# Reanalyzing the Schnall/Johnson “cleanliness” data sets: New insights from Bayesian and robust approaches

[mathjax]

I want to present a re-analysis of the raw data from two studies that investigated whether physical cleanliness reduces the severity of moral judgments – from the original study (*n* = 40; Schnall, Benton, & Harvey, 2008), and from a direct replication (*n* = 208, Johnson, Cheung, & Donnellan, 2014). Both data sets are provided on the Open Science Framework. All of my analyses are based on the composite measure as dependent variable.

This re-analsis follows previous analyses by Tal Yarkoni, Yoel Inbar, and R. Chris Fraley, and is focused on one question: *What can we learn from the data when we apply modern (i.e., Bayesian and robust) statistical approaches?*

The complete and reproducible R code for these analyses is at the end of the post.

Disclaimer 1: This analysis assumes that the studies from which data came from were internally valid. Of course the garbage-in-garbage-out principle holds. But as the original author reviewed the experimental material of the replication study and gave her OK, I assume that the relication data is as valid as the original data.

Disclaimer 2: I am not going to talk about tone, civility, or bullying here. Although these are important issues, a lot has been already written about it, including apologies from one side of the debate (not from the other, yet), etc. For nice overviews over the debate, see for example a blog post by Tal Yarkoni). I am completely unemotional about these data. False positives do exists, I am sure I had my share of them, and replication is a key element of science. I do not suspect anybody of anything – I just look at the data.

, and the summary provided byThat being said, let’s get to business:

## Bayes factor analysis

The BF is a continuous measure of evidence for H0 or for H1, and quantifies, “how much more likely is H1 compared to H0″. Typically, a BF of at least 3 is requested to speak of evidence (i.e., the H1 should be at least 3 times more likely than the H0 to speak of evidence for an effect). For an introduction to Bayes factors see here, here, or here.

Using the BayesFactor package, it is simple to compute a Bayes factor (BF) for the group comparison. In the original study, the Bayes factor against the H0, , is 1.08. That means, data are 1.08 times more likely under the H1 (“there is an effect”) than under the H0 (“There is no effect”). As the BF is virtually 1, data occurred equally likely under both hypotheses.

What researchers actually are interested in is not p(Data | Hypothesis), but rather p(Hypothesis | Data). Using Bayes’ theorem, the former can be transformed into the latter by assuming prior probabilities for the hypotheses. The BF then tells one how to update one’s prior probabilities after having seen the data. Given a BF very close to 1, one does not have to update his or her priors. If one holds, for example, equal priors (p(H1) = p(H0) = .5), these probabilities do not change after having seen the data of the original study. With these data, it is not possible to decide between H0 and H1, and being so close to 1, *this BF is not even “anectdotal evidence” for H1 *(although the original study was just skirting the boundary of significance, *p* = .06).

For the replication data, the situation looks different. The Bayes factor here is 0.11. That means, H0 is (1 / 0.11) = 9 times more likely than H1. A of 0.11 would be labelled “moderate to strong evidence” for H0. If you had equals priors before, you should update your belief for H1 to 10% and for H0 to 90% (Berger, 2006).

*To summarize, neither the original nor the replication study show evidence for H1. In contrast, the replication study even shows quite strong evidence for H0.*

## A more detailed look at the data using robust statistics

Parametric tests, like the ANOVA employed in the original and the replication study, rest on assumptions. Unfortunately, these assumptions are very rarely met (Micceri, 1989), and ANOVA etc. are not as robust against these violations as many textbooks suggest (Erceg-Hurn & Mirosevic, 2008). Fortunately, over the last 30 years robust statistical methods have been developed that do not rest on such strict assumptions.

In the presence of violations and outliers, these robust methods have much lower Type I error rates and/or higher power than classical tests. Furthermore, a key advantage of these methods is that they are designed in a way that they are equally efficient compared to classical methods, even if the assumptions are *not* violated. In a nutshell, when using robust methods, there nothing to lose, but a lot to gain.

Rand Wilcox pioneered in developing many robust methods (see, for example, this blog post by him), and the methods are implemented in the WRS package for R (Wilcox & Schönbrodt, 2014).

### Comparing the central tendency of two groups

A robust alternative to the independent group *t* test would be to compare the trimmed means via percentile bootstrap. This method is robust against outliers and does not rest on parametric assumptions. Here we find a *p* value of .106 for the original study and *p* = .94 for the replication study. Hence, the same picture: No evidence against the H0.

### Comparing other-than-central tendencies between two groups, aka.: Comparing extreme quantiles between groups

When comparing data from two groups, approximately 99.6% of all psychological research compares the *central tendency* (that is a subjective estimate).

