Progressive Statistics Will G Hopkins Sportscience 13, 55-70, 2009 (sportsci.org/2009/prostats.htm) 1 Institute of Sport and Recreation
Research, AUT University, Auckland NZ, Email; 2 School
of Health and Social Care, University of Teesside, Middlesbrough
UK, Email; 3
Departments of Epidemiology, Orthopedics, and Exercise & Sport Science,
University of North Carolina at Chapel Hill, Chapel Hill NC, Email; 4
KIHU-Research Institute for Olympic Sports, Jyvaskyla, Finland, Email. Reviewer:
Ian Shrier, Department of Family Medicine,
McGill University, Montreal, Canada.
Updated June 2014 with revised magnitude thresholds
for risk, hazard and count ratios (Hopkins, 2010). TABLE 1. Statements of best practice for reporting research TABLE 2.
Generic statistical advice for sample-based studies Note 7:
Non-parametric Analysis Note 10:
Effect of Continuous Predictors TABLE 3.
Additional statistical advice for specific designs Outcome
Statistics: Continuous Dependents Outcome
Statistics: Event Dependents MEASUREMENT
STUDIES: DIAGNOSTIC TESTS MEASUREMENT
STUDIES: RELIABILITY MEASUREMENT
STUDIES: FACTOR STRUCTURE SINGLE-CASE
STUDIES: QUANTITATIVE NON-CLINICAL SINGLE-CASE
STUDIES: QUALITATIVE |

In response to the widespread misuse of statistics in research, several biomedical organizations have published statistical guidelines in their journals, including the International Committee of Medical Journal Editors (www.icmje.org), the American Psychological Association (Anonymous, 2001), and the American Physiological Society (Curran-Everett and Benos, 2004). Expert groups have also produced statements about how to publish reports of various kinds of medical research (Table 1). Some medical journals now include links to these statements as part of their instructions to authors. In this article we provide our view of best practice for the use of statistics in sports medicine and the exercise sciences. The article is similar to those referenced in Table 1 but includes more practical and original material. It should achieve three useful outcomes. First, it should stimulate interest and debate about constructive change in the use of statistics in our disciplines. Secondly, it should help legitimize the innovative or controversial approaches that we and others sometimes have difficulty including in publications. Finally, it should serve as a statistical checklist for researchers, reviewers and editors at the various stages of the research process. Not surprisingly, some of the reviewers of this article disagreed with some of our advice, so we emphasize here that the article represents neither a general consensus amongst experts nor editorial policy for this journal. Indeed, some of our innovations may take decades to become mainstream.
Most of this article is devoted to advice on the various kinds of sample-based studies that comprise the bulk of research in our disciplines. Table 2 and the accompanying notes deal with issues common to all such studies, arranged in the order that the issues arise in a manuscript. This table applies not only to the usual studies of samples of individuals but also to meta-analyses (in which the sample consists of various studies) and quantitative non-clinical case studies (in which the sample consists of repeated observations on one subject). Table 3, which should be used in conjunction with Table 2, deals with additional advice specific to each kind of sample-based study and with clinical and qualitative single-case studies. The sample-based studies in this table are arranged in the approximate descending order of quality of evidence they provide for causality in the relationship between a predictor and dependent variable, followed by the various kinds of methods studies, meta-analyses, and the single-case studies. For more on causality and other issues in choice of design for a study, see Hopkins (2008).
