Estimating Sample Size for MagnitudeBased
Inferences Will G Hopkins Sportscience 10, 6370, 2006 (sportsci.org/2006/wghss.htm)

Update April 2016. Sample
sizes for designs where the dependent variable is a count of something have
now been updated to include crossovers and controlled trials. The estimates are
based by default on the normal approximation to the Poisson distribution, whereby
the observed betweensubject SD of the counts is the square root of the mean
count (the expected SD when the counts in each subject arise from independent
events). The estimates also allow for "overdispersion"
and "underdispersion" of the counts. With overdispersion, underlying real differences
between subjects' counts produce an observed betweensubject SD greater than the
square root of the mean count. With underdispersion, which is less common, the
observed SD is less than expected, possibly because of sampling variation
rather than any real underdispersion in the counts. This panel in the spreadsheet is configured for
smallest effects defined by a ratio of the counts, the default being 0.9 or
its inverse 1.11. For smallest effects defined by standardization, just use
the earlier panel highlighted in yellow, according to which a smallest effect
of 0.20 requires ~272 subjects (136+136) for a group comparison or
parallelgroups controlled trial (or a similar number for a crossover and 4x
as many for a prepost controlled trial). Update
October 2015. I have added a comment cell with extra information
about smallest changes and differences in means of continuous variables in
crossovers, controlled trials, and group comparisons. In particular, I now
indicate how to take into account error of measurement when using
standardization, according to which the smallest difference or change is 0.2
of the betweensubject standard deviation (SD). In most settings, the SD
should be the true or pure SD_{P}, not the observed SD_{O},
which is inflated by the typical or standard error of measurement e: SD_{O}^{2}
= SD_{P}^{2} + e^{2}. Hence, the smallest difference
or change is 0.2SD_{P} = 0.2Ö(SD_{O}^{2} – e^{2}) or
0.2SD_{O}Ör, where r
= SD_{P}^{2}/SD_{O}^{2} is the intraclass or
retest correlation. In other words, if the observed SD is used to define the
smallest important difference or change, it should be multiplied by the
square root of the retest correlation. The timeframe of the error of measurement
(or retest correlation) should reflect the timeframe of the effect to be
studied. If you are interested in acute differences or changes, the typical
error or retest correlation should come from a shortterm reliability study
that effectively measures technical error only. If instead you are interested
in stable differences or changes over a defined period (e.g., six months),
then the smallest important change in the mean (or difference the mean, in a
crosssectional study) should come from the pure betweensubject SD over such
a period. Update
August 2014. Cells for calculating the rate of various kinds of
magnitudebased outcome when the true effect is null worked previously for
clinical outcomes but did not give correct rates for nonclinical
outcomes. These cells have been
simplified and updated to allow estimation of rates for any true value. The
effect of changing the sample size on the observed change required for a
clear outcome has now also been added. The spreadsheet is now an xlsx file,
to make use of the new bugfree T functions. Updates
June 2013. Withinsubject SD (typical or standard error of
measurement) is needed to estimate sample size for crossovers and prepost
controlled trials, but it's often hard to find reliability studies with a
dependent variable and time between trials comparable with those in your intended
study. However, you can often find
comparable crossovers or controlled trials, so I have devised a panel in the
samplesize spreadsheet to estimate withinsubject SD from such studies. The
published studies needn't have the same kind of intervention, but try to find
some with similar time between trials and similar subjects, because the
approach is based on the assumption that the error in the published study or
studies is similar to what will be in your study. It's also assumed that
individual responses to the treatment in your study will be similar to those
in your study. This assumption may be
more realistic or conservative than the usual approach of using the error
from a reliability study, in which there are of course no individual
responses. You could address this
issue in your Methods section where you justify sample size, if you use this
approach. Updates
June 2011. A panel for a count outcome is now added to the
spreadsheet. The smallest important
effect is shown as a count ratio of 1.1, as explained in the article on linear models and effect magnitudes in the 2010 issue of Sportscience. The panel for event outcomes now allows inclusion of
smallest beneficial and harmful effects as risk difference, odds ratio and
hazard ratio (in addition to the risk ratio that was there originally). The
calculations for the event outcomes are based on assumption of a normal
distribution for the log of the odds ratio, and the sample sizes for risk difference,
hazard ratio and risk ratio are computed by converting the smallest effects
for these statistics into odds ratios.