In some cases, however, it would be sensible to compare other parts of the distributions.For example, an intervention could have effects only on slow reaction times (RT), but not on fast or medium RTs. Similarly, priming could have an effect only on very high responses, but not on low and average responses. Measures of central tendency might obscure or miss this pattern.

And indeed, descriptively there (only) seems to be a priming effect in the “extremely wrong pole” (large numbers on the x axis) of the original study (i.e., the black density line is higher than the red on at “7″ and “8″ ratings):

This visual difference can be tested. Here, I employed the `qcomhd`

function from the WRS package (Wilcox, Erceg-Hurn, Clark, & Carlson, 2013). This method looks whether two samples differ in several quantiles (not only the central tendency). For an introduction to this method, see this blog post.

Here’s the result when comparing the 10th, 30th, 50th, 70th, and 90th quantile:

1 0.1 20 20 3.86 3.15 0.712 -1.077 2.41 0.0500 0.457 NO

2 0.3 20 20 4.92 4.51 0.410 -0.341 1.39 0.0250 0.265 NO

3 0.5 20 20 5.76 5.03 0.721 -0.285 1.87 0.0167 0.197 NO

4 0.7 20 20 6.86 5.70 1.167 0.023 2.05 0.0125 0.047 NO

5 0.9 20 20 7.65 6.49 1.163 0.368 1.80 0.0100 0.008 YES

(Please note: Estimating 5 quantiles from 20 data points is not quite the epitome of precision. So treat this analysis with caution.)

As multiple comparison are made, the Benjamini-Hochberg-correction for the *p* value is applied. This correction gives new critical *p* values (column `p_crit`

) to which the actual *p* values (column `p.value`

) have to be compared. One quantile survives the correction: the 90th quantile. That means that there are fewer extreme answers in the cleanliness priming group than in the control group

This finding, of course, is purely exploratory, and as any other exploratory finding it awaits cross-validation in a fresh data set. Luckily, we have the replication data set! Let’s see whether we can replicate this effect.

The answer is: no. Not even a tendency:

1 0.1 102 106 4.75 4.88 -0.1309 -0.705 0.492 0.0125 0.676 NO

2 0.3 102 106 6.00 6.12 -0.1152 -0.571 0.386 0.0250 0.699 NO

3 0.5 102 106 6.67 6.61 0.0577 -0.267 0.349 0.0500 0.737 NO

4 0.7 102 106 7.11 7.05 0.0565 -0.213 0.411 0.0167 0.699 NO

5 0.9 102 106 7.84 7.73 0.1111 -0.246 0.431 0.0100 0.549 NO

Here’s a plot of the results:

## Overall summary

From the Bayes factor analysis, both the original and the replication study do not show evidence for the H1. The replication study actually shows moderate to strong evidence for the H0.

If anything, the original study shows some exploratory evidence that only the high end of the answer distribution (around the 90th quantile) is reduced by the cleanliness priming – not the central tendency. If one wants to interpret this effect, it would translate to: “Cleanliness primes reduce extreme morality judgements (but not average or low judgements)”. This exploratory effect, however, could not be cross-validated in the better powered replication study.

## Outlook

Recently, Silberzahn, Uhlmann, Martin, and Nosek proposed “crowdstorming a data set”, in cases where a complex data set calls for different analytical approaches. Now, a simple two group experimental design, usually analyzed with a *t* test, doesn’t seem to have too much complexity – still it is interesting how different analytical approaches highlight different aspects of the data set.

And it is also interesting to see that the majority of diverse approaches comes to the same conclusion: From this data base, we can conclude that we cannot conclude that the H0 is wrong (This sentence, a hommage to Cohen, 1990, was for my Frequentist friends ;-)).

And, thanks to Bayesian approaches, we can say (and even understand): *There is strong evidence that the H0 is true. Very likely, there is no priming effect in this paradigm.*

PS: Celebrate open science. Without open data, all of this would not be possible.

## http://www.nicebread.de

##

## This is a reanalysis of raw data from

## - Schnall, S., Benton, J., & Harvey, S. (2008). With a clean conscience cleanliness reduces the severity of moral judgments. Psychological Science, 19(12), 1219-1222.

## - Johnson, D. J., Cheung, F., & Donnellan, M. B. (2014). Does Cleanliness Influence Moral Judgments? A Direct Replication of Schnall, Benton, and Harvey (2008). Social Psychology, 45, 209-215.