Inferences are
evidence-based conclusions about the true nature of something. The
traditional approach to inferences in research on samples is an assertion
about whether the effect is statistically significant or “real”, based on a P
value. Specifically, when the range of
uncertainty in the true value of an effect represented by the 95% confidence
interval does not include the zero or null value, P is <0.05, the effect
“can’t be zero”, so the null hypothesis is rejected and the effect is termed
significant; otherwise P is >0.05 and the effect is non-significant. A fundamental theoretical dilemma with this
approach is the fact that the null hypothesis is always false; indeed, with a
large enough sample size all effects are statistically significant. On a more practical level, the failure of
this approach to deal adequately with the real-world importance of an effect
is evident in the frequent misinterpretation of a non-significant effect as a
null or trivial effect, even when it is likely to be substantial. A significant effect that is likely to be
trivial is also often misinterpreted as substantial. A more realistic
and intuitive approach to inferences is based on where the confidence
interval lies in relation to threshold values for substantial effects rather
than the null value (Batterham and Hopkins, 2006). If
the confidence interval includes values that are substantial in some positive
and negative sense, such as beneficial and harmful, you state in plain
language that the effect could be substantially positive Use of thresholds
for moderate and large effects allows even more informative inferential
assertions about magnitude, such as An appropriate
default level of confidence for the confidence interval is 90%, because it
implies quite reasonably that an outcome is clear if the true value is very
unlikely to be substantial in a positive and/or negative sense. Use of 90% rather than 95% has also been
advocated as a way of discouraging readers from reinterpreting the outcome as
significant or non-significant at the 5% level (Sterne and Smith, 2001). In
any case, a symmetrical confidence interval of whatever level is appropriate
for making only non-clinical or mechanistic inferences. An inference or decision about clinical or
practical utility should be based on probabilities of harm and benefit that
reflect the greater importance of avoiding use of a harmful effect than
failing to use a beneficial effect.
Suggested default probabilities for declaring an effect clinically
beneficial are <0.5% (most unlikely) for harm and >25% (possible) for
benefit (Hopkins, 2007). A clinically unclear effect is therefore
possibly beneficial (>25%) with an unacceptable risk of harm
(>0.5%). Equivalently, an unclear effect occurs when an asymmetric confidence
interval that is a 99% interval on the harmful side of an observed effect and
a 50% interval on the beneficial side overlaps into harmful and beneficial
values. (The disposition of an asymmetric confidence interval also underlies
the appropriate interpretation of statistical significance.) The
probabilities of >25% for benefit and <0.5% for harm correspond to a
minimum ratio of 66 for odds
of benefit to odds of harm, a suggested default when sample sizes are sub- or
supra-optimal (Hopkins, 2007). Thus you
could decide to make use of an effect with an 80% chance of benefit and a 5%
chance of harm, because the odds of benefit outweigh the odds of harm by a
factor of 76, which is >66. Magnitude-based
inferences as outlined above represent a subset of the kinds of inference
that are possible using so-called Bayesian
statistics, in which the researcher combines the study outcome with
uncertainty in the effect prior to the study to get the posterior (updated)
uncertainty in the effect. A
qualitative version of this approach is an implicit and important part of the
Discussion section of most studies, but in our view specification of the
prior uncertainty is too subjective to apply the approach quantitatively. Researchers may also have difficulty
accessing and using the computational procedures. On the other hand, confidence limits and
probabilities related to threshold magnitudes can be derived readily via a
spreadsheet (Hopkins, 2007) by making the same assumptions about
sampling distributions that statistical packages use to derive P values. Bootstrapping, in which a sampling
distribution for an effect is derived by resampling from the original sample
thousands of times, also provides a robust approach to computing confidence
limits and magnitude-based probabilities when data or modeling are too
complex to derive a sampling distribution analytically. Public access to depersonalized data, when feasible, serves the needs of the wider community by
allowing more thorough scrutiny of data than that afforded by peer review and
by leading to better meta-analyses. Make this statement in your initial
application for ethics approval, and state that the data will be available indefinitely
at a website or on request without compromising the subjects’ privacy. Any conclusive
inference about an effect could be wrong, and the more effects you
investigate, the greater the chance of making an error. If you test multiple hypotheses, there is
inflation of the Type I error rate: an
increase in the chance that a null effect will turn up statistically
significant. The usual remedy of making the tests more conservative is not
appropriate for the most important pre-planned effect, it is seldom applied
consistently to all other effects reported in a paper, and it creates
problems for meta-analysts and other readers who want to assess effects in
isolation. We therefore concur with
others (e.g., Perneger,
1998) who advise against adjusting the Type I
error rate or confidence level of confidence intervals for multiple
effects. For several
important clinical or practical effects, you should nevertheless constrain the increase in the chances of making
clinical errors. Overall chances of
benefit and harm for several interdependent effects can be estimated properly
by bootstrapping, but a more practical and conservative approach is to assume
the effects are independent and to estimate errors approximately by
addition. The sum of the chances of
harm of all the effects that separately are clinically useful should not
exceed 0.5% (or your chosen maximum rate for Type 1 clinical errors–see Note
4); otherwise you should declare fewer effects useful and acknowledge that
your study is underpowered. Your study
is also underpowered if the sum of chances of benefit of all effects that
separately are not clinically useful exceeds 25% (or your chosen Type 2
clinical error rate). When your sample size is small, reduce the chance that
the study will be underpowered by designing and analyzing it for fewer
effects. A problem with
inferences about several effects with overlapping confidence intervals is
misidentification of the largest (or smallest) and upward (or downward) bias
in its magnitude. In simulations the bias is of the order of the average standard
error of the outcome statistic, which is approximately one-third the width of
the average 90% confidence interval (WGH, unpublished observations).
