Robust Statistical Methods for Empirical Software Engineering
Abstract
There have been many changes in statistical theory in the past 30 years, including increased evidence that nonrobust methods may fail to detect important results. The statistical advice available to software engineering researchers needs to be updated to address these issues. This paper aims both to explain the new results in the area of robust analysis methods and to provide a largescale worked example of the new methods. We summarise the results of analyses of the Type 1 error efficiency and power of standard parametric and nonparametric statistical tests when applied to nonnormal data sets. We identify parametric and nonparametric methods that are robust to nonnormality. We present an analysis of a largescale software engineering experiment to illustrate their use. We illustrate the use of kernel density plots, and parametric and nonparametric methods using four different software engineering data sets. We explain why the methods are necessary and the rationale for selecting a specific analysis. We suggest using kernel density plots rather than box plots to visualise data distributions. For parametric analysis, we recommend trimmed means, which can support reliable tests of the differences between the central location of two or more samples. When the distribution of the data differs among groups, or we have ordinal scale data, we recommend nonparametric methods such as Cliff’s δ or a robust rankbased ANOVAlike method.
Keywords
Empirical software engineering Statistical methods Robust methods Robust statistical methods1 Introduction
In 1996, the first author of this paper wrote a book on software metrics (Kitchenham 1996). In the book chapter addressing statistical methods, her advice was to use box plots to visualize data. Box plots are based on the median and fourth statistics (which are similar to quartiles), so are more robust than any graphics based on means. If data were nonnormal, she advised the use of nonparametric methods such as KruskalWallis rank tests to compare multiple samples. With more complicated designs she advised using analysis of variance methods (ANOVA) with transformations if necessary.
Other software engineering researchers preferred to avoid the nonparametric tests relying on the Central Limit Theorem, which proves that for any set of N identically distributed variables, the mean of the variable values will be approximately normal, with mean, μ, and variance, σ ^{2}/N. The Central Limit Theorem provides the justification for use of methods based on the normal distribution to handle small samples, such as ttests. Their choice was justified by the observation that simulation studies had suggested the ttest and ANOVA were quite robust even if some of the variances within groups differed (Box 1954).
In this paper, we discuss more recent studies of the t and F tests that show that if data sets are not normal (that is the data sets do not originate from a Gaussian distribution), the statistical tests may not be trustworthy. Statistical hypothesis testing can make two kinds of error. Type I errors occur when we reject the null hypothesis when it is in fact true, which is also called a false positive. Conventionally statisticians choose a probability level they believe is acceptable for a Type I error, which is referred to as the αlevel. It is usually set to values of 0.05 or 0.01. Type II errors occur when we fail to reject the null hypothesis when it is in fact false, which is also called a false negative. Statisticians usually prefer the probability of a Type II, which is referred to as the βlevel to be 0.2 or less. A related concept is statistical power which is the probability of correctly rejecting the null hypothesis, so that p o w e r=1−β. Although the probability of either type of error is decreased by using larger sample sizes, aiming for a very low αlevel given a predetermined sample size will increase the achieved βlevel and reduce power. Studies of classical statistical tests under conditions of nonnormality have shown that the assumed α levels of tests are likely to be incorrect, and the power of various tests may be unacceptably low.
In a study of 440 largesample achievement and psychometric measures data sets, Micceri (1989) found all to be significantly nonnormal. He noted that data values were often discrete, while distributions exhibited skewness, multiple modes, long tails, large outlying values and contamination. In our experience, similar issues affect software engineering data sets.^{1} The prevalence of nonnormal data sets and recent studies showing poor performance of classical statistical tests on such data sets, suggest that empirical software engineers need a major rethink of the techniques used for statistical analysis. Recent statistical studies have not only identified analysis problems, they have also introduced methods of addressing these problems. In this paper we identify a number of robust methods that address the problems associated with nonnormal data.^{2}
“... experience and further research have forced us to recognize that classical techniques can behave badly when the practical situation departs from the ideal described by such assumptions.”

An emphasis on understanding the data using graphic representations of the data.

A focus on tentative model building and hypothesis generation as opposed to confirmatory analysis.

Use of robust measures.

Positions of skepticism and flexibility regarding which techniques to apply.

Resistant measures and methods are those that provide insensitivity to localized misbehavior in data. Resistant methods pay attention to the main body of the data and little to outliers.

Robust methods are those that are insensitive to departures from assumptions related to a specific underlying model.
Tukey and his colleagues preferred robust and resistant methods to nonparametric methods. They point out that distributionfree methods treat all distributions equally, but robust and resistant methods discriminate between those that are more plausible and those that are less plausible. To distinguish their approaches from classical methods, they introduced new terms such as batch as an alternative to sample and fourths as opposed to quartiles. Currently few of these terms are still in use with the exception of fourths, which are used in the context of box plots. In this paper we will introduce methods that arose from EDA concepts (specifically central location measures related to the median and trimmed means) but will also emphasize the use of robust nonparametric methods as viable alternatives to parametric analysis. An important issue raised in this paper is that under certain conditions nonparametric rankbased tests can themselves lack robustness.
We illustrate the new methods using software engineering data and analyse the results of a large scale experiment as an example of the use of these techniques. However, before considering the robust analysis methods, we introduce the use of kernel density plots as a means of visualising data. These can provide more information about the distribution of a data set than can be obtained from box plots alone.
Other researchers have started to adopt the robust statistical methods discussed in this paper, e.g., Arcuri and Briand (2011), ElAttar (2014), Madeyski et al. (2014) and Madeyski et al. (2012). In particular, Arcuri and Briand (2014) have undertaken an important survey of statistical tests for use in assessing randomized algorithms in software engineering. We agree with many of their recommendations (particularly their preference for nonparametric methods), but, in this paper, we focus on approaches suitable for relatively small samples such as those obtained from humanbased experiments, or algorithms that give rise to relative small data sets (such as project cost estimation models), rather than the large data sets they discuss. The main contribution of this paper is to provide an overview of the techniques with extended examples of their use and an introduction to the underlying theory. In addition, based upon using the open source R statistical programming language (R Core Team 2015), the reproducer R package by Madeyski (2015) complements this paper, as well as the paper by Jureczko and Madeyski (2015), with the aim of making our work reproducible by others (Gandrud 2015). All of our data sets are encapsulated in the reproducer R package we have created and made available from CRAN – the official repository of R packages. All of the figures in the paper (except the figures in Appendices A and B, which do not depend on data sets collected by us) are built on the fly from data sets stored in the reproducer package.
2 Problems with conventional statistical tests
In this section we summarise the results of studies that have investigated the performance of parametric and nonparametric statistical tests under conditions of nonnormality. These studies identify some of the problems that can occur when using conventional statistical tests on data exhibiting characteristics found in real data sets.
2.1 Parametric tests

The lower tail probability of a Type I error is 0.11 rather than 0.05.

The upper tail probability of a Type I error is 0.02 rather than 0.05.
Wilcox and Kesleman also investigated what would happen if the distribution was skewed and had heavy tails (i.e., a relatively large number of outliers). In this case, with n=20 and a normal distribution, there is a .95 probability that t will be between −2.09 and 2.09 but the actual distribution based on 5000 samples, had 0.025 and 0.975 quantiles of −8.5 and 1.29 respectively. With n=300, the quantiles were −2.50 and 1.70 compared with theoretical values (under normality) of −1.96 and 1.96 respectively.
There are also problems with “contaminated” normal distributions where the majority of the data comes from one distribution and a small percentage of the data comes from a distribution with a much larger variance. In this case, the variance is larger than the uncontaminated distribution, which means that the standard deviation is relatively large and the presence of the outliers that cause the variance inflation may be masked. Variance inflation will also increase the likelihood of Type II errors.
In the twosample case, if, the two groups exhibit the same amount of skewness and sample sizes are equal, the t test should perform correctly because the difference between the mean values should be distributed symmetrically. However, empirical studies summarised by Wilcox (2012) confirm that if distributions vary in shape, Type I errors may be incorrect.

Group sizes are equal.

Data in each group are normally distributed.

Sample sizes are not small, where small was defined as a sample size of n<15 in each group.

Data were normal and sample sizes were unequal for two or more groups.

Data were normal, sample sizes were the same and there were four or more groups.

Data were nonnormal when comparing two or more groups even if sample sizes were equal.

We need large sample sizes to avoid problems with nonnormal data.

With small samples and nonnormal data, t tests might be very problematic.