## ======================================================================

## Read raw data, provided on Open Science Framework

# - https://osf.io/4cs3k/

# - https://osf.io/yubaf/

## ======================================================================

library(foreign)

dat1 <- read.spss("raw/Schnall_Benton__Harvey_2008_Study_1_Priming.sav", to.data.frame=TRUE)

dat2 <- read.spss("raw/Exp1_Data.sav", to.data.frame=TRUE)

dat2 <- dat2[dat2[, "filter_."] == "Selected", ]

dat2$condition <- factor(dat2$Condition, labels=c("neutral priming", "clean priming"))

table(dat2$condition)

# build composite scores from the 6 vignettes:

dat1$DV <- rowMeans(dat1[, c("dog", "trolley", "wallet", "plane", "resume", "kitten")])

dat2$DV <- rowMeans(dat2[, c("Dog", "Trolley", "Wallet", "Plane", "Resume", "Kitten")])

# define shortcuts for DV in each condition

neutral <- dat1$DV[dat1$condition == "neutral priming"]

clean <- dat1$DV[dat1$condition == "clean priming"]

neutral2 <- dat2$DV[dat2$condition == "neutral priming"]

clean2 <- dat2$DV[dat2$condition == "clean priming"]

## ======================================================================

## Original analyses with t-tests/ ANOVA

## ======================================================================

# ---------------------------------------------------------------------

# Original study:

# Some descriptives ...

mean(neutral)

sd(neutral)

mean(clean)

sd(clean)

# Run the ANOVA from Schnall et al. (2008)

a1 <- aov(DV ~ condition, dat1)

summary(a1) # p = .0644

# --> everything as in original publication

# ---------------------------------------------------------------------

# Replication study

mean(neutral2)

sd(neutral2)

mean(clean2)

sd(clean2)

a2 <- aov(DV ~ condition, dat2)

summary(a2) # p = .947

# --> everything as in replication report

## ======================================================================

## Bayes factor analyses

## ======================================================================

library(BayesFactor)

ttestBF(neutral, clean, rscale=1) # BF_10 = 1.08

ttestBF(neutral2, clean2, rscale=1) # BF_10 = 0.11

## ======================================================================

## Robust statistics

## ======================================================================

library(WRS)

# ---------------------------------------------------------------------

# robust tests: group difference of central tendency

# percentile bootstrap for comparing measures of location:

# 20% trimmed mean

trimpb2(neutral, clean) # p = 0.106 ; CI: [-0.17; +1.67]

trimpb2(neutral2, clean2) # p = 0.9375; CI: [-0.30; +0.33]

# median

medpb2(neutral, clean) # p = 0.3265; CI: [-0.50; +2.08]

medpb2(neutral2, clean2) # p = 0.7355; CI: [-0.33; +0.33]

# ---------------------------------------------------------------------

# Comparing other quantiles (not only the central tendency)

# plot of densities

par(mfcol=c(1, 2))

plot(density(clean, from=1, to=8), ylim=c(0, 0.5), col="red", main="Original data", xlab="Composite rating")

lines(density(neutral, from=1, to=8), col="black")

legend("topleft", col=c("black", "red"), lty="solid", legend=c("neutral", "clean"))

plot(density(clean2, from=1, to=8), ylim=c(0, 0.5), col="red", main="Replication data", xlab="Composite rating")

lines(density(neutral2, from=1, to=8), col="black")

legend("topleft", col=c("black", "red"), lty="solid", legend=c("neutral", "clean"))

# Compare quantiles of original study ...

par(mfcol=c(1, 2))

qcomhd(neutral, clean, q=seq(.1, .9, by=.2), xlab="Original: Neutral Priming", ylab="Neutral - Clean")

abline(h=0, lty="dotted")

# Compare quantiles of replication study

qcomhd(neutral2, clean2, q=seq(.1, .9, by=.2), xlab="Replication: Neutral Priming", ylab="Neutral - Clean")

abline(h=0, lty="dotted")

*References*

Berger, J. O. (2006). Bayes factors. In S. Kotz, N. Balakrishnan, C. Read, B. Vidakovic, & N. L. Johnson (Eds.), Encyclopedia of Statistical Sciences, vol. 1 (2nd ed.) (pp. 378–386). Hoboken, NJ: Wiley.

Erceg-Hurn, D. M., & Mirosevich, V. M. (2008). Modern robust statistical methods: An easy way to maximize the accuracy and power of your research. American Psychologist, 63, 591–601.

Micceri, T. (1989). The unicorn, the normal curve, and other improbable creatures. Psychological Bulletin, 105, 156–166. doi:10.1037/0033-2909.105.1.156

Schnall, S., Benton, J., & Harvey, S. (2008). With a clean conscience cleanliness reduces the severity of moral judgments. Psychological Science, 19(12), 1219–1222.