Samplesize estimation when there is repeated
measurement of a dependent variable representing a count or an event is not
yet included in the spreadsheet. There is now a bullet point on the
issue of the sample size needed in a reliability pilot study. The reviewer of these updates (Greg Atkinson)
suggested I include a comment about sample size for equivalence studies,
which are aimed at showing that two treatments are practically equivalent. To
put it another way, what is the sample size for acceptable uncertainty in the
estimate of the difference in the effects of the two treatments? My novel approaches to samplesize
estimation address precisely this question.
Update
June 2008: a bullet point on
likelihood of an inconclusive outcome with an optimal sample size; also,
slideshow now replaced with an updated version presented at the 2008 annual
meeting of the American College of Sports Medicine in Indianapolis
(copresented by Stephen W Marshall, who made useful suggestions for changes
to some slides). Update Mar
2008: advice on how to estimate a value for the smallest
effect that a suboptimal sample size can estimate adequately now added to
appropriate bullet point; also more in the bullet point on choosing
smallest effects and their impact on sample size. Update Nov
2007: a bullet point on sample
size for adequate characterization of individual differences and responses. Updates to
Oct 2007: a bullet point on estimation of sample size when you have more
than one important effect in a study and you want to constrain the chance of
error with any of them; a paragraph reconciling
90% confidence intervals with Type 1 and 2 errors of 0.5% and 25%; a minor
addition to the bullet point on sample size on the fly; other minor edits. We study a sample of subjects to find out about an effect in a population. The bigger the sample, the closer we get to the true or population value of the effect. We don't need to study the entire population, but we do need to study enough subjects to get acceptable accuracy for the true value. "How many subjects?" is a question I am often called on to answer, usually before a project is submitted for ethical approval. Sample size is an ethical issue, because a sample that is too large represents a needless waste of resources, and a sample that is too small will also waste resources by failing to produce a clear outcome. If the study involves exposing subjects to pain or risk of harm, an appropriate sample size is ethically even more important. Applications for ethical approval of a study and the methods section of most manuscripts therefore require an estimate of sample size and a justification for the estimate. Free software is available at various sites on the Web to estimate sample size using the traditional approach based on statistical significance. However, my colleagues and I now avoid all mention of statistical significance in our publications, at least in those I coauthor. Instead, we make an inference about the importance of an effect, based on the uncertainty in its magnitude. See the article by Batterham and Hopkins (2005a) for more. I have therefore devised two new approaches to samplesize estimation for studies in which inferences are based on magnitudes. In this article I explain the traditional and new approaches, and I provide a spreadsheet for the estimates. I also explain various other issues in samplesize estimation that need to be understood or taken into account when designing a study. While preparing a talk on samplesize estimation in 2008, I realized that there is a kind of unified theory that ties together all methods of samplesize estimation, as follows. In research, we make inferences about effects. The inference results in a decision or declaration about the magnitude of the effect, usually the smallest magnitude that matters. Whatever way the decision goes, we could be wrong, so there are two kinds of error. We estimate a sample size that keeps both error rates acceptably low. Sample Size for Statistical Significance
According to this traditional approach, you need a sample size that would produce statistical significance for an effect most of the time, if the true value of the effect were the smallest worthwhile value. Stating that an effect is statistically significant means that the observed value of the effect falls in the range of extreme values that would occur infrequently (<5% of the time, for significance at the 5% or 0.05 level) if the true value were zero or null. The value of 5% defines the socalled Type I error rate: the chance that you will declare a null effect to be significant. "Most of the time" is usually assumed to be 80%, a number that is sometimes referred to as the power of the study. A power of 80% can also be reexpressed as a Type II error rate of 20%: the chance that you will fail to get statistical significance for the smallest important effect. I deal with the choice of the value of this effect later. The traditional approach works best when you use the sample size as estimated, and when the values of any other parameters required for the calculation (e.g., error of measurement in a prepost controlled trial, incidence of disease in a cohort study) turn out to be correct. In such rare cases you can interpret a statistically significant outcome as clinically or practically important and a statistically nonsignificant outcome as clinically or practically trivial. When the sample size is different from that calculated, and when other effects are estimated from the same data, statistical and clinical significance are no longer congruent. In any case, I have found that Type I and II errors of 5% and 20% lead to decisions that are too conservative (Hopkins, 2007). Some other approach is needed to make inferences about the realworld importance of an outcome and to estimate sample sizes for such inferences. Sample Size for MagnitudeBased Inferences
