Richard Kunert

Discovering a glaring error in a research paper – a personal account

New York Magazine has published a great article about how grad student Steven Ludeke tried to correct mistakes in the research of Pete Hatemi and Brad Verhulst. Overall, Ludeke summarises his experience as ‘not recommendable’. Back in my undergraduate years I spotted an error in an article by David DeMatteo and did little to correct it. Why?

Christian Bale playing a non-incarcerated American Psycho.

David DeMatteo, assistant professor in Psychology at Drexel University, investigates psychopathy. In 2010, I was a lowly undergraduate student and noticed a glaring mistake in one of his top ten publications which has now been cited 50 times according to Google Scholar.

The error

The study investigated the characteristics of psychopaths who live among us, the non-incarcerated population. How do these psychopaths manage to avoid prison? DeMatteo et al. (2006) measured their psychopathy in terms of personality features and in terms of overt behaviours. ‘Participants exhibited the core personality features of psychopathy (Factor 1) to a greater extent than the core behavioral features of psychopathy (Factor 2). This finding may be helpful in explaining why many of the study participants, despite having elevated levels of psychopathic characteristics, have had no prior involvement with the criminal justice system.’ (p. 142)

The glaring mistake in this publication is that Factor 2 scores at 7.1 (the behavioural features of psychopathy) are actually higher than the Factor 1 scores at 5.2 (the personality features of psychopathy). The numbers tell the exactly opposite story to the words.

DeMatteo_mistake.jpg

The error in short. The numbers obviously do not match up with the statement.

The numbers are given twice in the paper making a typo unlikely (p. 138 and p. 139). Adjusting the scores for the maxima of the scales that they are from (factor 1 x/x_max = 0.325 < factor 2 x/x_max=0.394) or the sample maximum (factor 1 x/x_max_obtained = 0.433 < factor 2 x/x_max_obtained = 0.44375) makes no difference. No outlier rejection is mentioned in the paper.

In sum, it appears as if DeMatteo and his co-authors interpret their numbers in a way which makes intuitive sense but which is in direct contradiction to their own data. When researchers disagree with their own data, we have a real problem.

The reaction

1) Self doubt. I consulted with my professor (the late Paddy O’Donnel) who confirmed the glaring mistake.

2) Contact the author. I contacted DeMatteo in 2010 but his e-mail response was evasive and did nothing to resolve the issue. I have contacted him again, inviting him to react to this post.

3) Check others’ reactions. I found three publications which cited DeMatteo et al.’s article (Rucevic, 2010; Gao & Raine, 2010; Ullrich et al., 2008) and simply ignored the contradictory numbers. They went with the story that community dwelling psychopaths show psychopathic personalities more than psychopathic behaviours, even though the data in the article favours the exactly opposite conclusion.

4) Realising my predicament. At this point I realised my options. Either I pursued this full force while finishing a degree and, afterwards, moving on to my Master’s in a different country. Or I let it go. I had a suspicion which Ludeke’s story in New York Magazine confirmed: in these situations one has much to lose and little to gain. Pursuing a mistake in the research literature is ‘clearly a bad choice’ according to Ludeke.

The current situation

And now this blog post detailing my experience. Why? Well, on the one hand, I have very little to lose from a disagreement with DeMatteo as I certainly don’t want a career in law psychology research and perhaps not even in research in general. The balance went from ‘little to gain, much to lose’ to ‘little to gain, little to lose’. On the other hand, following my recent blog posts and article (Kunert, 2016) about the replication crisis in Psychology, I have come to the conclusion that science cynicism is not the way forward. So, I finally went fully transparent.

I am not particularly happy with how I handled this whole affair. I have zero documentation of my contact with DeMatteo. So, expect his word to stand against mine soon. I also feel I should have taken a risk earlier in exposing this. But then, I used to be passionate about science and wanted a career in it. I didn’t want to make enemies before I had even started my Master’s degree.

In short, only once I stopped caring about my career in science did I find the space to care about science itself.