Wilcox, R. R., Erceg-Hurn, D. M., Clark, F., & Carlson, M. (2013). Comparing two independent groups via the lower and upper quantiles. *Journal of Statistical Computation and Simulation*, 1–9. doi:10.1080/00949655.2012.754026

Wilcox, R.R., & Schönbrodt, F.D. (2014). The WRS package for robust statistics in R (version 0.25.2). Retrieved from https://github.com/nicebread/WRS

# A comment on “We cannot afford to study effect size in the lab” from the DataColada blog

In a recent post on the DataColada blog, Uri Simonsohn wrote about “We cannot afford to study effect size in the lab“. The central message is: If we want accurate effect size (ES) estimates, we need large sample sizes (he suggests four-digit n’s). As this is hardly possible in the lab we have to use other research tools, like onelin studies, archival data, or more within-subject designs.

While I agree to the main point of the post, I’d like to discuss and extend some of the conclusions. As the DataColada blog has no comments section, I’ll comment in my own blog …

“Does it make sense to push for effect size reporting when we run small samples? I don’t see how.”

“Properly powered studies teach you almost nothing about effect size.”

It is true that the ES estimate with *n*=20 will be utterly imprecise, and reporting this ES estimate could misguide readers who give too much importance to the point estimate and do not take the huge CI into account (maybe, because it has not been reported).

**Still, and here’s my disagreement, I’d argue that also small- n studies should report the point estimate (along with the CI)**, as a meta-analysis of many imprecise small-

*n*estimates still can give an unbiased and precise cumulative estimate. This, of course, would require that all estimates are reported, not only the significant ones (van Assen, van Aert, Nuijten, & Wicherts, 2014).

Here’s an example – we simulate a population with a true Cohen’s d of 0.8. Then we look at three scenarios: a) a single small-*n* study with 20 participants, b) 400 participants, and c) 20 * *n*=20 studies which are meta-analyzed.

set.seed(0xBEEF1)

library(compute.es)

library(metafor)

library(ggplot2)

X1 <- rnorm(1000000, mean=0, sd=1)

X2 <- rnorm(1000000, mean=0, sd=1) - 0.8

## Compute effect size for ...

# ... a single n=20 study

x1 <- sample(X1, 20)

x2 <- sample(X2, 20)

(t1 <- t.test(x1, x2))

(ES1 <- tes(t1$statistic, 20, 20, dig=3))

This single small-*n* study has g = 1.337 [ 0.64 , 2.034] (g is an unbiased estimate of d). Quite biased, but the true ES is in the CI.

This single large-*n* study has g = 0.76 [ 0.616 , 0.903] . It close to the true ES, and has quite narrow CI (i.e., high precision).

Now, here’s a meta-analyses of 20*n=20 studies:

dat <- data.frame()

for (i in 1:20) {

x1 <- sample(X1, 20)

x2 <- sample(X2, 20)

dat <- rbind(dat, data.frame(

study=i,

m1i=mean(x1),

m2i=mean(x2),

sd1i=sd(x1),

sd2i=sd(x2),

n1i=20, n2i=20

))

}

}

# Do a fixed-effect model meta-analysis

es <- escalc("SMD", m1i=m1i, m2i=m2i, sd1i=sd1i, sd2i=sd2i, n1i=n1i, n2i=n2i, data=dat, append=TRUE)

(meta <- rma(yi, vi, data=es, method="FE"))

The meta-analysis reveals g = 0.775 [0.630; 0.920]. This has nearly exactly the same CI width as the n=400 study, and a slightly different ES estimate.

Here’s a plot of the results:

res <- data.frame(

n = factor(c("a) n=20", "b) n=400", "c) 20 * n=20\n(meta-analysis)"), ordered=TRUE),

point_estimate = c(ES1$d, ES2$d, meta$b),

ci.lower = c(ES1$l.d, ES2$l.d, meta$ci.lb),

ci.upper = c(ES1$u.d, ES2$u.d, meta$ci.ub)

)

ggplot(res, aes(x=n, y=point_estimate, ymin=ci.lower, ymax=ci.upper)) + geom_pointrange() + theme_bw() + xlab("") + ylab("Cohen's d") + geom_hline(yintercept=0.8, linetype="dotted", color="darkgreen")

To summarize, a single small-*n* study hardly teaches something about effect sizes – but many small-*n*‘s do. But meta-analyses are only possible, if the ES is reported.

“But just how big an

ndo we need to study effect size? I am about to show that the answer has four-digits.”

In Uri’s post (and the linked R code) the precision issue is approached from the power side – if you increase power, you also increase precision. But you can also directly compute the necessary sample size for a desired precision. This is called the AIPE-framework (“accuracy in parameter estimation”) made popular by Ken Kelley, Scott Maxwell, and Joseph Rausch (Kelley & Rausch, 2006; Kelley & Maxwell, 2003; Maxwell, Kelley, & Rausch, 2008). The necessary functions are implemented in the MBESS package for R. If you want a CI width of .10 around an expected ES of 0.5, you need 3170 participants:

The same point has been made from a Bayesian point of view in a blog post from John Kruschke: notice the sample size on the x-axis.