I have been aware of this problem for about 10 years, during which I have devised two approaches that seem to be suitable. Two years ago I did an extensive literature search but was unable to find anything similar, although it is apparent that a Bayesian approach can achieve what I have achieved and more (e.g., Joseph et al., 1997). However, I have yet to see the Bayesian approach presented in a fashion that researchers can access, understand, and use. A recent review of samplesize estimation was entirely traditional (Julious, 2004). I have worked my approaches into a spreadsheet that hopefully researchers can use. I have included the traditional approach and checked that it gives the same sample sizes as other tools (e.g., Dupont and Plummer's software). The new methods for estimating sample size are based on (a) acceptable error rates for a clinical or practical decision arising from the study and (b) adequate precision for the effect magnitude. I presented these methods as a poster at the 2006 annual conference of the American College of Sports Medicine (Hopkins, 2006a). For (a) I devised two new types of error: a decision to use an effect that is actually harmful (a Type 1 clinical error), and a decision not to use an effect that is actually beneficial (a Type 2 clinical error). I then constructed a spreadsheet using statistical first principles to calculate sample sizes for chosen values of Type 1 and 2 errors (e.g., 0.5% and 25% respectively), for chosen smallest beneficial and harmful values of outcome statistics in various straightforward designs (changes or differences in means in controlled trials or crosssectional studies, correlations in crosssectional studies, risk ratios in cohort studies, and odds ratios in casecontrol studies), and for chosen values of other designspecific statistics (error of measurement, betweensubject standard deviation, proportion of subjects in each group, and incidence of disease or prevalence of exposure). The calculations are based on the usual assumption of normality of the sampling distribution of the outcome statistic or its log transform. For (b) I reasoned that precision is adequate when the uncertainty in the estimate of an outcome statistic (represented by its confidence interval) does not extend into values that are substantial in both a positive and a negative sense when the sample value of the statistic is zero or null. Sample sizes are then derived from the spreadsheet by choosing equal Type 1 and 2 clinical errors (e.g., 5% for a 90% confidence interval, or 2.5% for a 95% confidence interval). Sample sizes for Type 1 and 2 clinical errors of 0.5% and 25% are almost identical to those for adequate precision with a 90% confidence interval, which in turn are only onethird of traditional sample sizes for the usual default Type I and II statistical errors of 5% and 20%. For adequate precision with a 95% confidence interval, the sample sizes are approximately half those of the traditional method. Perceptive readers may wonder if there is a problem with providing 90% confidence intervals in a paper and using them to make calls about effects being clear, while at the same time making a decision to use an effect only if the chance of harm is <0.5% (which is equivalent to a 99% rather than a 90% confidence interval not overlapping into harmful values). Although the sample sizes estimated by both methods are practically identical, there will indeed be occasions when an effect is conclusive by one method but inconclusive by another. An effect can also be clear and trivial on the basis of a 90% confidence interval but decisive and clinically useful on the basis of chances of benefit and harm. It is easy to generate these scenarios using the spreadsheet for confidence limits and clinical chances (Hopkins, 2007). Included in the spreadsheet are confidence limits and quantitative and qualitative chances of benefit and harm for any chosen values of the outcome statistic. The default values shown in the spreadsheet are the calculated "decision" values: observed values greater than the decision value will lead you to decide that the effect is clinically beneficial. (The decision values are analogous to the "critical" values of the traditional method of samplesize estimation, above which observed values will be statistically significant.) The confidence limits and chances of benefit and harm for the decision values serve as a check on the accuracy of the formulae I devised to estimate the sample sizes. You will see that the confidence limits and clinical chances provided by the spreadsheet are fully consistent with the Type 1 and 2 clinical errors. Also included are outcomes of studies for the estimated or any other sample size when the true effect is null (zero for differences in means, zero for correlation coefficients, 1.0 for rate ratios). For the sample size given by the default Type 1 and 2 errors of 0.5% and 25%, you will see that the chances of deciding to use a null effect are appreciable (up to 17%). Fortunately, for smaller sample sizes this figure declines rapidly. The chance of observing nontrivial outcomes that appear to be clear is the 10% you would expect for 90% confidence limits with a true null effect, when the sample size is optimal. This figure may seem high, but it is less problematic when you express these nontrivial outcomes with their full probabilities. As can be seen from the spreadsheet, only ~2.2% of the outcomes would be "likely [or probably] nontrivial", and <0.1% would be "very likely nontrivial". Thus 7.8% of the 10% would be "possibly [or maybe] nontrivial", which seems acceptable. With suboptimal sample sizes the "likely nontrivial" outcomes balloon out to a maximum of 17%, so you will need to be cautious about borderline clear outcomes when your sample size is much smaller than it ought to be. Of course, if you use more than the estimated sample size, the error rates are smaller. General SampleSize Issues
