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.
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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