In our own analysis on how correlations evolve with increasing sample size (Schönbrodt & Perugini, 2013; see also blog post), we conclude that for typical effect sizes in psychology, you need 250 participants to get sufficiently accurate and stable estimates of the ES:

### How much precision is needed?

It’s certainly hard to give general guidelines how much precision is sensible, but here are our thoughts we based our stability analyses on. We used a CI-like “corridor of stability” (see Figure) with a half-width of w= .10, w=.15, and w=.20 (everything in the “correlation-metric”).

w = .20 was chosen for following reason: The average reported effect size in psychology is around *r* = .21 (Richard, Bond, & Stokes-Zoota, 2003). For this effect size, an accuracy of w = .20 would result in a CI that is “just significant” and does not include a reversal of the sign of the effect. Hence, with the typical effect sizes we are dealing with in psychology, a CI with a half-width > .20 would not make much sense.

w = .10 was chosen as it corresponds to a “small effect size” à la Cohen. This is arbitrary, of course, but at least some anchor. And w = .15 is just in between.

Using these numbers and an ES estimate of, say, *r* = .29, a just tolerable precision would be [.10; .46] (w = .20), a tolerable precision [.15; .42] (w = .15) and a moderate precision [.20; .38] (w = .10).

If we use this lower threshold of “just tolerable precision”, we would need in the two-sample group difference around 200-250 participants per group. While I am not sure whether we really need four-digit samples for typical scenarios, **I am sure that we need at least three-digit samples when we want to talk about “precision”.**

Regardless of the specific level of precision and method used, however, one thing is clear: **Accuracy does not come in cheaply**. We need much less participants for an hypothesis test (Is there a non-zero effect or not?) compared to an accurate estimate.

With increasing sample size, unfortunately you have diminishing returns on precision: As you can see in the dotted lines in Figure 2, the CI levels off, and you need disproportionally large sample sizes to squeeze out the last tiny percentages of a shrinking CI. If you follow Pareto’s principle, you should stop somewhen. Probably in scientific progress accuracy will be rather achieved in meta-analyzing several studies (which also gives you an estimate about the ES variability and possible moderators) than doing one mega-study.

**Hence: Always report your ES estimate, even in small- n studies.**

### References

Kelley, K., & Maxwell, S. E. (2003). Sample Size for Multiple Regression: Obtaining Regression Coefficients That Are Accurate, Not Simply Significant. *Psychological Methods, 8*, 305–321. doi:10.1037/1082-989X.8.3.305

Kelley, K., & Rausch, J. R. (2006). Sample size planning for the standardized mean difference: Accuracy in parameter estimation via narrow confidence intervals. *Psychological Methods, 11*, 363–385. doi:10.1037/1082-989X.11.4.363

Maxwell, S. E., Kelley, K., & Rausch, J. R. (2008). Sample Size Planning for Statistical Power and Accuracy in Parameter Estimation. *Annual Review of Psychology, 59(1)*, 537–563. doi:10.1146/annurev.psych.59.103006.093735

*Review of General Psychology, 7*, 331–363. doi:10.1037/1089-2680.7.4.331

van Assen, M. A. L. M., van Aert, R. C. M., Nuijten, M. B., & Wicherts, J. M. (2014). Why publishing everything is more effective than selective publishing of statistically significant results.* PLoS ONE, 9*, e84896. doi:10.1371/journal.pone.0084896

# Interactive exploration of a prior’s impact

The probably most frequent criticism of Bayesian statistics sounds something like “It’s all subjective – with the ‘right’ prior, you can get any result you want.”.

In order to approach this criticism it has been suggested to do a sensitivity analysis (or robustness analysis), that demonstrates how the choice of priors affects the conclusions drawn from the Bayesian analysis. Ideally, it can be shown that for virtually any reasonable prior the conclusions remain the same. In this case, the critique “it’s all in the prior” can be refuted on empirical grounds.

In their recent paper “The p < .05 rule and the hidden costs of the free lunch in inference” Jeff Rouder and colleagues argue that in the case of the default Bayes factor for *t* tests the choice of the H1 prior distribution does not make a strong difference (see Figure 6, right panel). They come to the conclusion that “Prior scale does matter, and may change the Bayes factor by a factor of 2 or so, but it does not change the order of magnitude.” (p. 24).