Acknowledge such bias when your aim is to quantify the largest or smallest of
several effects. Sample sizes that
give acceptable precision with 90% confidence limits are similar to those
based on a Type 1 clinical error of 0.5% (the chance of using an effect that
is harmful) and a Type 2 clinical error of 25% (the chance of not using an
effect that is beneficial). The sample
sizes are approximately one-third those based on the traditional approach of
an 80% chance of statistical significance at the 5% level when the true effect
has the smallest important value. Until
hypothesis testing loses respectability, you should include the traditional
and new approaches in applications for ethical approval and funding. Whatever approach
you use, sample size needs to be quadrupled to adequately estimate individual
differences or responses and effects of covariates on the main effect. Larger samples are also needed to keep
clinical error rates for clinical or practical decisions acceptable when
there is more than one important effect in a study (Note 3). See Reference (Hopkins, 2006a) for a spreadsheet and details of these and
many other sample-size issues. In a mechanisms
analysis, you determine the extent to which a putative mechanism variable
mediates an effect through being in a causal chain linking the predictor to
the dependent variable of the effect.
For an effect derived from a linear model, the contribution of the
mechanism (or mediator) variable is represented by the reduction in the
effect when the variable is included in the model as another predictor. Any such reduction is a necessary but not
sufficient condition for the variable to contribute to the mechanism of the
effect, because a causal role can be established definitively only in a
separate controlled trial designed for that purpose. For interventions,
you can also examine a plot of change scores of the dependent variable vs
those of potential mediators, but beware that a relationship will not be
obvious in the scattergram if individual responses
are small relative to measurement error.
Mechanism variables are particularly useful in unblinded
interventions, because evidence of a mechanism that cannot arise from
expectation (placebo or nocebo) effects is also
evidence that at least part of the effect of the intervention is not due to
such effects. An effect
statistic is derived from a model (equation) linking a dependent (the “Y”
variable) to a predictor and usually other predictors (the “X” variables or covariates). The model is linear if the dependent can be
expressed as a sum of terms, each term being a coefficient times a predictor
or a product of predictors (interactions, including polynomials), plus one or
more terms for random errors. The effect
statistic is the predictor’s coefficient or some derived form of it. It follows from the additive nature of such
models that the value of the effect statistic is formally equivalent to the
value expected when the other predictors in the model are held constant.
Linear models therefore automatically provide adjustment for potential
confounders and estimates of the effect of potential mechanism variables. A
variable that covaries with a predictor and
dependent variable is a confounder if it causes some of the covariance and is
a mechanism if it mediates it. The
reduction of an effect when such a variable is included in a linear model is
the contribution of the variable to the effect, and the remaining effect is
independent of (adjusted for) the variable. The usual models
are linear and include: regression, ANOVA, general linear and mixed for a
continuous dependent; logistic regression, Poisson regression, negative
binomial regression and generalized linear modeling for events (a dichotomous
or count dependent); and proportional-hazards regression for a time-to-event
dependent. Special linear models
include factor analysis and structural equation modeling. For repeated
measures or other clustering of observations of a continuous dependent
variable, avoid the problem of interdependence of observations by using
within-subject modeling, in which you combine each subject's repeated measurements
into a single measure (unit of analysis) for subsequent modeling; alternatively,
account for the interdependence using the more powerful approach of mixed
(multilevel or hierarchical) modeling, in which you estimate different random
effects or errors within and between clusters. Avoid repeated-measures ANOVA,
which sometimes fails to account properly for different errors. For clustered event-type dependents
(proportions or counts), use generalized estimation equations. Note 7: Non-parametric Analysis A requirement for
deriving inferential statistics with the family of general linear models is
normality of the sampling distribution of the outcome statistic. Although there is no test that data meet
this requirement, the central-limit theorem ensures that the sampling
distribution is close enough to normal for accurate inferences, even when
sample sizes are small (~10) and especially after a transformation that
reduces any marked skewness in the dependent
variable or non-uniformity of error. Testing for normality of the dependent
variable and any related decision to use purely non-parametric analyses
(which are based on rank transformation and do not use linear or other
parametric models) are therefore misguided. Such analyses lack power for
small sample sizes, do not permit adjustment for covariates, and do not
permit inferences about magnitude.