Data distributions exhibiting combinations of nonnormal properties usually have more severe problems than distributions with only one nonnormal property.

Except under specific conditions, the classical parametric t and F tests are vulnerable to nonnormality and heteroscedasticity.
Overall the problem is that, although the Central Limit theory confirms that (under most practical situations) the mean of a sample is distributed normally, there are no such guarantees about the variance of a sample. With messy data sets, estimates of the variance may be far from reliable, rendering unreliable any statistical tests, such as the t test, that rely upon knowing the variance of a mean value.
2.2 Nonparametric tests
Given that there might be problems with parametric tests, what about the nonparametric methods? Unfortunately, simulation studies have shown that the large sample approximation for the MannWhitneyWilcoxon (MWW) tests and KruskalWallis test are strongly affected by unequal variances, even if sample sizes are equal. In fact they can be less robust than the standard t test, see Zimmerman and Zumbo (1993) and Zimmerman (2000).
Furthermore, problems with the rankmethods can affect the results of statistical packages and can make the difference between finding a significant result and finding a nonsignificant result. Bergmann et al. (2000) compared the results of the MWW test for nonnormal data provided by 11 different statistical packages. They note that the different packages delivered p values ranging “from significant to nonsignificant at the 5 % level, depending on whether a largesample approximation or an exact permutation form of the test was used and, in the former case, whether or not a correction for continuity was used and whether or not a correction for ties was made”. They concluded that “the only accurate form of the WilcoxonMannWhitney procedure is one in which the exact permutation null distribution is compiled for the actual data”.
The equations for the mean and variance of ranks make it clear that, unlike the mean and variance of the raw variables, ranks can never converge to a finite mean and variance. As the number of observations increase, the mean and variance of the ranks increase. Furthermore, if sample sizes are unequal and the null hypothesis is false (i.e., the groups differ), we are almost certain to find large differences in the variances of each group. This variance instability makes applying the large sample tests, which are equivalent to applying the t test (or the F test for multiple groups) to the ranks, very unreliable. This is the reason why the rank transform process proposed by Conover and Imam (1981) is invalid.^{3} In addition, the values of U and W depend on the number of observations, so they do not lead to a meaningful effect size.
Looking back to the definition of U, we can see that it is related to the probability that a random observation from one group is larger than a random observation from another group. Other more reliable nonparametric effect sizes are based on normalising U with respect to the sample size and are discussed in Section 3.3.
3 Robust statistical methods
Firstly we consider the use of kernel density plots to visualise the distribution of data sets. Then, we present various robust statistical methods described by Wilcox (2012), who also provides R algorithms implementing them at his website.^{4}
3.1 Kernel density plots
In the past, Kitchenham recommended the use of box plots to give researchers an overview of the distribution of a data set, which could alert them to potential problems of nonnormality.^{5} Now, we believe that advice to be incorrect, and that kernel density plots are often preferable. Kernel density plots are derived from smoothing histograms. Algorithms that construct kernel density plots are available in the R language (R Core Team 2015).
It shows the box plots of the percentage of classes that need to be tested to find 80 % of the defects using a simple productbased model and an advanced model including a process metric. The data is based on 34 software projects (Madeyski and Jureczko 2015; Madeyski 2015). Looking at the box plots of the raw data many of us would believe it was acceptable to use a paired ttest to determine whether the advanced algorithm was better than the simple algorithm (that is, required fewer classes to find 80 % of defects). It is not until we view the box plot of the difference between the raw data values in Fig. 3c that we see any indication of the problem with this data set.
Overall these examples suggest that the use of kernel density plots and histograms are more likely to alert us to nonnormal data than box plots, but box plots can also provide useful additional information.
3.2 Robust parametric methods
One of the most wellknown robust metrics of central location is the median. It is, however, not ideal. Although the median is robust, it ignores all but one or two observations. This means that estimates of the standard error of the median are not efficient. They may also be unreliable if there are duplicate values in the data. Price and Bonett (2001) have evaluated several estimators of the sample median and proposed a new estimator that tends to have the smallest bias.
 1.
Outlier detection methods based on means and standard deviations can fail to detect outliers.
 2.
When extreme values are discarded, the remaining observations are no longer independent, which invalidates the calculation of the standard error.
3.2.1 Robust measures based on outlier detection
Initially, MADN is constructed using the median of the raw data. If the estimation process is stopped at that point M _{ e s t } is referred to as the onestep M−estimator (MOS). However, M _{ e s t } can be iteratively refined by substituting the current value of M _{ e s t } for the median when calculating MADN in the next iteration. We explain the theoretical justification for M _{ e s t } in Appendix A. Wilcox provides a bootstrap method for calculating the standard error of M _{ e s t }, but this must be treated with caution unless our data set is a random sample from a defined population.
Omitting the term 1.28(M A D N)(i _{2}−i _{1}) and replacing the criterion for identifying an outlier with k=2.24, leads to another estimate called the modified one step Mestimator (MOM). Wilcox notes that MOS is better in terms of the size of the standard error, but MOM has advantages when using small sample sizes to test hypotheses. Wilcox provides a bootstrap method for calculating the confidence limits of MOM but does not provide an estimate of the standard error.
3.2.2 Trimmed and Winsorized means
Winsorized means are derived by replacing the X % lowest observations with the value of the X % quantile and X % largest observations with the value of the (100−X) % quantile. This is referred to as Winsorizing the data. All observations with subscripts lower than i _{ b o t t o m } are replaced by the value of the observation with subscript equal to i _{ b o t t o m }. All observations with subscript greater than i _{ t o p } are replaced by the value of the observation with the subscript i _{ t o p }.
3.2.3 Examples of robust measures of central location and spread
The goal of robust measures of central location and spread is to be resistant to “misbehaviour in the data”. We identify the mean as nonrobust because one very large abnormal value could make the mean value abnormally large. In contrast, the median is considered robust because one very large abnormal value would not have any effect on the median. This property is shared by all the other robust metrics discussed in Sections 3.2.1 and 3.2.2 which either remove abnormally large and abnormally small values or replace them. However, unlike the data sets used in our examples, in industry data sets are not static. They grow as new projects are completed and existing products are updated. To investigate the impact of data set growth, we look at how the robust metrics behave when the largest value is removed
Central location and scale measures for the Effort Data with and without maximum value
Metric name  Central location  Standard error  Central location without maximum (%age Change)  Standard error without maximum (%age Change) 

Mean  7678.2895  1157.4953  7165 (6.68 %)  1065.8918 (7.91 %) 
Median  5430  1522.0595  4830 (11.05 %)  1626.3678 (6.85 %) 
MEstimator  6634.2307  1560.7222  6206.4239 (6.45 %)  1484.903 (4.86 %) 
MOS  6634.2307  NA  6206.4239 (6.45 %)  NA 
MOM  6377.2857  NA  5658.697 (11.27 %)  NA 
20 % Trimmed Mean  6123.4583  1414.9294  5756.3043 (6 %)  1403.2146 (0.83 %) 
20 % Winsorized Mean  6796.0263  1365.7145  6573.8649 (3.27 %)  1377.7016 (0.88 %) 
Considering first the metrics derived from the full data set, we see that, as might be expected in a highly skewed data set, the mean is the largest of the central value metrics and the median is the smallest. The M _{ e s t }, MOM and MOS are all derived in a similar way and all have similar values, in fact M _{ e s t } and MOS have identical values. The mean has the smallest standard error while the standard error of the other metrics (for which standard errors can be calculated) are similar.
Looking at the impact on the metrics after removing the maximum value from the data set, we can see that all the values have been reduced. The median has exhibited the largest percentage change (11 %). This might be considered unexpected because the median is supposed to be resistant to changes at the extremes of the data set. It occurs because the values in the data set consist of only 38 data points, which are spread over a very large range of values (from 460 to 26670). The data points in the centre of the data set are not close together, so when a data point is removed, it causes a large fluctuation in the median. Originally, the median was calculated as the average of the two central values (5430=(4830+6030)/2), once the maximum was removed the median became the central value of the remaining 37 values which is 4830.
Of the other metrics, most exhibited a change of between 6 % and 7 %, including the mean. The mean was not as affected by the removal of the largest value as might be expected because there were a relatively large number of large values in the data set. In this case, the Winsorized mean exhibited the smallest change because with 38, the observation with i _{ t o p }=31 corresponded to an observation with value 14568. Once the maximum value was removed, the value of i _{ t o p }=30 corresponded to an observation with the value 14504, corresponding to a very small 0.4 % change in the maximum value of the Winsorized data set. In terms of the effect of removing the maximum value on the standard error, as expected, the standard error of the mean exhibited the largest change, and the standard error of the trimmed mean exhibited the smallest change.
Central location and spread of productivity data with and without the maximum value
Metric name  Central location  Standard error  Central location without maximum (% age Change)  Standard error without maximum (% age Change) 