The default Bayes factor for *t* tests (Rouder, Speckman, Sun, Morey, Iverson, 2009) assumes that effect sizes (expressed as Cohen’s *d*) are distributed as a Cauchy distribution (this is the prior distribution for H1). The spread of the Cauchy distribution can be changed with the scale parameter *r*. Depending on the specific research area, one can use a wider (large *r*‘s, e.g. *r* =1.5) or a thinner (small r’s, e.g. r = 0.5) Cauchy distribution. This corresponds to the prior belief that typically larger or smaller effect sizes can be expected.

For the two-sample *t* test, the BayesFactor package for R suggest three defaults for the scale parameter:

- “medium” (r = sqrt(2)/2 = 0.71),
- “wide” (r = 1), and
- “ultra-wide” (r = sqrt(2) = 1.41).

Here’s a display for these distributions:

**For a given effect size: How does the choice of the prior distribution change the resulting Bayes factor?**

The following shiny app demonstrates how the choice of the prior influences the Bayes factor for a given effect size and sample size. Try moving the sliders! You can also provide arbitrary values for r (as comma-separated values; r must be > 0; reasonable ranges are between 0.2 and 2).

For a robustness analysis simply compare the lines at each vertical cut. An important line is the solid blue line at log(1), which indicates the same support for H1 and H0. All values above that line are in favor of the H1, all values below that line are in favor of H0.

As you will see, in most situations the Bayes factors for all *r*‘s are either above log(1), or below log(1). That means, regardless of the choice of the prior you will come to the same conclusion. There are very few cases where a data line for one *r* is below log(1) and the other is above log(1). In this case, different *r*‘s would come to different conclusions. But in these ambiguous situations the evidence for H1 or for H0 is always in the “anectodal” region, which is a very weak evidence. With the default r’s, the ratio of the resulting Bayes factors is indeed maximally “a factor of 2 or so”.

To summarize, within a reasonable range of prior distributions it is **not** possible that one prior generates strong evidence for H1, while some other prior generates strong evidence for H0. In that sense, the conclusions drawn from a default Bayes factor are robust to the choice of (reasonable) priors.

*References*

Rouder, J. N., Morey, R. D., Verhagen, J., Province, J. M., & Wagenmakers, E. J. (submitted). The p < .05 rule and the hidden costs of the free lunch in inference. Retrieved from http://pcl.missouri.edu/biblio/author/29

Rouder, J. N., Speckman, P. L., Sun, D., Morey, R. D., & Iverson, G. (2009). Bayesian t tests for accepting and rejecting the null hypothesis. *Psychonomic Bulletin & Review, 16*, 225–237.

### Related posts

# A short taxonomy of Bayes factors

I started to familiarize myself with Bayesian statistics. In this post I’ll show some insights I had about *Bayes factors* (BF).

## What are Bayes factors?

Bayes factors provide a numerical value that quantifies how well a hypothesis predicts the empirical data relative to a competing hypothesis. For example, if the BF is 4, this indicates: “This empirical data is 4 times more probable if H₁ were true than if H₀ were true.” . Hence, evidence points towards H₁. A BF of 1 means that data are equally likely to be occured under both hypotheses. In this case, it would be impossible to decide between both.

More formally, the BF can be written as:

where D is the data.

(for more formal introductions to BFs, see Wikipedia, Bayesian-Inference, or the classic paper by Kass and Raftery, 1995).

Hence, the BF is a ratio of probabilities, and is related to larger class of likelihood-ratio test.

Although many authors agree about the many theoretical advantages of BFs, until recently it was complicated and unclear how to compute a BF even for the simplest standard designs (Rouder, Morey, Speckman, & Province, 2012). Fortunately, over the last years *default Bayes factors* for several standard designs have been developed (Rouder et al., 2012; Rouder, Speckman, Sun, Morey, & Iverson, 2009; Morey & Rouder, 2011). For example, for a two-sample *t* test, a BF can be derived simply by plugging the *t* value and the sample sizes into a formula. The BF is easy to compute by the R package BayesFactor (Morey & Rouder, 2013), or by online calculators [1][2].

## Flavors of Bayes factors

When I started to familiarize myself with BFs, I was sometimes confused, as the same number seemed to mean different things in different publications. And indeed, **four types of Bayes factors** can be distinguished. “Under the hood”, all four types are identical, but you have to be aware which type has been employed in the specific case.

The first distinction is, whether the BF indicates “ over ” (=), or “ over ” (=). A of 2 means “Data is 2 times more likely to be occured under than under “, while the same situation would be a of 0.5 (i.e., the reciprocal value 1/2). Intuitively, I prefer larger values to be “better”, and as I usually would like to have evidence for instead of , I prefer the .