Whether you use the spreadsheet for the traditional or new approaches, there are several important samplesize issues you should know about when designing a study. Some of these are implicit in the spreadsheet, but you will need to take others into account yourself. • Samplesize estimation is challenging for the average researcher, so mistakes are common. Check your estimate by comparing it with sample sizes in published studies that have measures, subjects and design similar to yours. • You can justify a sample size on the grounds that it is similar to those in similar studies that produced clear outcomes, but be aware that effects are clear in many studies because the effects are substantial. See how wide the confidence interval is in these studies, using my spreadsheet (Hopkins, 2007) to generate it, if necessary; if your effect turns out to be smaller but with a confidence interval of similar width, will your effect be clear or will you need a larger sample? • All methods for estimation of sample size need a value for the smallest important effect. The estimates are sensitive to the value: halving it results in a quadrupling of sample size. Your justification of sample size must therefore include a justification of choice of the smallest important effect. For most continuous measures the default can be Cohen's thresholds of 0.20 for a standardized difference or change in means and a correlation of 0.10. In observational studies the resulting sample size is ~270 for the defaults of my default methods. A reasonable default for a hazard, risk or odds ratio in an intervention is ~1.101.20, because a 1020% change in the incidence of an injury or illness would affect one or more groups in a community, however rare the condition. A risk ratio of this order is quantifiable in a wellcontrolled largescale intervention, but expert epidemiologists consider that biases inherent in most cohort and casecontrol studies effectively set the smallest believable risk ratio in such studies to ~3.0 (Taubes, 1995). This limitation is bad news for public health but good news for researchers who can’t afford huge sample sizes. Smallest effects for measures directly related to the performance of solo athletes are ~0.5 of the competitiontocompetition variability in performance (Hopkins, 2004; Hopkins, 2006b); the resulting sample sizes are usually many times larger than most researchers use. • Sample size depends on the design. Nonrepeated measures studies (crosssectional, prospective, casecontrol) usually need hundreds of subjects. Repeatedmeasures interventions (crossovers and controlled trials) usually need scores of subjects. Crossovers need less than parallelgroup controlled trials (down to one quarter), provided reliability does not worsen too much during the washout period. These assertions are easily verified with the spreadsheet. If you have limited access to subjects or limited time or resources, you should choose a design and research question to accommodate the number you can investigate. • To take account of any clustering of subjects, you can in theory inflate sample size by a factor of 1+r(c1), where r is the intracluster correlation coefficient and c is the mean cluster size. It follows that you should keep the cluster size as small as possible. The formula for r is (between)/(between + within), where between and within are the pure betweencluster variance and the withincluster variance respectively. As such, r is difficult to guestimate and would need to be estimated in an exploratory study. For a repeatedmeasures design the r is for change scores, so the exploratory study would have to be done with the intended interventions–usually an impractical option. • Samplesize estimates for prospective studies and controlled trials should be inflated by 1030% to allow for dropouts, depending on the demands placed on the subjects, the duration of the study, and incentives for compliance. • A larger true effect needs a smaller sample size. You can understand this assertion by considering sample size estimated via acceptable uncertainty. The confidence interval for a trivial effect has to be sufficiently narrow not to overlap small positive and negative values, whereas the confidence interval for a large positive or negative effect can be much wider before it overlaps small negative or positive values. But the width of the confidence interval is approximately inversely proportional to the square root of the sample size, so the wider confidence interval for larger effects implies a smaller sample size. When you have to use a small sample size, it follows that you will still get a clear outcome, if the true effect is sufficiently large. On the other hand, if the outcome is unclear, you will find it more difficult to publish the work. The spreadsheet has instructions on how to estimate sample size for larger effects. • The relationship between effect magnitude and sample size makes it possible to determine sample size "on the fly", whereby you study a series of cohorts of subjects until you get a clear outcome. This approach, also known as a groupsequential design, is a practical way to deal with the various uncertainties in the estimation of sample