Mean  0.2725  0.0316  0.2568 (5.78 %)  0.0278 (11.96 %) 
Median  0.1923  0.0387  0.192 (0.17 %)  0.0283 (26.98 %) 
MEstimator  0.2251  0.0313  0.2206 (2.03 %)  0.0298 (4.83 %) 
MOS  0.2256  NA  0.2209 (2.08 %)  NA 
MOM  0.203  NA  0.203 (0 %)  NA 
20 % Trimmed Mean  0.2092  0.0291  0.2033 (2.82 %)  0.0256 (11.74 %) 
20 % Winsorized Mean  0.2259  0.0284  0.212 (6.17 %)  0.0254 (10.81 %) 
Given the properties of this data set it is not surprising to find that the mean exhibits a large change when the maximum value is removed and the median exhibits only a small change. In this case, the Winsorized mean exhibits the largest change. This is because with the full data set, N=63, and the value of i _{ t o p } was 51 corresponding to an observation with the value 0.4333. Once the maximum value was removed, the value of i _{ t o p } was 50 corresponding to an observation with the value 0.3786. This corresponded to a relatively large 12.6 % change in the maximum value of the Winsorized data set. In this case, most of the standard errors exhibited a relatively large change with the change to the median standard error being the largest (27.0 %).
These examples, might suggest that resistance is a somewhat relative concept in the context of evolving data sets and depends on the specific nature of a data set. However, they confirm that for skewed data with outliers, the trimmed mean will be closer to the central point of the data set than the mean and will usually be smaller than the M−E s t i m a t o r, MOS or MOM. It will also usually have a smaller standard error than the mean, even though the divisor (and associated degrees of freedom) will be based on N(1−0.0X) rather than N.
However, the real importance of using trimmed means and other robust parametric measures is that they allow nonnormal data to be analysed fairly on the raw data scale. This is particularly important for ratiobased measures that are known to be strongly skewed, such as productivity (effort/size) or defect rates (faults/size). In spite of the extreme nonnormality of such data, practitioners still prefer to use average productivity metrics based on the raw data, for example, to set up baselines and identify good practice, see for example Huijgens et al. (2013).
The problem with using the mean is that with skewed data more than 50 % of projects have productivity values less than the mean. In the COCOMO productivity data, 62 % of the projects had productivity values less than the mean productivity value. Using the mean value gives an inflated value to the central location of the data set, as a result of the large values. The median is much smaller than the mean and 49 % of the projects are less than the median. However, since the median is only based on one or two values (depending on whether the data set has an odd or even number of observations), it is hard to defend the median as a trustworthy measure. In contrast to the mean, 54 % projects had productivity values less than the trimmed mean. Furthermore, since the trimmed mean is based on 60 % of the data set it is a more defensible estimate of the central location than the median.
The practical implication is that benchmarking initiatives that label projects with values less than the mean as poorlyperforming projects might justifiably be rejected by project managers whose projects performed better than the median. In the case of the COCOMO productivity data, five projects had values greater than the trimmed mean but less than the mean. Furthermore, if the data did not include the largest value, none of the projects would change from being classified as above the trimmed mean to below the trimmed mean.
We would also suggest that projects within plus or minus two standard errors of the trimmed mean should be considered as exhibiting average productivity. Using this criterion, the trimmed mean would classify projects with order statistics i=28 to i=39 as being average, and there would be no change if the largest value were removed. In contrast, using the mean and its standard error, the nine projects with order statistics i=35 to i=43 would be classified as average, and if the largest value were removed, the mean would classify the 8 projects with order statistics i=36 to i=43 as being average. Bearing in mind that the median value corresponds to the project with order statistic i=32, it is clear that using the trimmed mean identifies more projects close to the centre of the distribution as average than does the mean.
To identify poorly and exceptionally performing projects, observations with productivity values less than the value of the observation corresponding to i _{ b o t t o m } could be described as poorly performing (in the COCOMO example, the observation with i=13 which had a value 0.07266 corresponded i _{ b o t t o m }). Equally, projects with productivity values greater than the value of the observation corresponding to i _{ t o p } could be described as exceptionally performing projects (in the COCOMO example the observation with i=51 which had a value 0.4333 corresponded to i _{ t o p }). (Huijgens et al. 2013) point out the value of investigating whether poorly performing projects and exceptionally performing projects have specific characteristics. In the case of the COCOMO productivity data, all of the poorly performing projects were categorized as embedded projects, while the projects with the six largest productivity values were all classified as organic projects and the remaining six exceptionally performing products were classified as semidetached projects. In the next section, we follow up the issue of the impact of project type on productivity in order to demonstrate how trimming can be used to test hypotheses about nonnormal data sets on the raw data scale.
Another important issue is that robust measures of spread can be generalised into robust measures of covariance. This leads to the ability to undertake multivariate analysis and robust regression analysis of nonnormal data sets without relying on normalising transformations. Although it is beyond the scope of this paper, Wilcox (2012) discusses multivariate methods and robust regression extensively.
3.2.4 Robust alternatives to t and F tests
The problem associated with heteroscedasticity among different samples has been known for a long time. Welch (1938) proposed a variant of the ttest that allowed for different variances within each group. This is the default version of the t–test in R (R Core Team 2015).
Yuen’s method is appropriate when testing for differences between central locations, but would not be sensitive to changes in the lower tail of a distribution of the kind that can be seen in Fig. 4.
A disadvantage of the use of Yuen’s method is that the use of trimming and Welch’s test means that the number of degrees of freedom are substantially reduced. This will mean we need more observations. However, if our data are not normal, we will also need a great many observations before we can be sure that results based on the full data set are reliable.
As an example of this approach, consider the original COCOMO data set (Boehm 1981). As discussed in Section 3.2.3, the projects were divided into three different types (referred to as the project mode), labelled organic, embedded and semidetached. Using this data it is possible to test whether the productivity of projects of each type is the same.
COCOMO project productivity summary statistics
Project type  # Projects  Mean  SE  Trimmed mean  TM SE 

Organic  23  0.4368  0.0625  0.3901  0.0718 
Semidetached  12  0.291  0.0482  0.285  0.0375 
Embedded  28  0.1296  0.0233  0.1052  0.0133 
Using Yuen’s method, an overall Ftest for differences among the three groups of projects was statistically significant (F=18.678, d f _{1}=2,d f _{2}=14.74,p=9.100371e−05). Although there are 28 embedded projects, 12 semidetached projects and 23 organic projects, the degrees of freedom for the denominator of the Ftest is 14.74 rather than the 60 that would be found in a standard analysis of variance. This is because 40 % of the data is removed by trimming and the use of Welch’s method for unstable variances further reduces the degrees of freedom and results in noninteger values for degrees of freedom.
COCOMO project productivity group comparisons
Comparison  TM difference  Lower 95 % CL  Upper 95 % CL  df 

