] and its accompanying discussion.

Common misinterpretations of P value comparisons and predictions

Some of the most severe distortions of the scientiﬁc literature produced by statistical testing involve erroneous comparison and synthesis of results from different studies or study subgroups. Among the worst are:

15. When the same hypothesis is tested in different

studies and none or a minority of the tests are statistically signiﬁcant (all P > 0.05), the overall evidence supports the hypothesis. No! This belief is often used to claim that a literature supports no effect when the opposite is case. It reﬂects a tendency of researchers to ‘‘overestimate the power of most research’’ [89]. In reality, every study could fail to reach statistical signiﬁcance and yet when combined

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show a statistically signiﬁcant association and persuasive evidence of an effect. For example, if there were ﬁve studies each with P = 0.10, none would be signiﬁcant at 0.05 level; but when these P values are combined using the Fisher formula [9], the overall P value would be 0.01. There are many real examples of persuasive evidence for important effects when few studies or even no study reported ‘‘statistically significant’’ associations [90, 91]. Thus, lack of statistical signiﬁcance of individual studies should not be taken as implying that the totality of evidence supports no effect. 16. When the same hypothesis is tested in two different

populations and the resulting P values are on [Annotation 15] opposite sides of 0.05, the results are conﬂicting. No! Statistical tests are sensitive to many differences between study populations that are irrelevant to whether their results are in agreement, such as the sizes of compared groups in each population. As a consequence, two studies may provide very different P values for the same test hypothesis and yet be in perfect agreement (e.g., may show identical observed associations). For example, suppose we had two randomized trials A and B of a treatment, identical except that trial A had a known standard error of 2 for the mean difference between treatment groups whereas trial B had a known standard error of 1 for the difference. If both trials observed a difference between treatment groups of exactly 3, the usual normal test would produce P = 0.13 in A but P = 0.003 in B. Despite their difference in P values, the test of the hypothesis of no difference in effect across studies would have P = 1, reﬂecting the perfect agreement of the observed mean differences from the studies. Differences between results must be evaluated by directly, for example by estimating and testing those differences to produce a conﬁden ce interval and a P value comparing the results (often called analysis of heterogeneity, interaction, or modiﬁcation). 17. When the same hypothesis is tested in two different

populations and the same P values are obtained, the results are in agreement. No! Again, tests are sensitive to many differences between populations that are irrelevant to whether their results are in agreement. Two different studies may even exhibit identical P values for testing the same hypothesis yet also exhibit clearly different observed associations. For example, suppose randomized experiment A observed a mean difference between treatment groups of 3.00 with standard error 1.00, while B observed a mean difference of 12.00 with standard error 4.00. Then the standard normal test would produce P = 0.003 in both; yet the test of the hypothesis

of no difference in effect across studies gives P = 0.03, reﬂecting the large difference (12.00 - 3.00 = 9.00) between the mean differences. 18. If one observ es a small P value, there is a good

chance that the next study will produce a P value at least as small for the same hypothesis. No! This is false even under the ideal condition that both studies are independent and all assumptions including the test hypothesis are correct in both studies. In that case, if (say) one observes P = 0.03, the chance that the new study will show P B 0.03 is only 3 %; thus the chance the new study will show a P value as small or smaller (the ‘‘replication probability’’) is exactly the observed P value! If on the other hand the small P value arose solely because the true effect exactly equaled its observed estimate, there would be a 50 % chance that a repeat experiment of identical design would have a larger P value [37]. In general, the size of the new P value will be extremely sensitive to the study size and the extent to which the test hypothesis or other assumptions are violated in the new study [86]; in particular, P may be very small or very large depending on whether the study and the violations are large or small.

Finally, although it is (we hope obviously) wrong to do so, one sometimes sees the null hypothesis compared with another (alternative) hypothesis using a two-sided P value for the null and a one-sided P value for the alternative. This comparison is biased in favor of the null in that the twosided test will falsely reject the null only half as often as the one-sided test will falsely reject the alternative (again, under all the assumptio ns used for testing).