The second distinction is, whether one reports the raw BF, or the natural logarithm of the BF. The logarithm has the advantage that the scale above 1 (evidence for ) is identical to the scale below 1 (evidence for ). In the previous example, a of 2 is equivalent to a of 0.5. Taking the log of both values leads to = 0.69 and = -0.69: Same value, reversed sign. This makes the log(BF) ideal for visualization, as the scale is linear in both directions. Following graphic shows the relationship between raw/log BF:

As you can see in the Table of Figure 1, different authors use different flavors. Notably, the website calculator gives “raw-” BF, while the BayesFactor package gives “log+” BF. (That caused me some headache … To be clear: The help page of ?ttest.tstat clearly states that it computes the “log(e) Bayes factor (against the point null)”. Once you understand the system, everything falls into place; but it took me some time to figure out how to understand and convert the different metrics.)

Figure 2 shows conversion paths of the different BF flavors:

For example, if you enter t = 2.51, n = 100 into the website, you get a JZS Bayes Factor = 0.6140779. The same numbers in the BayesFactor package give a BF of 0.4876335:

As you can see: After applying the conversion, it is exactly the same.

Related posts: Exploring the robustness of Bayes Factors: A convenient plotting function

### References

Morey, R. D. & Rouder, J. N. (2011). Bayes factor approaches for testing interval null hypotheses. Psychological Methods, 16(4), 406–419. PMID: 21787084. doi:10.1037/a0024377

Morey, R. D. & Rouder, J. N. (2013). {BAYESFACTOR}: computation of bayes factors for common designs. R package version 0.9.4. Retrieved from http://CRAN.R- project.org/package=BayesFactor

Rouder, J. N., Morey, R. D., Speckman, P. L., & Province, J. M. (2012). Default bayes factors for ANOVA designs. Journal of Mathematical Psychology, 56(5), 356–374. doi:10.1016/j.jmp.2012.08.001

Rouder, J. N., Speckman, P. L., Sun, D., Morey, R. D., & Iverson, G. (2009). Bayesian t tests for accepting and rejecting the null hypothesis. Psychonomic Bulletin & Review, 16(2), 225–237.

# New robust statistical functions in WRS package – Guest post by Rand Wilcox

Today a new version (0.23.1) of the WRS package (Wilcox’ Robust Statistics) has been released. This package is the companion to his rather exhaustive book on robust statistics, “Introduction to Robust Estimation and Hypothesis Testing” (Amazon Link de/us).

For a fail-safe installation of the package, follow this instruction.

As a guest post, Rand Wilcox describes the new functions of the newest WRS version – have fun!

“Hi everyone,

As you probably know, when standard assumptions are violated, classic methods for comparing groups and studying associations can have very poor power and yield highly misleading results. The better known methods for dealing with these problem (transforming the data or testing assumptions) are ineffective compared to more modern methods. Simply removing outliers among the dependent variable and applying standard techniques to the remaining data is disastrous.

Methods I derive to deal with these problems can be applied with R functions stored in an R package (WRS) maintained by Felix Schönbrodt. Felix asked me to briefly describe my recent efforts for a newsletter he posts. In case this might help some of you, a brief description of my recently developed methods and corresponding R functions are provided below. (The papers I cite illustrate that they can make a substantial difference compared to extant techniques.)

### Comparing groups:

Sometimes it can be important and more informative to compare the tails (upper and lower quantiles) of two groups rather than a measure of location that is centrally located. Example: have been involved in a study aimed at determining whether intervention reduced depressive symptoms. But the typical individual was not very depressed prior to intervention and no difference is found using the more obvious techniques. Simply ignoring the less depressed individuals results in using the wrong standard error – a very serious problem. But comparing quantiles, it was found that the more depressed individuals benefitted the most from intervention.

The new method beats the shift function. See

Wilcox, R. R., Erceg-Hurn, D., Clark, F. & Carlson, M. (2013). Comparing two independent groups via the lower and upper quantiles. Journal of Statistical Computation and Simulation. DOI: 10.1080/00949655.2012.754026

Use the R function `qcomhd`

.

For **dependent groups** must use another method. There are, in fact, two distinct ways of viewing the problem. See

Wilcox, R. R. & Erceg-Hurn, D. (2012). Comparing two dependent groups via quantiles. Journal of Applied Statistics, 39, 2655–2664.

Use the R function `Dqcomhd`

.

When comparing two groups based on a Likert scale, use the function `disc2com`

.

It performs a global test of P(X=x)=P(Y=x) for all x using a generalization of the Storer–Kim method for comparing binomials.

`binband`

: a multiple comparison method for the individual cell probabilities.

### Regression:

`tshdreg`

: This is a modification of the Theil–Sen estimator. When there are tied values among the dependent variable, this modification might result in substantially higher power. A paper (Wilcox & Clark, in press) provides details. The function `tsreg`

now checks whether there are any tied values and prints a message suggesting that you might want to use `tshdreg`

instead.