E v SD  −0.1798  −0.2863  −0.0733  8.8933 
E v O  −0.2849  −0.4664  −0.1034  14.9841 
SD v O  −0.1051  −0.3004  0.0902  19.6753 
The value of the linear combination of trimmed means for the COCOMO data is −0.7706 with 95 % confidence limits (−0.2779, 0.1284). This indicates that we cannot rule out the possibility of a linear effect. However, the degrees of freedom for this test is 18.85, which suggests the test has a low power, which is particularly problematic if we want to be confident that the null hypothesis is likely to be true.
3.3 Nonparametric tests
Cliff derived the standard deviation for δ, which can be used to calculate the standard deviation of \(\hat {P}\), since \(var_{\delta }=4var_{\hat {P}}\).
Akritas and Arnold (1994) and Brunner et al. (2002) suggested a different but related method, which also allows for duplicate observations by using midranks. Midranks are necessary if there are two (or more) observations with the same value, in that case, the observations are both allocated the average of the two (or more) related ranks. Their method is an ANOVAlike method based on ranks but is robust to heteroscedasticity of group variances. It is important because it can be used to analyse much more complicated statistical designs than simple betweengroups designs.
The estimated value of Cliff’s δ is −0.2647 with 95 % confidence interval (−0.4884,−0.0410) on the assumption that the estimate is approximately normally distributed. The test value is −2.319 which has a probability of p=0.0102. This suggests that the predictions made by the advanced defect prediction algorithm have a significant probability of requiring the search of fewer classes than the simple algorithm. This can be compared with the standard Wilcoxon test which reports a p−value of 0.01577 but delivers a warning “cannot compute exact pvalues with zeroes”.
For analysing multiple repeated measures (for example, studies where many different cost estimation algorithms are applied to many different data sets), software engineering researchers have often adopted Friedman’s test with corresponding posthoc tests as recommended by Demšar (2006) (see, for example, Dejaeger et al. 2012). However, in a study of the performance of Friedman’s test, Agresti and Pendergast (1986) found that for an underlying normal distribution, their rank transformed ANOVA test could be substantially more powerful than the Friedman test. In a more recent paper, Tian and Wilcox (2007) compared the AgrestiPendergast method with the ANOVAlike method developed by Brunner and colleagues. They found that under most conditions, the ANOVAlike method was preferable to the AgrestiPendergast method in terms of both Type I errors and power. The exception occurred when there were only two repeated measures for each data set. There has been no direct comparison of the AgrestiPendergast and Cliff’s method for cases where there are only two repeated measures.
3.4 Guidelines for interpreting effect size magnitude
Effect size is a name given to indicators that measure the magnitude of a treatment effect. We agree with Arcuri and Briand (2014) that effect sizes are extremely useful, as they provide an objective measure of the importance of the experimental effect, regardless of the statistical significance of the test statistic. Furthermore, effect sizes are much less affected by sample size than statistical significance and, as a result, are better indicators of practical significance (Madeyski 2010; Urdan 2005; Stout and Ruble 1995).
Cohen (1988, 1992) was the first person to propose interpretation guidelines for effect sizes, by suggesting criteria to define a small, a medium or a large effect for use in the behavioural sciences. However, Cohen did not present any systematic calculation of effect sizes from research studies as the basis for his generalizations. That is why Lipsey and Wilson (2001) found these guidelines somewhat arbitrary, and presented different interpretations of the magnitude of effect sizes based on the distribution of effect sizes for over 300 metaanalyses of psychological, behavioural, and education studies, suggesting the need for domain specific guidelines.
To allow an interpretation of effect sizes in a software engineering context, Kampenes et al. (2007) therefore proposed magnitude labels based on a systematic review of effect size in 92 software engineering controlled experiments. The sample size is limited but gives a rough estimation of what constitutes small, medium and large effect sizes in the software engineering domain.
Guidelines for effect size magnitude interpretation
Effect  small  medium  large 

(Cohen 1988)  
d  0.20  0.50  0.80 
r  0.10  0.243  0.371 
r ^{2}  0.01  0.059  0.138 
(Cohen 1992)  
d  0.20  0.50  0.80 
r  0.10  0.30  0.50 
r ^{2}  0.01  0.09  0.25 
(Lipsey and Wilson 2001)  
d  0.30  0.50  0.67 
(Kampenes et al. 2007)  
g  0.17 [0.00–0.376]  0.60 [0.378–1.000]  1.40 [1.002–3.40] 
r  0.09 [0–0.193]  0.30 [0.193–0.456]  0.60 [0.456–0.868] 
r ^{2}  0.008 [0–0.0372]  0.09 [0.0372–0.208]  0.36 [0.208–0.753] 
Cliffs δ (SRD)  0.112  0.276  0.428 
\(PS (\hat {A_{12}})\)  0.556  0.638  0.714 
An important issue for the use of effect sizes in metaanalysis is that the variance of the effect size needs to be estimated. Effect size variances are often quite complex to calculate, but Wilcox’s software provides standard errors for the Cliff’s d and the probability of superiority (Wilcox 2012).
4 Example derived from a multisite experiment
This section presents a largescale example of an analysis using robust methods. In this section, we will demonstrate three different options for analysing our data. However, this is for explanatory purposes only, we do not advocate trying many methods until finding one that gives the answer you want. We return to this issue when discussing the results of the experimental analysis.
4.1 Background to the multisite experiment
Are software engineering researchers likely to produce clearer and more complete abstracts when these are written using a structured form?
A report on our experiences regarding the organisation of the multisite experiment (referred to using the alternative term distributed experiment) is provided elsewhere (Budgen et al. 2013). In this paper we are only concerned with the analysis of the data that was collected from this and used to assess the above research question.
4.2 Experimental design

Null Hypothesis 1: Structured and conventional abstracts written by software engineering researchers are not significantly different with respect to completeness.

Alternative Hypothesis 1: Software engineering researchers write structured abstracts that are significantly more complete than conventional abstracts.

Null Hypothesis 2: Structured and conventional abstracts written by software engineering researchers are not significantly different with regard to clarity.

Alternative Hypothesis 2: Software engineering researchers write structured abstracts that are significantly clearer than conventional abstracts.
To address these, we asked participants to assess the clarity and completeness of abstracts of scientific papers with an empirical element that were published by a Software Engineering journal that had adopted structured abstracts, comparing them with the clarity and completeness of both abstracts published by the same journal before it adopted structured abstracts, as well as with the abstracts published by a similar journal that did not adopt structured abstracts. This gave us the opportunity to see whether the advantages of structured abstracts we had observed in controlled experiments carried over into the field.
4.2.1 Structure and organisation of the multisite experiment
The abstracts were obtained from academic papers published in the Information and Software Technology journal (IST) and the Journal of Systems and Software (JSS). These software engineering journals are both published by Elsevier, and contain many papers with an empirical content. The important point for our experiment was that IST began mandating the use of structured abstracts in the time period 20092011 whereas JSS retained the use of conventional abstracts.
This experiment is a quasiexperiment because we selected abstracts from particular volumes of the two journals, and could not randomise the source of the structured abstracts. Based on the categories provided by Shadish et al. (2002), the experiment can be classified as “a twogroup pretestposttest design with nonequivalent control groups”. Here the change between pretest and posttest is provided by the transition to the use of structured abstracts over the period 2009–2011 for IST, and the nonequivalent control group is provided by the two blocks of abstracts from JSS.
We conducted the experiment across five sites: Durham and Keele Universities (UK), Lincoln University (New Zealand), the City University (Hong Kong), and the Prince of Songkla University (Thailand). Subsequent to the initial experiment two further sets of data were collected, one from students at City University (Hong Kong) and the other from students at Wroclaw University of Science and Technology (Poland). The experiment was organized by Budgen who prepared the experiment protocol and the experimental materials, circulated the relevant materials to each site, and coordinated the responses.
An EntityRelationship style diagram illustrating the experiment together with an explanation of the entities and their relationships is presented in Appendix B.
4.2.2 Independent and dependent variables
 1.
The source of the abstracts (JSS; IST)
 2.
The time of publication (Block1; Block2) For both journals, these blocks consist of roughly eighteen monthsworth of issues within the period 2009–2011. For JSS, the boundary between blocks was based upon date (mid2010), whereas for IST, where the transition from conventional to structured abstracts was gradual, with many issues having mixed forms, the boundary is across all issues of 2010, with assignment to block being determined by the form of the abstract.
 3.
The location of the study/participants (UK2 sites, NZ, Thailand, HK, Poland)
4.2.3 Participants and their roles
The participants who acted as “judges” of the abstracts were intended to be undergraduate students studying computing in some form, and who were at approximately the same level of technical educational attainment, approximating to two years of specialist computing study at university, but in practice, some universities also recruited participants who were more experienced, see Budgen et al. (2013). These were students who might be expected to read research papers that have abstracts, but who had not yet had to write dissertations and similar documents containing abstracts. Within the English context (Durham and Keele) this would equate to students who were at the end of their second year of study, or beginning their third year of study. For each site, sixteen participants were recruited locally, using local expertise to match them to the above description. Where necessary, we paid a small honorarium to those taking part. Participants were expected to have a reasonable level of English, since the abstracts were in English, and so we collected data about whether or not this was their first language. Figure 16 is a flow diagram showing a highlevel overview of the experimental process undertaken at each site.
Participants were required to act as judges for four abstracts, one taken from IST and one from JSS in the time period prior to the introduction of structured abstracts and one from IST and one from JSS in the time period following the adoption of structured abstracts by IST. In addition, each abstract was evaluated by four judges. A flow diagram of the experimental process from the viewpoint of the judges is shown in Fig. 17.
4.2.4 Experimental materials
Allocation of abstracts to blocks
Id  IST organisation  No.  JSS organisation  No. 