Rank transformation followed by parametric analysis can be appropriate
(Note 8), and ironically, the distribution of a rank-transformed variable is
grossly non-normal. Non-uniformity of
effect or error in linear models can produce incorrect estimates and
confidence limits. Check for
non-uniformity by comparing standard deviations of the dependent variable in
different subgroups or by examining plots of the dependent variable or its
residuals for differences in scatter (heteroscedasticity)
with different predicted values and/or different values of the predictors. Differences in
standard deviations or errors between groups can be taken into account for
simple comparisons of means by using the unequal-variances t statistic. With more complex models use mixed modeling
to allow for and estimate different standard deviations in different groups
or with different treatments. For a simpler robust approach with independent
subgroups, perform separate analyses then compare the outcomes using a
spreadsheet (Hopkins, 2006b). Transformation of
the dependent variable is another approach to reducing non-uniformity,
especially when there are differences in scatter for different predicted
values. For many dependent variables,
effects and errors are uniform when expressed as factors or percents; log transformation converts these to uniform
additive effects, which can be modeled linearly then expressed as factors or percents after back transformation. Always use log
transformation for such variables, even when a narrow range in the dependent
variable effectively eliminates non-uniformity. Rank
transformation eliminates non-uniformity for most dependent variables and
models, but it results in loss of precision with a small sample size and
should therefore be used as a last resort.
To perform the analysis, sort all observations by the value of the
dependent variable, assign each observation a rank (consecutive integer),
then use the rank as the dependent variable in a liner model. Such analyses are often referred to
incorrectly as non-parametric. Use the
transformed variable, not the raw variable, to gauge magnitudes of correlations
and of standardized differences or changes in means. Back-transform the mean
effect to a mean in raw units and its confidence limits to percents or factors (for log transformation) or to raw
units at the mean of the transformed variable or at an appropriate value of
the raw variable (for all other transformations). When
analysis of a transformed variable produces impossible values for an effect
or a confidence limit (e.g., a negative rank with the rank transformation),
the assumption of normality of the sampling distribution of the effect is
violated and the analysis is therefore untrustworthy. Appropriate use of
bootstrapping avoids this problem. Outliers Note 10: Effect of Continuous Predictors The use of two
standard deviations (SD) to gauge the effect of a continuous predictor
ensures congruence between Cohen's threshold magnitudes for correlations and
standardized differences (Note 1). Two SD of a normally distributed predictor
also corresponds approximately to the mean separation of lower and upper tertiles (2.2 SD). The SD is ideally the variation in the
predictor after adjustment for other predictors; the effect of 2 SD in a
correlational study is then equivalent to, and can be replaced by, the
partial correlation (the square root of the fraction of variance explained by
the predictor after adjustment for all other predictors). A grossly skewed
predictor can produce incorrect estimates or confidence limits, so it should
be transformed to reduce skewness. Log transformation is often suitable for
skewed predictors that have only positive values; as simple linear predictors
their effects are then expressed per factor or percent change of their
original units. Alternatively, a skewed predictor can be parsed into quantiles (usually 2-5 subgroups with equal numbers of
observations) and included in the model as a nominal variable or as an
ordinal variable (a numeric variable with integer values). Parsing is also appropriate for a predictor
that is likely to have a non-linear effect not easily or realistically
modeled as a polynomial. The standard error
of the mean (SEM = SD/√(group sample size)) is
the sampling variation in a group mean, which is the expected typical
variation in the mean from sample to sample.