Common misinterpretations of conﬁdence intervals

Most of the above misinterpr etations translate into an analogous misinterpretation for conﬁdence intervals. For example, another misinterpretation of P [ 0.05 is that it means the test hypothesis has only a 5 % chance of being false, which in terms of a conﬁdence interval becomes the common fallacy:

19. The speciﬁc 95 % conﬁdence interval presented by

a study has a 95 % chance of containing the true effect size. No! A reported conﬁdence interval is a range between two numbers. The frequency with which an observed interval (e.g., 0.72–2.88) contains the true effect is either 100 % if the true effect is within the interval or 0 % if not; the 95 % refers only to how often 95 % conﬁdence intervals computed from very many studies would contain the true size if all the assumptions used to compute the intervals were correct.Itispossibleto compute an interval that can be interpreted as having

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95 % probability of containing the true value; nonetheless, such computations require not only the assumptions used to compute the conﬁdence interval, but also further assumptions about the size of effects in the model. These further assumptions are summarized in what is called a prior distribution, and the resulting intervals are usually called Bayesian posterior (or credible) intervals to distinguish them from conﬁdence intervals [18]. Symmetrically, the misinterpretation of a small P value as disproving the test hypothesis could be translated into:

20. An effect size outside the 95 % conﬁdence interval

has been refuted (or excluded) by the data. No! As with the P value, the conﬁdence interval is computed from many assumptions, the violation of which may have led to the results. Th us it is the combination of the data with the assumptions, along with the arbitrary 95 % criterion, that are needed to declare an effect size outside the interval is in some way incompa tible with the observations. Even then, judgements as extreme as saying the effect size has been refuted or excluded will require even stronger conditions. As with P values, naı ¨ ve comparison of conﬁdence intervals can be highly misleading:

21. If two conﬁdence intervals overlap, the difference [Annotation 16]

between two estimates or studies is not signiﬁcant. No! The 95 % conﬁdence intervals from two subgroups or studies may overlap substantially and yet the test for difference between them may still produce P \ 0.05. Suppose for example, two 95 % conﬁdence intervals for means from normal populations with known variances are (1.04, 4.96) and (4.16, 19.84); these intervals overlap, yet the test of the hypothesis of no difference in effect acrossstudies gives P = 0.03. As with P values, comparison between groups requires statistics that directly test and estimate the differences across groups. It can, however, be noted that if the two 95 % conﬁdence intervals fail to overlap, then when using the same assumptions used to compute the conﬁdence intervals we will ﬁnd P \ 0.05 for the difference; and if one of the 95 % intervals contains the point estimate from the other group or study, we will ﬁnd P [ 0.05 for the difference. Finally, as with P values, the replication properties of conﬁdence intervals are usually misunderstood:

22. An observed 95 % conﬁdence interval predicts

that 95 % of the estimates from future studies will fall inside the observed interval. No! This statement is wrong in several ways. Most importantly, under the model, 95 % is the frequency with which other unobserved intervals will contain the true effect, not how fre quently the one interval being presented will contain future estimates. In fact, even under ideal

conditions the chance that a future estimate will fall within the current interval will usually be much less than 95 %. For example, if two independent studies of the same quantity provide unbiased normal point estimates with the same standard errors, the chance that the 95 % conﬁdence interval for the ﬁrst study contains the point estimate from the second is 83 % (which is the chance that the difference between the two estimates is less than 1.96 standard errors). Again, an observed interval either does or does not contain the true effect; the 95 % refers only to how often 95 % conﬁdence intervals computed from very many studies would contain the true effect if all the assumpt ions used to compute the intervals were correct. 23. If one 95 % conﬁdence interval includes the null

value and another excludes that value, the interval excluding the null is the more precise one.No! When the model is correct, precision of statistical estimation is measured directly by conﬁdence interval width (measured on the appropriate scale). It is not a matter of inclusion or exclusion of the null or any other value. Consider two 95 % conﬁdence intervals for a difference in means, one with limits of 5 and 40, the other with limits of -5 and 10. The ﬁrst interval excludes the null value of 0, but is 30 units wide. The second includes the null value, but is half as wide and therefore much more precise.