Block 1  All 2009; conventional (2010)  110  All 2009; Jan–June (2010)  132 
Block 2  Structured (2010); all 2011  131  Jul–Dec (2010); all 2011  173 
All IST  241  All JSS  305 
Budgen then created a set of four random number sequences, based on the size of each of the blocks of abstracts. The first four values from each sequence were used to select the abstracts for the first site, the next four for the second site and so on until he had selected 20 abstracts from each journal and each block. In the second data collection activity (from the universities in Hong Kong and Poland), four further abstracts were selected from each journal and block.
All data were collected using paper forms. Budgen prepared a set of data collection forms organized as two A5 sized pages side by side. Each of these had the abstract printed on the right hand page, and the questions on the left hand page. They were also suitably coded so that they could be tracked by the experimenter. To avoid participants guessing which abstract was supposed to be best, Budgen removed the headings from the structured abstracts and revised any sentences rendered ungrammatical by the removal of the headings. In addition, the title and keywords were removed from each abstract.
The questions were derived from those used in the previous studies (Budgen et al. 2011, 2008), with modifications to address the restriction of using only those papers that had an empirical element. For the purpose of data collection, each student judge was required to first complete a consent form, then a short form asking for demographic information, and would then receive the four data collection forms in the defined order,^{11} and one at a time. As they completed a form it was to be returned to the experimenter, who would check that it had been fully completed and then issue the next form. A flow diagram of the process is shown in Fig. 15.
The details of the conduct of the experiment, and of the divergences from the plan that occurred, are described in Budgen et al. (2013). The second data collection exercise used the same set of 16 abstracts at two different universities: one in Hong Kong (the City University) the other in Poland (Wroclaw University of Science and Technology).
4.3 Data analysis
This section examines a number of approaches to analysing the data from the experiment using robust methods.
4.3.1 Preliminary analysis
Agreement among Judges for each site
Phase  Site  MSBA  MSWA  F  p  ICC 

1  Keele  0.0802  0.019  4.2217  0.0001  0.7631 (Substantial) 
1  Durham  0.0673  0.0253  2.6598  0.0052  0.624 (Substantial) 
1  Lincoln  0.0858  0.0227  3.7767  0.0002  0.7352 (Substantial) 
1  Pr. Songkla  0.0409  0.0205  1.9931  0.0362  0.4983 (Moderate) 
1  Hong Kong (CU)  0.0463  0.032  1.4494  0.1636  0.31 (Fair) 
2  Hong Kong (CU)  0.0429  0.0579  0.7404  0.7322  −0.3506 (Poor) 
2  Wroclaw (POLAND)  0.0424  0.025  1.6955  0.0841  0.4102 (Moderate) 
4.3.2 Analysis of the experimental data
The main analysis is in two phases relating to the two data collection periods. In the first phase we analyzed the data from the first 5 sites, in the second phase we used metaanalysis to aggregate the data from both phases.
4.3.3 Phase 1 analysis
Figure 7 shows the kernel density plot of the abstract data from the original 5sites. This is based on the median of the four average completeness scores for each abstract with 20 abstracts per journal/time period group. We use the median since it is more robust than the mean.

Trimmed mean analysis of variance testing a linear combination of the trimmed means.

ANOVAlike rankbased analysis testing the interaction term.

Cliff’s method adapted for differences in differences.

The Time period effect is significant (p = 0.006)

The Journal effect is not significant (p = 0.062)

The Interaction effect is not significant (p = 0.065)
Trimmed means for phase 1 abstract completeness
IST  JSS  

Period 1  0.5104  0.5097 
Period 2  0.6711  0.5439 
Testing the linear contrast directly gives an effect size of 0.1265 with 95 % confidence limits (−0.008293 to 0.2613). The confidence interval spans zero so the effect size is not statistically significant at the p=0.05 level.

The Time period effect is statistically significant with p=0.00091.

The Journal effect is statistically significant with p=0.0153.

The interaction is not statistically significant with p=0.10939.
These results indicate that the completeness of the abstracts is better for the more recent studies and that the interaction term is not significant, which agree with the trimmed mean analysis. However, in contrast to the trimmed mean analysis, the rankbased study suggests that there is a significant journal effect.
Relative effect sizes for phase 1 abstract completeness
IST  JSS  

Period 1  0.4238  0.3731 
Period 2  0.7219  0.4812 
However, the relative effect sizes do not consider the differences in differences effect (that is, they are exactly the same values that would be obtained if the data were treated simply as coming from a one factor experiment with four levels), so cannot act as an effect size for metaanalysis purposes. Without an effect size and the effect size variance, we cannot incorporate data from other independent studies using metaanalysis. For that reason we consider another analysis approach, based on Cliff’s δ.

The Time period effect shows Time period 2 completeness exceeds Time period 1 completeness with δ=0.4065 and 95 % confidence interval (0.1581 to 0.6061)

The Journal effect shows that IST completeness exceeds JSS completeness with δ=0.2912 and 95 % confidence interval (0.02908 to 0.5159).
Cliff’s d for phase 1 abstract completeness
Period 1  Period 2  Difference  

p _{1}  0.5075  0.735  
p _{2}  0.0425  0.02  
p _{3}  0.45  0.245  
d  0.0575  0.49  0.4325 
s _{ d }  0.0374  0.0278  0.0465 
Since \(z_{\frac {\alpha }{2}}=1.96\), the 95 % confidence interval for the difference of the differences is (0.3413, 0.5237). Because the effect size is positive and the confidence interval does not include zero, the difference in difference analysis based on Cliff’s δ suggests that the IST abstracts are more complete than JSS abstracts after the introduction of structured abstracts, after allowing for the fact that the IST abstracts were slightly more complete than the JSS abstracts before the introduction of structured abstracts. This result is inconsistent with the results found by the trimmed mean analysis and the ANOVAlike rankbased method. However, for the purposes of this example we will continue to use Cliff’s approach.
Ciff’s d for phase 1 abstract clarity
Period 1  Period 2  Difference  

p _{1}  0.46  0.5875  
p _{2}  0.1175  0.075  
p _{3}  0.4225  0.3375  
d  0.0375  0.25  0.2125 
s _{ d }  0.036  0.0336  0.0493 
4.3.4 Phase 2 analysis
In this section we analyse the data from Wroclaw University of Science and Technology and discuss how it can be aggregated with the previous data. As previously noted, the second set of data from Hong Kong showed no evidence of consensus about abstract complexity and clarity, so could not be used.

The Time period effect is not statistically significant with p=0.41535.

The Journal effect is not statistically significant with p=0.6621164.

The interaction is not statistically significant with p=0.44237.
Relative effect sizes for phase 2 abstract completeness
IST  JSS  

Period 1  0.4062  0.4609 
Period 2  0.6641  0.4688 
Cliff’s d for phase 2 abstract completeness
Period 1  Period 2  Difference  

p _{1}  0.5  0.6875  
p _{2}  0  0  
p _{3}  0.5  0.3125  
d  0  0.375  0.375 
Ciff’s d for phase 2 abstract clarity
Period 1  Period 2  Difference  