Some researchers argue that, as such, this measure communicates
uncertainty in the mean and is therefore preferable to the SD. A related widespread belief is that
non-overlap of SEM bars on a graph indicates a difference that is
statistically significant at the 5% level.
Even if statistical significance was the preferred approach to
inferences, this belief is justified only when the SEM in the two groups are equal, and for comparisons of changes in means, only
when the SEM are for means of change scores.
Standard error bars on a time-series graph of means of repeated
measurements thus convey a false impression of significance or
non-significance, and therefore, to avoid confusion, SEM should not be shown
for any data. In any case, researchers
are interested not in the uncertainty in a single mean but in the uncertainty
of an effect involving means, usually a simple comparison of two means. Confidence intervals or related inferential
statistics are used to report uncertainty in such effects, making the SEM
redundant and inferior. The above
represents compelling arguments for not using the SEM, but there are even
more compelling arguments for using the SD.
First, it helps to assess non-uniformity, which manifests as different
SD in different groups. Secondly, it
can signpost the likely need for log transformation, when the SD of a
variable that can have only positive values is of magnitude similar to or
greater than the mean. Finally and
most importantly, the SD communicates the magnitude of differences or changes
between means, which by default should be assessed relative to the usual
between-subject SD (Note 1). The manner
in which the SEM depends on sample size makes it unsuitable for any of these
applications, whereas the SD is practically unbiased for sample sizes ~10 or
more (Gurland and Tripathi, 1971). Random error or
random misclassification in a variable attenuates effects involving the
variable and widens the confidence interval.
(Exception: random error in a continuous dependent variable does not
attenuate effects of predictors on means of the variable.) After adjustment of the variable for any
systematic difference from a criterion in a validity study with subjects
similar to those in your study, it follows from statistical first principles
that the correction for attenuation of an effect derived directly from the
variable’s coefficient in a linear model is 1/v When one variable
in an effect has Substantial random or systematic error of measurement in a covariate used to adjust for confounding results in partial or unpredictable adjustment respectively and thereby renders untrustworthy any claim about the presence or absence of the effect after adjustment. This problem applies also to a mechanisms analysis involving such a covariate.
Bland and Altman
introduced limits of agreement (defining a reference interval for the
difference between measures) and a plot of subjects' difference vs mean
scores of the measures (for checking relative bias and non-uniformity) to
address what they thought were shortcomings arising from misuse of validity
and reliability correlation coefficients in measurement studies. Simple linear regression nevertheless
provides superior statistics in validity studies, for the following reasons:
the standard error of the estimate and the validity correlation can show that
a measure is suitable for clinical assessment of individuals and for
sample-based research, yet the measure would not be interchangeable with a
criterion according to the limits of agreement; the validity correlation provides a
correction for attenuation (see Note 12), but no such correction is available
with limits of agreement; the
regression equation provides trustworthy estimates of the bias of one measure
relative to the other, whereas the Bland-Altman plot shows artifactual bias for measures with substantially
different errors (Hopkins, 2004);
regression statistics can be derived in all validity studies, whereas
limits of agreement can be derived from difference scores in only a minority
of validity studies (“method-comparison” studies, where both measures are in
the same units); finally, limits of agreement in a method-comparison study of
a new measure with an existing imprecise measure provide no useful
information about the validity of the new measure, whereas regression
validity statistics can be combined with published validity regression
statistics for the imprecise measure to correctly estimate validity
regression statistics for the new measure. Arguments have also
been presented against the use of limits of agreement as a measure of
reliability (Hopkins, 2000). Additionally, data generally contain
several sources of random error, which are invariably estimated as variances
in linear models then combined and expressed as standard errors of
measurement and/or correlations. Transformation to limits of agreement is of
no further clinical or theoretical value. Note 14: Qualitative Inferences Some qualitative
researchers believe that it is possible to use qualitative methods to
generalize from a sample of qualitatively analyzed cases (or assessments of
an individual) to a population (or the individual generally). Others do not even recognize the legitimacy
of generalizing. In our view, generalizing is a fundamental obligation that
is best met quantitatively, even when the sample is a series of qualitative
case studies or assessments.
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