— — —

DeMatteo, D., Heilbrun, K., & Marczyk, G. (2006). An empirical investigation of psychopathy in a noninstitutionalized and noncriminal sample Behavioral Sciences & the Law, 24 (2), 133-146 DOI: 10.1002/bsl.667

Gao, Y., & Raine, A. (2010). Successful and unsuccessful psychopaths: A neurobiological model Behavioral Sciences & the Law DOI: 10.1002/bsl.924

Kunert, R. (2016). Internal conceptual replications do not increase independent replication success Psychonomic Bulletin & Review DOI: 10.3758/s13423-016-1030-9

Rucević S (2010). Psychopathic personality traits and delinquent and risky sexual behaviors in Croatian sample of non-referred boys and girls. Law and human behavior, 34 (5), 379-91 PMID: 19728057

Ullrich, S., Farrington, D., & Coid, J. (2008). Psychopathic personality traits and life-success Personality and Individual Differences, 44 (5), 1162-1171 DOI: 10.1016/j.paid.2007.11.008

— — —

Update 16/11/2016: corrected numerical typo in sentence beginning ‘Adjusting the scores for the maxima…’ pointed out to me by Tom Foulsham via twitter (@TomFoulsh).

How to excel at academic conferences in 5 steps

Academic conferences have been the biggest joy of my PhD and so I want to share with others how to excel at this academic tradition. 

1185006_10151842316587065_1748658640_n

The author (second from right, with can) at his first music cognition conference (SMPC 2013 in Toronto) which – despite appearances – he attended by himself.

1) Socialising

A conference is not all about getting to know facts. It’s all about getting to know people. Go to a conference where you feel you can approach people. Attend every single preparatory excursion/workshop/symposium, every social event, every networking lunch. Sit at a table where you know no-one at all. Talk to the person next to you in every queue. At first, you will have only tiny chats. Later, these first contacts can develop over lunch. Still later you publish a paper together (Kunert & Slevc, 2015). The peer-review process might make you think that academics are awful know-it-alls. At a conference you will discover that they are actually interesting, intelligent and sociable people. Meet them!

2) Honesty

The conference bar is a mythical place where researchers talk about their actual findings, their actual doubts, their actual thoughts. If you want to get rid of the nagging feeling that you are an academic failure, talk to researchers at a conference. You will see that the published literature is a very polished version of what is really going on in research groups. It will help you put your own findings into perspective.

3) Openness

You can get even more out of a conference if you let go of your fear of being scooped and answer other people’s honesty with being open about what you do. I personally felt somewhat isolated with my research project at my institute. Conferences were more or less the only place to meet people with shared academic interests. Being open there didn’t just improve the bond with other academics, it led to concrete improvements of my research (Kunert et al., 2016).

4) Tourism

Get out of the conference hotel and explore the city. More often than not conferences are held in suspiciously nice places. Come a few days early, get rid of your jet-lag while exploring the local sights. Stay a few days longer and gather your thoughts before heading back to normal life. You might never again have an excuse to go to so many nice places so easily.

5) Spontaneity

The most important answer is yes. You might get asked for all sorts of things to do during the conference. Just say yes. I attended the Gran’ Ol Opry in Nashville. I found myself in a jacuzzi in Redwood, CA. I attended a transvestite bar in Toronto. All with people I barely knew. All with little to no information on what the invitation entailed. Just say yes and see what happens.

It might sound terribly intimidating to go to an academic conference if you just started your PhD. In this case a national or student only conference might be a good first step into the academic conference tradition.

Conferences are the absolute highlight of academia. Don’t miss out on them.

— — —

Kunert R, & Slevc LR (2015). A Commentary on: “Neural overlap in processing music and speech”. Frontiers in human neuroscience, 9 PMID: 26089792

Kunert R, Willems RM, & Hagoort P (2016). Language influences music harmony perception: effects of shared syntactic integration resources beyond attention. Royal Society open science, 3 (2) PMID: 26998339

How to test for music skills

In a new article I evaluate a recently developed test for music listening skills. To my great surprise the test behaves very well. This could open the path to better understand the psychology underlying music listening. Why am I surprised?