p _{1}  0.8125  0.6875  
p _{2}  0.125  0.0625  
p _{3}  0.0625  0.25  
d  0.75  0.4375  −0.3125 
For completeness, the standard error is large enough to indicate that the effect size is not statistically significant. Furthermore, for clarity the effect size is negative. Thus, analysed by itself the Polish data does not support the hypothesis that structured abstracts improve completeness and clarity. The number of abstracts is clearly insufficient to provide statistically significant results and estimates of d have a large standard error.
The correct way to incorporate the results of data collected after the analysis of an initial tranche of data is via metaanalysis (Braver et al. 2014). Just adding the new data to the existing data set is wrong, since it involves deciding to collect more data after looking at the results (John et al. 2012). Equally, metaanalysis of all six studies is not a valid approach because the five studies in the first tranche were planned in advance (before the experiment) as defined in the protocol. Thus, they are treated as one distributed experiment.
When undertaking a metaanalysis, it is important to decide whether to perform a fixedeffects analysis or a randomeffects analysis. Borenstein et al. (2009) discuss whether metaanalysts should use a fixedeffect or a randomeffect analysis. They suggest a fixed effects analysis is appropriate if two conditions are met. Firstly the analysts believe that all the studies are functionally similar, secondly the goal is to compute the common effect size for the identical population, and not to generalise to other populations. In our case the use of exactly the same protocol and output variables model and the limited goal of our metaanalysis suggest that a fixedeffect size is justified.
Using the R metafor package (Viechtbauer 2010) and a fixed effects analysis, the aggregated effect size, for the completeness data, was estimated to be 0.4315 with 95 % confidence interval (0.3411,0.5219).
For the clarity data, the effect size is reversed, and the fixed effects analysis showed evidence of heterogeneity (Q=4.6908,d f=1,p=0.0303). This suggests that the clarity data results from each data collection period should not be aggregated into an overall effect size using a fixedeffects model.
4.4 Discussion of the multisite example
An important issue arising from the multisite experiment is that analyses performed using the different nonparametric methods gave different results. We must reemphasize that we do not advocate trying every possible method of analysis until finding one that gives a significant result. There needs to be a good reason for rejecting or selecting a specific analysis method.
Since the completeness and clarity metrics used in our experiment are both restricted—completeness to between 0 and 1 and clarity to between 0 and 10, and because the kernel density plots look as if the impact of structured abstracts is to reduce the likelihood of very incomplete abstracts, we would expect the nonparametric analyses to be more reliable than the trimmed mean analysis.

Uses ranks obtained across all groups, which may reduce the rank differences between specific groups.

Includes the midrank values used to cater for tied values while Cliff’s method removes the impact of tied values.

Uses statistical tests that allow for variance heterogeneity between groups but that result in a reduction in the degrees of freedom for the F test.
Median abstract completeness
Period 1  Period 2  

IST  0.5  0.6786 
JSS  0.5156  0.5781 
This suggests that the median score is increased by approximately 0.1 which is equivalent to getting one additional Yes answer in the 8 completeness questions. In contrast, Budgen et al. (2011) observed a median difference between conventional and structured abstracts of just over 0.2 using a similar scoring method. In addition, the abstracts in the Budgen study were all written by undergraduates who would have had little experience of writing abstracts, whereas the abstracts in our multisite experiment were written by the authors of the papers. Authors, even if they were post graduate students, would be more experienced than computer science undergraduates. Thus, the likely impact of using structured abstracts would be greater in the previous study.

Keep the title and keywords with the abstract on the evaluation form to be more consistent with research practice.

Ensure that abstracts selected from JSS and IST for study should come from the same two time periods. The observed increase on completeness between the time periods suggests that we should have ensured that the time periods for both JSS and IST were exactly the same. As it is, there is a risk that any conventional IST abstracts obtained from the last six months of 2010 would have a greater completeness value than earlier conventional abstracts. This would have lead to an increased average completeness for IST period 1 abstracts, which would have reduced the likelihood of detecting a difference in differences effect.

Review the evaluation questions themselves to see whether they can be made more objective. The lower levels of agreement among judges who do not have English as a first language may be a result of the abstracts, but could also be due to problems with the evaluation questions.
Our experimental design is not appropriate for testing hypotheses regarding overall timetrends in abstract completeness. However, our results suggest that the overall quality of abstracts has improved in the second time period for both JSS and IST. This could be explained because general criticisms of abstracts in systematic literature reviews, together with experimental results suggesting structured abstracts were likely to be more complete than conventional abstracts, would probably have increased awareness of the need for good quality abstracts and helped produce an overall improvement. However, to properly test the hypothesis of a general improvement an experiment would need to test the completeness of abstracts across a wide range of journals.
In terms of advantages of nonparametric methods, looking at Fig. 7, the multisite example, suggests that the new nonparametric methods are preferable to conventional analysis methods because they are able to detect changes related to the overall distribution, not just the mean.
5 Discussion
This section summarises arguments in favour of the use of robust statistics and identifies limitations associated with their use.
5.1 Arguments for the use of robust statistics
We have proposed using analysis techniques that are robust to nonnormality when we have reason to believe our data is nonnormal. We have also suggested the use of Kernel density functions to identify empirical distributions that appear nonnormal. However, we have not discussed whether we should use quantilequantile plots (qq plots) or statistical tests to check for normality, nor have we discussed whether it is preferable to transform data.
With respect to qq plots, like kernel density plots, they require the analyst to make a judgment about whether the data is normal (or normal enough) or not. In our view, the kernel density plots are somewhat easier to interpret, but we accept that this is a matter of personal preference.
ShapiroWilk normality test probability for example data sets (data sets available from the reproducer R package (Madeyski 2015))
Data set  Measure  Data set size  pvalue of test  pvalue for log transformed data 

Finnish data  Effort  38  0.0004  0.0653 
Software defect prediction  
Simple model  % Modules  34  0.3917  0.0123 
Advanced model (NDC)  % Modules  34  0.0373  0.0101 
Embedded  Productivity  28  <0.0001  0.7734 
SemiDetached  Productivity  12  0.6135  0.0161 
Organic  Productivity  23  0.0379  0.7103 
Abstract experiment data  
JSS1  Completeness  20  0.0899  0.0017 
JSS2  Completeness  20  0.4853  0.8029 
IST1  Completeness  20  0.3194  0.0658 
IST2  Completeness  20  0.6371  0.2059 
The table shows that the ShapiroWilk test suggests more of the data sets are normally distributed than inspection of the Kernel density plots would indicate. In addition, if we use normality tests and they suggest some groups have normally distributed data and some do not, applying a transformation to all groups (which is necessary for any valid statistical analysis) may reduce the normality of any group which had more or less normal data to begin with. Overall, with relatively small, messy data sets it seems best to err on the side of caution and assume that the data is nonnormal. Under such circumstances adopting robust methods may sometimes be conservative, but using nonrobust analysis methods would make the results of any analysis untrustworthy.

Simple transformations do not guard against low statistical power when dealing with heavytailed distributions.

Simple transformations can alter skewed distributions but do not deal directly with outliers.

They are a compromise between the median (maximum trimming) and the mean (zero trimming).

They are a form of weighted mean.

They are based on excluding the observations that provide least information about the central location.

They are in common use for scoring competitions where performance and style are judged subjectively, for example, scoring diving competitions where the two upper and lower values from seven assessments are discarded.

They are the best way of testing ordinal scale measures. In Software Engineering many of our measures (other than those related to elapsed time) have no physical basis, and are more likely to be ordinal than interval or ratio measures. For example, function points and any measures constructed primarily from subjective assessments. This includes metrics such as the abstract completeness score used in our example in Section 4.

\(\hat {P}\) and δ provide sensible nonparametric effect sizes. Indeed for metaanalysis, Kromrey et al. (2005) report that Cliff’s δ outperformed Cohen’s d and Hedges g statistics.

For purposes of metaanalysis studies, it is possible to convert the MWW U or the Wilcoxon W statistic into \(\hat {P}\) or δ. Although it should be noted that there is some disagreement about terminology. For example, R reports the W statistic (that is, the sum of the ranks of the first group) but labels it U.

\(\hat {P}\) and δ do not suffer from the large scale approximation problems associated with U or W.

Brunner’s and Cliff’s methods are implemented in R source code provided by Wilcox.