In addition to the above misinterpretations, 95 % conﬁdence intervals force the 0.05-level cutoff on the reader, lumping together all effect sizes with P [ 0.05, and in this way are as bad as presenting P values as dichotomies. Nonetheless, many authors agree that conﬁdence intervals are superior to tests and P values because they allow one to shift focus away from the null hypothesis, toward the full range of effect sizes compatible with the data—a shift recommended by many authors and a growing number of journals. Another way to bring attention to non-null hypotheses is to present their P values; for example, one could provide or demand P values for those effect sizes that are recognized as scientiﬁcally reasonable alternatives to the null.

As with P values, further cautions are needed to avoid misinterpreting conﬁdence intervals as providing sharp answers when none are warranted. The hypothesis which says the point estimate is the correct effect will have the largest P value (P = 1 in most cases), and hypotheses inside a conﬁdence interval will have higher P values than hypotheses outside the interval. The P values will vary greatly, however, among hypotheses inside the interval, as well as among hypotheses on the outside. Also, two hypotheses may have nearly equal P values even though one of the hypotheses is inside the interval and the other is outside. Thus, if we use P valu es to measure compatibility of

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hypotheses with data and wish to compare hypotheses with this measure, we need to examine their P values directly, not simply ask whether the hypotheses are inside or outside the interval. This need is particularly acute when (as usual) one of the hypotheses under scrutiny is a null hypothesis.

Common misinterpretations of power

The power of a test to detect a correct alternative hypothesis is the pre-study probability that the test will reject the test hypothesis (e.g., the probability that P will not exceed a pre-speciﬁed cut-off such as 0.05). (The corresponding pre-study probability of failing to reject the test hypothesis when the alternative is correct is one minus the power, also known as the Type-II or beta error rate) [84] As with P values and conﬁdence intervals, this p robability is deﬁned over repetitions of the same study design and so is a frequency probability. One source of reasonable alternative hypotheses are the effect sizes that were used to compute power in the study proposal. Pre-study power calculations do not, howe ver, measure the compatibility of these alternatives with the data actually observed, while power calculated from the observed data is a direct (if obscure) transformation of the null P value and so provides no test of the alternatives. Thus, presentation of power does not obvia te the need to provide interval estimates and direct tests of the alternatives.

For these reasons, many authors have condemned use of power to interpret estimates and statistical tests [42, 92– 97], arguing that (in contrast to conﬁdence intervals) it distracts attention from direct comparisons of hypotheses and introduces new misinterpretations, such as:

24. If you accept the null hypothesis because the null

P value exceeds 0.05 and the power of your test is 90 %, the chance you are in error (the chance that your ﬁnding is a false negative) is 10 %. No! If the null hypot hesis is false and you accept it, the chance you are in error is 100 %, not 10 %. Conversely, if the null hypothesis is true and you accept it, the chance you are in error is 0 %. The 10 % refers only to how often you would be in error over very many uses of the test across different studies when the particular alternative used to compute power is correct and all other assumptions used for the test are correct in all the studies. It does not refer to your single use of the test or your error rate under any alternative effect size other than the one used to compute power. It can be especially misleading to compare results for two hypotheses by presenting a test or P value for one and power for the other. For example, testing the null by seeing whether P B 0.05 with a power less than 1 - 0.05 = 0.95 for the alternative (as done routinely) will bias the comparison in

favor of the null because it entails a lower probability of incorrectly rejecting the null (0.05) than of incorrectly accepting the null when the alternative is correct. Thus, claims about relative support or evidence need to be based on direct and comparable measures of support or evidence for both hypotheses, otherwise mistakes like the following will occur:

25. If the null P value exceeds 0.05 and the power of this

test is 90 % at an alternative, the results support the null over the alternative. This claim seems intuitive to many, but counterexamples are easy to construc t in which the null P valu e is between 0.05 and 0.10, and yet there are alternatives whose own P value exceeds 0.10 and for which the power is 0.90. Parallel results ensue for other accepted measures of compatibility, evidence, and support, indicating that the data show lower compatibility with and more evidence against the null than the alternative, despite the fact that the null P value is ‘‘not signiﬁcant’’ at the 0.05 alpha level and the power against the alternative is ‘‘very high’’ [42].