size; it is also ethically superior to using a fixed sample size, because it reduces waste of resources and risk to subjects. When statistical significance or lack of it is used to terminate sampling, the groupsequential approach is known to produce biased outcomes and inflated error rates, but software is available to avoid these problems. (See Rogers et al., 2005) The extent of error and bias when adequate precision and acceptable clinical error rates are used to terminate sampling needs to be investigated. Meanwhile, estimate the approximate sample size for an additional cohort by assuming the true value of the effect is the value in subjects already assayed, then using this value in the spreadsheet to estimate the total sample size. • An unavoidably suboptimal sample size (i.e., smaller than the size estimated for acceptable errors with the smallest important effect) is ethically defensible if the true effect is likely to be large enough for the outcome to be clear. You can also argue that an unclear outcome with a sample size that isn’t way too small will still set useful limits on the likely magnitude of the effect and will therefore be worth publishing, because it will contribute to a metaanalysis. To obtain a value for the smallest effect your sample size will estimate with acceptable confidence, change the value of the smallest important effect in the accompanying spreadsheet until it gives your sample size. Provide this value and its confidence interval in a proposal, ethics application and Methods section of a manuscript. Use the confidence interval to comment on the “useful limits” in the proposal or ethics application, if you end up observing a trivial effect. • Even optimal sample sizes can produce inconclusive outcomes, thanks to sampling variation. The likelihood of such an outcome, which I have estimated by simulation, is at most ~10%. For the approaches based on statistical and clinical significance, this maximum occurs with small sample sizes and apparently when the true value is equal to the critical and decision value respectively, while for the confidenceinterval approach it occurs when the true value is null. Interested academics can download a zip file (9 MB) of spreadsheets showing the simulations. The spreadsheets can be tweaked to show that increasing the sample size by ~25% makes the likelihood of an inconclusive outcome negligible. • For nonrepeated measures designs, sample size depends on validity of the dependent variable. This principle follows from the fact that the random error represented by lessthanperfect validity increases the uncertainty in the outcome statistic, so more subjects are needed for acceptable uncertainty. From first principles, the sample size is proportional to 1/v^{2} = 1+e^{2}/SD^{2}, where v is the validity correlation coefficient, e is the error of the estimate, and SD is the betweensubject standard deviation of the criterion variable in the validity study. Sample size thus needs to be doubled when the validity correlation is 0.7 and quadrupled when it is 0.5. Such adjustments are not included in the spreadsheet. • With controlled trials and other repeatedmeasures designs, sample size is sensitive to reliability of the dependent variable, again because of the effect of error on uncertainty. From statistical first principles, sample size is proportional to (1‑r) = e^{2}/SD^{2}, where r is the testretest reliability correlation coefficient, e is the error of measurement, and SD is the observed betweensubject standard deviation. Thus sample sizes of only a few subjects are theoretically possible for measures of sufficiently high reliability, although you should always have at least 10 subjects in each group to reduce the chance that the sample substantially misrepresents the population. This effect of reliability on sample size is implicit in the spreadsheet, because you have to enter the error of measurement (the withinsubject standard deviation) to get the sample size. • The estimate of measurement error used to estimate sample size in a repeatedmeasures intervention has to come from a reliability study of duration similar to that of the intervention. The resulting sample size may still be an underestimate, because any individual responses to the treatment will effectively inflate the error of measurement and thereby widen the confidence interval for the treatment effect. Sample size on the fly is one way to allow for individual responses. • Validity of a predictor variable in any design has the same effect on sample size as validity of the dependent variable in a nonrepeated measures design. However, the effect of lessthanperfect validity manifests itself as a reduction in the magnitude of the effect of the predictor, the reduction being proportional to v, the validity correlation for the predictor–hence the need for a larger sample size. The socalled correction for attenuation is therefore a factor of 1/v (or 1/√r, if reliability error is the only source of validity error). In contrast, validity and reliability of a dependent variable affect the uncertainty of a difference or change in a mean, but have no effect on its expected magnitude. • With designs involving comparison of groups (e.g., a parallelgroups controlled trial), make the groups of equal size to give the smallest total size. If the size of one group is limited only by availability of subjects, a larger number of subjects for the comparison group will increase the precision of the outcome, but more than five times as many subjects in the comparison group gives no further practical increase in precision. You can check this assertion with the spreadsheet. • When you want to compare an outcome