Both methods can be used with more complex designs than simple betweengroups designs, including repeated measures designs. The rankbased ANOVAlike approach can be applied to virtually all standard experimental designs, including n by m factorials.
5.2 Limitations of robust statistical methods
If data sets are normally distributed or sample sizes relatively large, the robust methods are less powerful than the standard methods. However, in many cases, the robust methods are designed to be reasonably powerful even if the data are normal, and they are considerably more powerful if the data are not normally distributed or sample sizes are small.
A related issue is that all the robust methods discussed in this paper (with the exception of Cliff’s method) will lead to a reduction in the degrees of freedom available for statistical tests and the construction of confidence intervals. For the parametric methods, trimming which removes large and small data values, and the use of Welch’s test both contribute to a reduction in the degrees of freedom (compare, for example, the number of projects in each Mode type in Table 3 with the degrees of freedom for the trimmed mean statistical test shown in Table 4).
Finally, the use of power analysis to estimate required sample size is more complex for robust methods. In particular, the relationship between degrees of freedom and the group variances in Welch’s test (see (16)) complicates any power analysis for trimmed means or the rankbased ANOVAlike method.
6 Conclusions
Classical statistical analysis methods have limitations when dealing with real data that are skewed, and/or heavytailed, and/or have unstable variances. Box plots can also conceal the extent of nonnormality. We recommend using kernel density plots to inspect the distribution of data.
Parametric tests such as t and F tests are not robust to nonnormality, particularly severe skewness and combinations of nonnormal properties. For comparing the central location of different data sets, we recommend using Yuen’s test based on trimmed means and Welch’s test for unequal variances.
Rankbased methods such as MWW and KruskalWallis have problems when statistical tests are based on large sample approximations for the rank variance. Furthermore, since the U and W test statistics are based on rank averages which increase as the number of observations increase, they do not deliver reliable effect sizes. For analyses that are concerned with general shifts in the distribution rather than changes in the central location or are concerned that their data are naturally ordinalscaled, we recommend using Cliff’s or Brunner et al.’s methods for robust nonparametric methods with Cliff’s δ or the probability of superiority as effect sizes.
Footnotes
 1.
There has not been a systematic review of all publicly available software engineering data sets. However, Whigham et al. (2015) propose the use of the logarithmic transformation for their proposed cost estimation baseline, and suggest that nonNormality is the norm for cost estimation data sets.
 2.
This part of the paper is based on a keynote paper given at the EASE2015 conference (Kitchenham 2015).
 3.
Using the rank transform process, data are converted to ranks and a standard parametric analysis is applied to the ranked data rather than the raw data.
 4.
 5.
There are still many circumstances when a box plot can be extremely useful, for example when comparing a large number of related distributions.
 6.
The theoretical value of the upper (lower) tail of the box plot equivalent is found by multiplying the box length (which calculated as z _{0.75}−z _{.25}) by 1.5 and adding (subtracting) it to the upper fourth (from the lower fourth).
 7.
The adjustment occurs when projects are updated rather than created as new, and is intended to reflect the amount of new/changed lines of code needed to produce the update.
 8.
This equation and the equation for the degrees of freedom are incorrect in Kitchenham (2015).
 9.
 10.
We use d rather than δ when referring to samplebased estimates of δ.
 11.
The order was changed for each group of judges that assessed the same abstract
Notes
References
 Acion L, Peterson JJ, Temple S, Arndt S (2006) Probabilistic index: an intuitive nonparametric approach to measuring the size of treatment effects. Stat Med 25(4):591–602. doi: http://dx.doi.org/10.1002/sim.2256 MathSciNetCrossRefGoogle Scholar
 Agresti A, Pendergast J (1986) Comparing mean ranks for repeated measures data. Communications in Statistics  Theory and Methods 15(5):1417–1433MathSciNetCrossRefzbMATHGoogle Scholar
 Akritas MG, Arnold SF (1994) Fully nonparametric hypotheses for factorial designs i: multivariate repeated measures designs. J Am Stat Assoc 89(425):336–343. doi: 10.1080/01621459.1994.10476475 MathSciNetCrossRefzbMATHGoogle Scholar
 Akritas MG, Arnold SF, Brunner E (1997) Nonparametric hypotheses and rank statistics for unbalanced factorial designs. J Am Stat Assoc 92(437):258–265. doi: 10.1080/01621459.1997.10473623 MathSciNetCrossRefzbMATHGoogle Scholar
 Arcuri A, Briand L (2011) A practical guide for using statistical tests to assess randomized algorithms in software engineering. In: ACM/IEEE international conference on software engineering (ICSE), IEEE. doi: 10.1145/1985793.1985795, pp 1–10
 Arcuri A, Briand L (2014) A hitchhiker’s guide to statistical tests for assessing randomized algorithms in software engineering. Software Testing, Verification and Reliability 24(3):219–250. doi: 10.1002/stvr.1486 CrossRefGoogle Scholar
 Behrens JT (1997) Principles and procedures of exploratory data analysis. Psychol Methods 2(2):131–160CrossRefGoogle Scholar
 Bergmann R, Ludbrook J, Spooren WPJM (2000) Different outcomes of the WilcoxonMannWhitney test from different statistics packages. Am Stat 54(1):72–77Google Scholar
 Boehm BW (1981) Software engineering economics. PrenticeHallGoogle Scholar
 Borenstein M, Hedges LV, Higgins JP, Hannah RR (2009) Introduction to metaanalysis. WileyGoogle Scholar
 Box GEP (1954) Some theorems on quadratic forms applied in the study of analysis of variance problems, i. Effect of inequality of variance in the OneWay classification. Ann Math Stat 25(2):290–302. doi: 10.1214/aoms/1177728786 MathSciNetCrossRefzbMATHGoogle Scholar
 Braver SL, Thoemmes FJ, Rosenthal R (2014) Continuously cumulating metaanalysis and replicability. Perspect Psychol Sci 9(3):333–342. doi: 10.1177/1745691614529796 CrossRefGoogle Scholar
 Brunner E, Munzel U, Puri ML (2002) The multivariate nonparametric Behrens–Fisher problem. Journal of Statistical Planning and Inference 108(1–2):37–53. doi: 10.1016/S03783758(02)002690 MathSciNetCrossRefzbMATHGoogle Scholar
 Budgen D, Kitchenham BA, Charters SM, Turner M, Brereton P, Linkman SG (2008) Presenting software engineering results using structured abstracts: a randomised experiment. Empir Softw Eng 13(4):435–468. doi: 10.1007/s1066400890757 CrossRefGoogle Scholar
 Budgen D, Burn AJ, Kitchenham B (2011) Reporting computing projects through structured abstracts: a quasiexperiment. Empir Softw Eng 16(2):244–277. doi: 10.1007/s1066401091393 CrossRefGoogle Scholar
 Budgen D, Kitchenham B, Charters S, Gibbs S, Pohthong A, Keung J, Brereton P (2013) Lessons from conducting a distributed quasiexperiment. In: 2013 ACM/IEEE international symposium on empirical software engineering and measurement. doi: 10.1109/ESEM.2013.12, pp 143–152
 Cliff N (1993) Dominance statistics: ordinal analyses to answer ordinal questions. Psychol Bull 114(3):494–509CrossRefGoogle Scholar
 Cohen JW (1988) Statistical power analysis for the behavioral sciences, 2nd edn. Lawrence Erlbaum Associates, Hillsdale, New YorkzbMATHGoogle Scholar
 Cohen JW (1992) A power primer. Psychol Bull 112(1):155–159CrossRefGoogle Scholar
 Conover W, Imam RL (1981) Rank transformations as a bridge between parametric and nonparametric statistics. Am Stat 35(3):124–129zbMATHGoogle Scholar
 D’Agostino RB, Belanger A, D’Agostino J, Ralph B (1990) A suggestion for using powerful and informative tests of normality. Am Stat 44(4):316–321Google Scholar
 Dejaeger K, Verbeke W, Martens D, Baesens B (2012) Data mining techniques for software effort estimation: a comparative study. IEEE Trans Softw Eng 38(2):357–397CrossRefGoogle Scholar
 Demšar J (2006) Statistical comparisons of classifiers over multiple data sets. J Mach Learn Res 7:1–30MathSciNetzbMATHGoogle Scholar
 Dybå T, Kampenes VB, Sjøberg DIK (2006) A systematic review of statistical power in software engineering experiments. Inf Softw Technol 48(8):745–755. doi: 10.1016/j.infsof.2005.08.009 CrossRefGoogle Scholar