Despite its shortcomings for interpreting current data, power can be useful for designing studies and for understanding why replication of ‘‘statistical signiﬁcance’’ will often fail even under ideal conditions. Studies are often designed or claimed to have 80 % power against a key alternative when using a 0.05 signiﬁcance level, although in execution often have less powe r due to unanticipated problems such as low subject recruitment. Thus, if the alternative is correct and the actual power of two studies is 80 %, the chance that the studies will both show P B 0.05 will at best be only 0.80(0.80) = 64 %; furthermore, the chance that one study shows P B 0.05 and the othe r does not (and thus will be misinterpreted as showing conﬂicting results) is 2(0.80)0.20 = 32 % or about 1 chance in 3. Similar calculations taking account of typical problems suggest that one could anticipate a ‘‘replication crisis’’ even if there were no publication or reporting bias, simply because current design and testing conventions treat individual study results as dich otomous outputs of ‘‘si gniﬁcant’’/‘‘nonsigniﬁcant’’ or ‘‘reject’’/‘‘accept.’’

A statistical model is much more than an equation with Greek letters

The above list could be expanded by reviewing the research literature. We will however now turn to direct discussion of an issue that has been receiving more attention of late, yet is still widely overlooked or interpreted too narrowly in statistical teaching and presentations: That the statistical model used to obtain the results is correct.

Too often, the full statistical model is treated as a simple regression or structural equation in which effects are

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represented by parameters denoted by Greek letters. ‘‘Model checking’’ is then limited to tests of ﬁt or testing additional terms for the model. Yet these tests of ﬁt themselves make further assumptions that should be seen as part of the full model. For example, all common tests and conﬁdence intervals depend on assumptions o f random selection for observation or treatment and random loss or missingness within levels of controlled covariates. These assumptions have gradually come under scrutiny via sensitivity and bias analysis [98], but such methods remain far removed from the basic statistical training given to most researchers.

Less often stated is the even more crucial assumption that the analyses themselves were not guided toward ﬁnding nonsigniﬁcance or signiﬁcance (analysis bias), and that the analysis results were not reported based on their nonsigniﬁcance or signiﬁcance (reporting bias and publication bias). Selective reporting renders false even the limited ideal meanings of statistical signiﬁcance, P values, and conﬁdence intervals. Because author decisions to report and editorial decisions to publish results often depend on whether the P value is above or below 0.05, selective reporting has been identiﬁed as a major probl em in large segments of the scientiﬁc literature [99–101 ].

Although this selection problem has also been subject to sensitivity analysis, there has been a bias in studies of reporting and publication bias: It is usually assumed that these biases favor signiﬁcance. This assumption is of course correct when (as is often the case) researchers select results for presentation when P B 0.05, a practice that tends to exaggerate associations [101–105]. Nonetheless, bias in favor of reporting P B 0.05 is not always plausible let alone supported by evidence or common sense. For example, one might expect selection for P [ 0.05 in publications funded by those with stakes in acceptance of the null hypothesis (a practice which tends to understate associations); in accord with that expectation, some empirical studies have observed smaller estimates and ‘‘nonsigniﬁcance’’ more often in such publications than in other studies [101, 106, 107].

Addressing such problems would require far more political will and effort than addressing misinterpretation of statistics, such as enforcing registration of trials, along with open data and analysis code from all completed studies (as in the AllTrials initiative, http://www.alltrials.net/). In the meantime, readers are advised to consider the entire context in which research reports are produced and appear when interpreting the statistics and conclusions offered by the reports.