`qhdsm`

: A quantile regression smoother. That is, plot the regression line when predicting some quantile without specifying a parametric form for the regression line. Multiple quantile regression lines can be plotted. The method can be more satisfactory than using the function `qsmcobs`

(a spline-type method), which often creates waves and curvature that give an incorrect sense of the association. Another advantage of `qhsdm`

is that it can be used with more than one predictor; `qsmcobs`

is limited to one predictor only. The strategy behind `qhdsm`

is to get an initial approximation of the regression line using a running interval smoother in conjunction with the Harrell–Davis quantile estimator and then smoothed again via LOESS.

It is surprising how often an association is found when dealing with the higher and lower quantiles of the dependent variable that are not detected by least squares and other robust estimators.

`qhdsm2g`

: Plots regression lines for two groups using the function `qhdsm`

.

`rplot`

has been updated: setting the argument `LP=TRUE`

gives a smoother regression line.

`rplotCI`

. Same as `rplot`

but includes lines indicating a confidence interval for the predicted Y values

`rplotpbCI`

. Same as `rplotCI`

, only use a bootstrap method to compute confidence intervals.

### ANCOVA or comparing regression lines associated with independent groups:

`ancJN`

: The function fits a robust regression line for each group and then determines whether the predicted Y values differ significantly at specified points. So it has connections to the classic Johnson-Neyman method. That is, the method provides an indication of where the regression lines cross. Both types of heteroscedasticity are allowed, which can result in improved power beyond the improved power stemming from a robust estimator. See

Wilcox, R. R. (2013). A heteroscedastic method for comparing regression lines at specified design points when using a robust regression estimator. Journal of Data Science, 11, 281–291

`anctspb`

: Like `ancJN`

but uses a percentile bootstrap method that might help when there are tied values among the dependent variable.

`ancGLOB`

. A robust global ANCOVA method. Like the function ancova, it provides a flexible way of dealing with curvature and heteroscedasticity is allowed. But this function can reject in situations where ancova does not reject. The function returns a p-value and the hypothesis of identical regression lines is rejected if the p-value is less than or equal to a critical p-value. In essence, it can beat reliance on improved versions of the Bonferroni method. (Details are in a paper submitted for publication.) It does not dominate my original ANCOVA method (applied with the R function `ancova`

) in terms of power, but have encountered situations where it makes a practical difference.

It determines a critical p-value via the R function `ancGLOB_pv`

.

In essence, simulations are used. By default, the number of replications is `iter=500`

. But suggest using `iter=2000`

or larger. Execution time can be reduced substantially with `cpp=TRUE`

, which calls a C++ version of the function written by Xiao He. Here are the commands to install the C++ version:

For a global test that two parametric regression lines are identical, see

Wilcox, R. R. & Clark, F. (in press). Heteroscedastic global tests that the regression parameters for two or more independent groups are identical. Communications in Statistics– Simulation and Computation.

`ancGpar`

performs the robust method. The paper includes a different method when using least squares regression. It is based in part on the HC4 estimator, which deals with heteroscedasticity. But if there are outliers among the dependent variable, you are much better off using a robust estimator.

### ANCOVA or comparing regression lines associated with dependent groups:

`Dancova`

: ANCOVA for two dependent groups that provides a flexible way of dealing with curvature. Both types of heteroscedasticity are allowed. Roughly, approximate the regression lines with a running interval smoother and at specified design points compare the regression lines. This is an extension of the R function `ancova`

to dependent groups. The function can do an analysis on either the marginal measures of location or a measure of location based on the difference scores. When using a robust estimator, the choice between these two approaches can be important. Defaults to using a trimmed mean.

`Dancovamp`

: Like `Dancova`

only designed to handle multiple covariates.

`Danctspb`

: Compare regression lines of two dependent groups using a robust regression estimator. The default is to use Theil–Sen, but any estimator can be used via the argument regfun. So in contrast to `Dancova`

, a parametric form for the regression line is made. As usual, can eliminate outliers among the independent variable by setting the argument `xout=TRUE`

. When a parametric regression line provides a more accurate fit, can have more power compared to using a smoother. But when there is curvature that is not modeled well with a parametric fit, the reverse can happen.

Note: a version of `ancGLOB`

for dependent groups is being studied.

### Coefficient alpha

`Rcoefalpha`

: computes a robust analog of coefficient alpha. Developed this method some years ago but just got around to writing an R function. See

Wilcox, R. R. (1992). Robust generalizations of classical test reliability and Cronbach’s alpha. British Journal of Mathematical and Statistical Psychology, 45, 239–254.

*R. R. Wilcox*”

Have fun exploring these new methods!