between independent subgroups, a surprising consequence of statistical first principles is that you will need twice as many subjects in each subgroup to get the same precision of estimation for the comparison as for either subgroup alone. Thus, for example, a controlled trial that would give adequate precision with 20 subjects would need 40 females and 40 males for adequate precision of the comparison of the effect between females and males. Comparisons of effects in subgroups therefore should not be undertaken as a primary aim of a study without adequate resources. • But it is important to characterize individual differences or responses in an effect, which means attempting to quantify the contribution of the subject characteristic(s) responsible by including them in the analytical model. The characteristic effectively divides the sample into independent subgroups, so it follows from the previous bullet point that you need four times the usual sample size to estimate the modifying effect of the characteristic properly. (This rule applies also to a continuous subject characteristic, such as height.) For treatment effects in a controlled trial, it is also important to establish the extent of individual responses, even if you can't identify the subject characteristic(s) responsible. The magnitude of individual responses is expressed as a standard deviation free of measurement error (e.g., ±2.6% around the treatment's mean effect of 1.8%). By working through the various formulae, I found that the uncertainty (confidence interval) in the standard deviation representing individual responses is ~1.0 to 3.0´ the uncertainty in the mean effect for group sample sizes of 10 to 100 respectively, in the worstcase scenario of observed trivial individual responses (a result which I also checked with estimates in my controlledtrial spreadsheets). Use of 4´ the usual sample size to characterize the moderating effect of a subject characteristic would halve the confidence interval for the standard deviation representing individual responses; the resulting uncertainty in the standard deviation would be adequate, because it would represent little chance of true substantial individual responses in the worstcase scenario of no observed individual responses (observed standard deviation of zero). For more on the neglected but increasingly important issue of individual responses, see the articles on controlled trials in this journal (Batterham and Hopkins, 2005b; Hopkins, 2003; Hopkins, 2006c). • Researchers who have difficulty recruiting enough subjects of one sex sometimes recruit a small proportion of the other sex and analyze the outcome without regard to sex. This approach is misguided. If you do not adjust for sex, you bias the mean effect towards that of the larger group. But to adjust for sex, you average the separate effects for the males and females. The resulting effective sample size is actually less than that of the larger group, when less than 30% of the subjects are in the smaller group. Download a simple spreadsheet I devised to illustrate this point. Conclusion: use subjects of one sex only, or aim for proportions of females and males in the sample that come close to their proportions in the population. This conclusion applies to other subgroupings. • When you investigate more than one effect in a study, there is inevitable inflation in the chances of making errors. For example, imagine you studied two independent effects and found chances of harm and benefit of 0.4% and 76% for one effect and 0.3% and 56% for the other. If you decide to use both effects, the chance of doing harm overall is 0.7%, which exceeds the default threshold of 0.5%. Opting to use only the most important or preplanned effect would keep the chance of harm below 0.5%, but you would thereby fail to use an effect that has a chance of benefit of either 56% or 76%, which is way above the default threshold of 25% and represents potential waste of a beneficial effect. You could have avoided this scenario by using a sample size that kept the overall Type 1 and 2 errors to <0.5% and <25%. For the worst case of independent effects that are on the borderline for making a decision one way or the other, the spreadsheet provides the sample size when you set the Type 1 and 2 errors to 0.5/n% and 25/n%, where n is the number of independent effects. (These values are approximations; exact values are 100[1 – [1e/100]^{1/n}], where e is the Type 1 or 2 percent error, but the simpler formulae are accurate enough.) The same formulae apply when estimating sample size with Type I and II statistical errors. For two effects the spreadsheet shows that sample size needs to increase by nearly 50%, and for four effects the sample size needs to be doubled. If the effects are not independent, for example in a study where you intend to choose the best of three or more treatments, sample size usually does not need to be increased to the same extent. Exactly how big it should be is difficult to estimate, so err towards studying too many subjects rather than too few. • Sample size for a case series is not included in the spreadsheet. A case series is aimed at establishing norms of specific measures to allow confident characterization of future cases relative to the norms. (Cases can also refer to normal subjects, if the aim is to characterize a subject characteristic, such as a skill.) Assuming the measure or an appropriate transform is normally distributed, norms are established with a mean and SD estimated with adequate precision. The uncertainty in the mean needs to be less than the default of 0.2 SD, which is achieved with a sample size onequarter that of a crosssectional