Conclusions

Upon realizing that statistical tests are usually misinterpreted, one may wonder wha t if anything these tests do for science. They were originally intended to account for

random variability as a source of error, thereby sounding a note of caution against overinterpretation of observed associations as true effects or as stronger evidence against null hypotheses than was warranted. But before long that use was turned on its head to provide fallacious support for null hypotheses in the form of ‘‘failure to achieve’’ or ‘‘failure to attain’’ statistical signiﬁcance.

We have no doubt that the founders of modern statistical testing would be horriﬁed by common treatments of their invention. In their ﬁrst paper describing their binary approach to statistical testing, Neyman and Pearson [108] wrote that ‘‘it is doubtful whether the knowledge that [a P value] was really 0.03 (or 0.06), rather than 0.05…would in fact ever modify our judgment’’ and that ‘‘The tests themselves give no ﬁnal verdict, but as tools help the worker who is using them to form his ﬁnal decision.’’ Pearson [109] later added, ‘‘No doubt we could more aptly have said, ‘his ﬁnal or provisional decision.’’’ Fisher [110] went further, saying ‘‘No scientiﬁc worker has a ﬁxed level of signiﬁcance at which from year to year, and in all circumstances, he rejects hypotheses; he rather gives his mind to each particular case in the light of his evidence and his ideas.’’ Yet fallacious and ritualistic use of tests continued to spread, including beliefs that whether P was above or below 0.05 was a universal arbiter of discovery. Thus by 1965, Hill [111] lamented that ‘‘too often we weaken our capacity to interpret data and to take reasonable decisions whatever the value of P. And far too often we deduce ‘no difference’ from ‘no signiﬁcant difference.’’’

In response, it has been argued that some misinterpretations are harmless in tightly controlled experiments on well-understood systems, where the test hypothesis may have special support from established theories (e.g., Mendelian genetics) and in which every other assumption (such as random allocation) is forced to hold by careful design and execution of the study. But it has long been asserted that the harms of statistical testing in more uncontrollable and amorphous research settings (such as social-science, health, and medical ﬁelds) have far outweighed its beneﬁts, leading to calls for banning such tests in research reports— again with one journal banning P values as well as conﬁdence intervals [2].

Given, however, the deep entrenchment of statistical testing, as well as the absence of generally accepted alternative methods, there have been many attempts to salvage P values by detaching them from their use in signiﬁcance tests. One approach is to focus on P values as continuous measures of compatibility, as described earlier. Although this approach has its own limitations (as described in points 1, 2, 5, 9, 15, 18, 19), it avoids comparison of P values with arbitrary cutoffs such as 0.05, (as described in 3, 4, 6–8, 10–13, 15, 16, 21 and 23–25). Another approach is to teach and use correct relations of P values to

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hypothesis probabilities. For exampl e, under common statistical models, one-sided P values can provide lower bounds on probabilities for hypotheses about effect directions [45, 46, 112, 113]. Whether such reinterpretations can eventually replace common misinterpretations to good effect remains to be seen.

A shift in emphasis from hypothesis testing to estimation has been promoted as a simple and relatively safe way to improve practice [5, 61, 63, 114, 115] resulting in increasing use of conﬁdence intervals and editorial demands for them; nonetheless, this shift has brought to the fore misinterpretations of intervals such as 19–23 above [116]. Other approaches com bine tests of the null with further calculations involving both null and alternative hypotheses [117, 118]; such calculations may, however, may bring with them further misinterpretations similar to those described above for power, as well as greater complexity.