 ElAttar M (2014) Using SMCD to reduce inconsistencies in misuse case models: a subjectbased empirical evaluation. J Syst Softw 87:104–118. doi: 10.1016/j.jss.2013.10.017 CrossRefGoogle Scholar
 ElAttar M, Elish M, Mahmood S, Miller J (2012) Is indepth objectoriented knowledge necessary to develop quality robustness diagrams? Journal of Software 7 (11):2538–2552. doi: 10.4304/jsw.7.11.25382552 CrossRefGoogle Scholar
 ErcegHurn DM, Mirosevich VM (2008) Modern robust statistical methods an easy way to maximize the accuracy and power of your research. Am Psychol 63 (7):591–601CrossRefGoogle Scholar
 Gandrud C (2015) Reproducible research with R and R studio. CRC PressGoogle Scholar
 Goodall C (1983) Understanding robust and exploratory data analysis. John Wiley and Sons Inc., chap MEstimators of Location: An outline of the theory, pp 339–403Google Scholar
 Grissom RJ (1996) The magical number .7 ± .2: metametaanalysis of the probability of superior outcome in comparisons involving therapy, placebo, and control. J Consult Clin Psychol 64 (5):973–982. doi: 10.1037/0022006X.64.5.973 CrossRefGoogle Scholar
 Hoaglin DC, Mosteller F, Tukey JW (eds) (1983) Understanding robust and exploratory data analysis. WileyGoogle Scholar
 Huijgens H, van Solingen R, van Deursen A (2013) How to build a good practice software project portfolio? Tech. Rep. TUDSERG2013019, Delft University of TechnologyGoogle Scholar
 John LK, Loewenstein G, Prelec D (2012) Measuring the prevalence of questionable research practices with incentives for truth telling. Psychol Sci 23 (5):524–532. doi: 10.1177/0956797611430953 CrossRefGoogle Scholar
 Jureczko M, Madeyski L (2015) Cross–project defect prediction with respect to code ownership model: an empirical study. eInformatica Software Engineering Journal 9(1):21–35. doi: 10.5277/eInf150102 Google Scholar
 Kampenes VB, Dybå T, Hannay JE, Sjøberg DIK (2007) A systematic review of effect size in software engineering experiments. Inf Softw Technol 49(1112):1073–1086. doi: 10.1016/j.infsof.2007.02.015 CrossRefGoogle Scholar
 Kitchenham B (1996) Software metrics: measurement for software process improvement. Blackwell Publishers Inc.Google Scholar
 Kitchenham B (2015) Robust statistical methods: why, what and how: keynote. In: Proceedings of the 19th international conference on evaluation and assessment in software engineering (EASE 2015). doi: 10.1145/2745802.2747956, pp 1:1–1:6
 Kitchenham B, Känsälä K (1983) Interitem correlations among function points. In: Proceedings ICSE 15. IEEE Computer Society Press, pp 477–480Google Scholar
 Kraemer HC, Kupfer DJ (2006) Size of treatment effects and their importance to clinical research and practice. Biol Psychiatry 59(11):990–996. doi: 10.1016/j.biopsych.2005.09.014 CrossRefGoogle Scholar
 Kromrey JD, Hogarty KY, Ferron JM, Hines CV, Hess MR (2005) Robustness in metaanalysis: an empirical comparison of point and interval estimates of standardized mean differences and Cliff’s delta. In: Proceedings of the joint statistical meetings, MinneapolisGoogle Scholar
 Lipsey MW, Wilson DB (2001) Practical metaanalysis. Sage Publications, CaliforniaGoogle Scholar
 Madeyski L (2010) Testdriven development: an empirical evaluation of agile practice. Springer, HeidelbergCrossRefGoogle Scholar
 Madeyski L (2015) Reproducer: reproduce statistical analyses and metaanalyses. http://madeyski.einformatyka.pl/reproducibleresearch, R package (http://CRAN.Rproject.org/package=reproducer)
 Madeyski L, Jureczko M (2015) Which process metrics can significantly improve defect prediction models? An empirical study. Softw Qual J 23(3):393–422. doi: 10.1007/s1121901492417 CrossRefGoogle Scholar
 Madeyski L, Orzeszyna W, Torkar R, Józala M (2012) Appendix to the paper “Overcoming the equivalent mutant problem: a systematic literature review and a comparative experiment of second order mutation”. http://madeyski.einformatyka.pl/download/app/AppendixTSE.pdf
 Madeyski L, Orzeszyna W, Torkar R, Józala M (2014) Overcoming the equivalent mutant problem: a systematic literature review and a comparative experiment of second order mutation. IEEE Trans Softw Eng 40(1):23–42. doi: 10.1109/TSE.2013.44 CrossRefGoogle Scholar
 Micceri T (1989) The unicorn, the normal curve, and other improbable creatures. Psychol Bull 105(1):156–166CrossRefGoogle Scholar
 Mosteller F, Tukey JW (1977) Data analysis and regression: a second course in statistics. AddisonWesleyGoogle Scholar
 Mudholkar GS, Marchetti CE, Lin CT (2002) Independence characterizations and testing normality against restricted skewness–kurtosis alternatives. Journal of Statistical Planning and Inference 104(2):485– 501MathSciNetCrossRefzbMATHGoogle Scholar
 Price RM, Bonett DG (2001) Estimating the variance of the sample median. J Stat Comput Simul 68(3):295–305. doi: 10.1080/00949650108812071 MathSciNetCrossRefzbMATHGoogle Scholar
 R Core Team (2015) R: a language and environment for statistical computing. R foundation for statistical computing, Vienna, AustriaGoogle Scholar
 Ramsey PH (1980) Exact type 1 error rates for robustness of student’s t test with unequal variances. J Educ Behav Stat 5(4):337–349. doi: 10.3102/10769986005004337 MathSciNetCrossRefGoogle Scholar
 Razali NM, Wah YB (2011) Power comparisons of ShapiroWilk, KolmogorovSmirnov, Lilliefors and AndersonDarling tests. Journal of Statistical Modeling and Analytics 2(1):21–33Google Scholar
 Shadish WR, Cook TD, Campbell DT (2002) Experimental and quasiexperimental designs for generalized causal inference. Houghton Mifflin, BostonGoogle Scholar
 Shapiro SS, Wilk M, Chen HJ (1968) A comparative study of various tests for normality. J Am Stat Assoc 63(324):1343–1372MathSciNetCrossRefGoogle Scholar
 Shrout P, Fleiss J (1979) Intraclass correlations: uses in assessing rater reliability. Psychol Bull 86(2):420–428. doi: 10.1037/00332909.86.2.420 CrossRefGoogle Scholar
 Stout DE, Ruble TL (1995) Assessing the practical significance of empirical results in accounting education research: the use of effect size information. Journal of Accounting Education 13(3):281– 298CrossRefGoogle Scholar
 Tappenden AF, Miller J (2014) Automated cookie collection testing. ACM Trans Softw Eng Methodol 23(1):3:1–3:40. doi: 10.1145/2559936 CrossRefGoogle Scholar
 Tian T, Wilcox R (2007) A comparison of two rank tests for repeated measures designs. Journal of Modern Applied Statistical Methods 6(1):331–335Google Scholar
 Urdan TC (2005) Statistics in plain english, 2nd edn. Routledge, Oxon, UKzbMATHGoogle Scholar
 Vargha A, Delaney HD (2000) A critique and improvement of the CL common language effect size statistics of McGraw and Wong. J Educ Behav Stat 25(2):101–132. doi: 10.3102/10769986025002101 Google Scholar
 Viechtbauer W (2010) Conducting metaanalyses in R with the metafor package. J Stat Softw 36(3):1–48CrossRefGoogle Scholar
 Welch BL (1938) The significance of the difference between two means when the population variances are unequal. Biometrika 29(34):350–362. doi: 10.1093/biomet/29.34.350 CrossRefzbMATHGoogle Scholar
 Whigham PA, Owen C, MacDonell S (2015) A baseline model for software effort estimation. ACM Trans Softw Eng Methodol 24(3):20:1–20:11CrossRefGoogle Scholar
 Wilcox RR (1998) How many discoveries have been lost by ignoring modern statistical methods? Am Psychol 53(3):300–314CrossRefGoogle Scholar
 Wilcox RR (2012) Introduction to robust estimation & hypothesis testing, 3rd edn. ElsevierGoogle Scholar
 Wilcox RR, Keselman HJ (2003) Modern robust data analysis methods: measures of central tendency. Psychol Methods 8(3):254–274CrossRefGoogle Scholar
 Yuen KK (1974) The twosample trimmed t for unequal population variances. Biometrika 61(1):165–170CrossRefzbMATHGoogle Scholar
 Zimmerman DW (2000) Statistical significance levels of nonparametric tests biased by heterogeneous variances of treatment groups. J Gen Psychol 127(4):354–364. doi: 10.1080/00221300009598589 CrossRefGoogle Scholar
 Zimmerman DW, Zumbo BD (1993) Rank transformations and the power of the Student t test and Welch t test for nonnormal populations with unequal variances. Canadian Journal of Experimental Psychology/Revue canadienne de psychologie expérimentale 47(3):523– 539CrossRefGoogle Scholar
Copyright information
Open AccessThis article is distributed under the terms of the Creative Commons Attribution 4.0 International License (http://creativecommons.org/licenses/by/4.0/), which permits unrestricted use, distribution, and reproduction in any medium, provided you give appropriate credit to the original author(s) and the source, provide a link to the Creative Commons license, and indicate if changes were made.