study, or about 70 subjects for 90% confidence limits. This sample size also gives uncertainty of ´¤¸1.15 for the SD, which is sometimes used as the smallest important difference in an SD. Smaller sample sizes establish noisier norms, which result in less confident characterization of future typical cases but acceptable characterization of future unusual cases. Larger samples are needed to characterize percentiles accurately, especially when the measure is not normal distributed. • The number of repeated observations in a singlesubject study is analogous to the sample size for a samplebased study and can be estimated using the same procedures. Sample size in principle should be increased to take account of autocorrelation between repeated observations, but it is reasonable to assume that the model in the analysis removes most of the autocorrelation from the residuals and therefore that the sample size need not be increased substantially. The smallest important effect used in the calculation should be the same as for a samplebased study, because the effects that matter for a single subject are still the same as for subjects in general. • Measurement studies, which characterize validity and reliability of any measures and factor structure of psychometric inventories, are not included in available software for estimating sample size. Sample size for such studies shows a dependence on magnitude similar to that for the other designs. Very high reliability or validity (observed error << smallest important effect) can be characterized with as few as 10 subjects, because the upper confidence limit for the true error is still negligible. More modest observed validity or reliability (correlations ~0.70.9; errors of measurement of ~23´ the smallest important effect) need samples of 50100 subjects for reasonable confidence that the true values of validity or reliability aren't substantially higher or lower than the observed values. Studies of diagnostic tests require hundreds of subjects to ensure adequate sampling of the various subject characteristics that can modify diagnostic accuracy. Studies of factor structure usually need hundreds of subjects, because the alpha reliability of the factors is usually modest. • Sample size for a reliability pilot study aimed at determining error of measurement for estimation of sample size in a repeatedmeasures main study. Sample size in the main study is inversely proportional to the square of the error of measurement. It follows that uncertainty in the error of measurement estimated in the pilot study is magnified into uncertainty in the sample size needed for the main study. For example, to limit the uncertainty in the estimate of sample size in a repeatedmeasures study to no more than ±20% (or a ´¤¸ factor of 1.20), the uncertainty in the estimate of error has to be ±9.5% (´¤¸√1.20). If "uncertainty" is 90% confidence limits, the spreadsheet for confidence limits (Hopkins, 2007) shows that the sample size for the reliability study has to be 174, which is unrealistically high. The smaller sample sizes of <50 that researchers often use in reliability studies is justifiable only if the resulting estimate of sample size in the main study turns out to be ~1020, because the uncertainty in the estimate of such small sample sizes (e.g., ´¤¸1.70 if the pilot study had 20 subjects) can be accommodated by increasing the sample size in the main study by ~510 subjects. • Use of simulation to determine sample size for complex designs or analyses, especially those involving nonlinear models or combinations of repeated measurements or other correlated dependent variables. You make reasonable assumptions about errors and relationships between the variables. You then generate data sets of various sizes using appropriately transformed random numbers to represent the errors and relationships. Finally you analyze the data sets to determine the sample size that gives acceptable width of the confidence interval. An advantage of this approach is that you have to consider carefully the nature of the data and the intended analysis before you begin, which could lead to improvements in the design. It also provides the ideal vehicle for a sensitivity analysis, in which you explore how changes in parameters and errors affect the outcome statistic. In conclusion, it is important to point out that the approaches to samplesize estimation described here provide estimates based on inferences about a population mean effect. When the effect is an intervention, the outcome for an individual receiving the intervention will be different from the mean effect and will depend on individual responses to the intervention. To calculate chances of benefit and harm for the individual, we therefore need a sample size that characterizes individual responses adequately. As yet there is no spreadsheet and, as far as I know, no published formulae for this purpose. I have created a slideshow to summarize most of the above principles, which you can download in Powerpoint or PDF format. You should view the slideshow as a fullscreen presentation, especially for those slides explaining the statistical basis of the traditional and new approaches. The spreadsheet itself has extensive comments. References
Batterham AM, Hopkins WG (2005b). A decision tree for controlled trials. Sportscience 9, 3339 Hopkins WG (2004). How to interpret changes in an athletic performance test. Sportscience 8, 17 Hopkins WG (2006b). Magnitude matters. Sportscience 10, 58 Taubes G (1995). Epidemiology faces its limits. Science 269, 164169 Updated,
reviewed and published Apr 2007.
Updated and reviewed Oct 2007, Nov 2007, Mar 2008, Jun 2011, Jun 2013, Aug 2014. 