Meanwhile, in the hopes of minimizing harms of current [Annotation 17] practice, we can offer several guidelines for users and readers of statistics, and re-emphasize some key warnings from our list of misinterpretations:

(a) Correct and careful interpretation of statistical tests

demands examining the sizes of effect est imates and conﬁdence limits, as well as precise P values (not just whether P values are above or below 0.05 or some other threshold). (b) Careful interpretation also demands critical exami-

nation of the assumptions and conventions used for the statistical analysis—not just the usual statistical assumptions, but also the hidden assumptions about how results were generated and chosen for presentation. (c) It is simply false to claim that statistically non-

signiﬁcant results support a test hypothesis, because the same results may be even more compatible with alternative hypotheses—even if the power of the test is high for those alternatives. (d) Interval estimates aid in evaluating whether the data

are capable of discriminating among various hypotheses about effect sizes, or whether statistical results have been misrepresented as supporting one hypothesis when those results are better explained by other hypotheses (see points 4–6). We caution however that conﬁdence intervals are often only a ﬁrst step in these tasks. To compare hypotheses in light of the data and the statistical model it may be necessary to calculate the P value (or relative likelihood) of each hypothesis. We further caution that conﬁdence intervals provide only a best-case measure of the uncertainty or ambiguity left by the data, insofar as they depend on an uncertain statistical model.

(e) Correct statistical evaluation of multiple studies

requires a pooled analysis or meta-analysis that deals correctly with study biases [68, 119–125]. Even when this is done, however, all the earlier cautions apply. Furthermore, the outcome of any statistical procedure is but one of many considerations that must be evaluated when examining the totality of evidence. In particular, statistical signiﬁcance is neither necessary nor sufﬁcient for determining the scientiﬁc or practical signiﬁcance of a set of observations. This view was afﬁrmed unanimously by the U.S. Supreme Court, (Matrixx Initiatives, Inc., et al. v. Siracusano et al. No. 09–1156. Argued January 10, 2011, Decided March 22, 2011), and can be seen in our earlier quotes from Neyman and Pearson. (f) Any opinion offered about the probability, likeli-

hood, certainty, or similar property for a hypothesis cannot be derived from statistical methods alone. In particular, signiﬁcance tests and conﬁdence intervals do not by themselves provide a logically sound basis for concluding an effect is present or absent with certainty or a given probability. This point should be borne in mind whenever one sees a conclusion framed as a statement of probability, likelihood, or certainty about a hypothesis. Information about the hypothesis beyond that contained in the analyzed data and in conventional statistical models (which give only data probabilities) must be used to reach such a conclusion; that information should be explicitly acknowledged and described by those offering the conclusion. Bayesian statistics offers methods that attempt to incorporate the needed information directly into the statistical model; they have not, however, achieved the popularity of P values and conﬁdence intervals, in part because of philosophical objections and in part because no conventions have become established for their use. (g) All statistical methods (whether frequentist or

Bayesian, or for testing or estimation, or for inference or decision) mak e extensive assumptions about the sequence of events that led to the results presented—not only in the data generation, but in the analysis choices. Thus, to allow critical evaluation, research reports (including meta-analyses) should describe in detail the full sequence of events that led to the statistics presented, including the motivation for the study, its design, the original analysis plan, the criteria used to include and exclude subjects (or studies) and data, and a thorough description of all the analyses that were conducted.

In closing, we note that no statistical method is immune to misinterpretation and misuse, but prudent users of

Statistical tests, P values, conﬁdence intervals, and power: a guide to misinterpretations 347

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statistics will avoid approaches especially prone to serious abuse. In this regard, we join others in singling out the degradation of P values into ‘‘signiﬁcant’’ and ‘‘nonsignificant’’ as an especially pernicious statistical practice [126].

Acknowledgments SJS receives funding from the IDEAL project supported by the European Union’s Seventh Framework Programme for research, technological development and demonstration under Grant Agreement No. 602552. We thank Stuart Hurlbert, Deborah Mayo, Keith O’Rourke, and Andreas Stang for helpful comments, and Ron Wasserstein for his invaluable encouragement on this project.

Open Access This article is distributed under the terms of the Creative Commons Attribution 4.0 International License (http://creative commons.org/licenses/by/4.0/), which permits unrestricted use, distribution, and reproduction in any medium, provided you give appropriate credit to the original author(s) and the source, provide a link to the Creative Commons license, and indicate if changes were made.

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