I got my first taste of how difficult it is to replicate published scientific results during my very first empirical study as an undergraduate (eventually published as Kunert & Scheepers, 2014). Back then, I used a 25 minute long dyslexia screening test to distinguish dyslexic participants from non-dyslexic participants (the Lucid Adult Dyslexia Screener). Even though previous studies had suggested an excellent sensitivity (identifying actually dyslexic readers as dyslexic) of 90% and a moderate to excellent specificity (identifying actually non-dylexic readers as non-dyslexic) of 66% – 91% (Singleton et al., 2009; Nichols et al., 2009), my own values were worse at 61% sensitivity and 65% specificity. In other words, the dyslexia test only flagged someone with an official dyslexia diagnosis in 11/18 cases and only categorised someone without known reading problems as non-dyslexic in 13/20 cases. The dyslexia screener didn’t perform exactly as suggested by the published literature and I have been suspicious of ability tests every since.

Five years later I acquired data to look at how music can influence language processing (Kunert et al., 2016) and added a newly proposed music abilitily measure called PROMS (Law & Zentner, 2012) to the experimental sessions to see how bad it is. I really thought I would see the music listening ability scores derived from the PROMS to be conflated with things which on the face of it have little to do with music (digit span, i.e. the ability to repeat increasingly longer digit sequences), because previous music ability tests had that problem. Similarly, I expected people with better music training to not have that much better PROMS scores. In other words, I expected the PROMS to perform worse than suggested by the people who developed the test, in line with my negative experience with the dylexia screener.

It then came as a surprise to see that PROMS scores were hardly associated with the ability to repeat increasingly longer digit sequences (either in the same order, i.e. forward digit span, or in reverse order, i.e. backward digit span), see Figure 1A and 1B. This makes the PROMS scores surprisingly robust against variation in working memory, as you would expect from a good music ability test.

journal.pone.0159103.g002

Figure 1. How the brief PROMS (vertical axis) correlates with various validity measures (horizontal axis). Each dot is one participant. Lines are best fit lines with equal weights for each participant (dark) or downweighting unusual participants (light). Inserted correlation values reflect dark line (Pearson r) or a rank-order equivalent of it which is robust to outliers (Spearman rho). Correlation values range from -1 to +1.

The second surprise came when musical training was actually associated with better music skill scores, as one would expect for a good test of music skills, see Figures 1C, 1D, 1E, and 1H. To top it of, the PROMS score was also correlated with the music task performance in the experiment looking at how language influences music processing. This association between the PROMS and musical task accuracy was visible in two independent samples, see Figures 1F and 1G, which is truly surprising because the music task targets harmonic music perception which is not directly tested by the PROMS.

To conclude, I can honestly recommend the PROMS to music researchers. To my surprise it is a good test which could truly tell us something about where music skills actually come from. I’m glad that this time I have been proven wrong regarding my suspicions about ability tests.

— — —

Kunert R, & Scheepers C (2014). Speed and accuracy of dyslexic versus typical word recognition: an eye-movement investigation. Frontiers in psychology, 5 PMID: 25346708

Kunert R, Willems RM, & Hagoort P (2016). Language influences music harmony perception: effects of shared syntactic integration resources beyond attention. Royal Society open science, 3 (2) PMID: 26998339

Kunert R, Willems RM, & Hagoort P (2016). An Independent Psychometric Evaluation of the PROMS Measure of Music Perception Skills. PloS one, 11 (7) PMID: 27398805

Law LN, & Zentner M (2012). Assessing musical abilities objectively: construction and validation of the profile of music perception skills. PloS one, 7 (12) PMID: 23285071

Nichols SA, McLeod JS, Holder RL, & McLeod HS (2009). Screening for dyslexia, dyspraxia and Meares-Irlen syndrome in higher education. Dyslexia, 15 (1), 42-60 PMID: 19089876

Singleton, C., Horne, J., & Simmons, F. (2009). Computerised screening for dyslexia in adults Journal of Research in Reading, 32 (1), 137-152 DOI: 10.1111/j.1467-9817.2008.01386.x
— — —

A critical comment on “Contextual sensitivity in scientific reproducibility”

Psychological science is surprisingly difficult to replicate (Open Science Collaboration, 2015). Researchers are desperate to find out why. A new study in the prestigious journal PNAS (Van Bavel et al., 2016) claims that unknown contextual factors of psychological phenomena (“hidden moderators”) are to blame. The more an effect is sensitive to unknown contextual factors, the less likely a successful replication is. In this blog post I will lay out why I am not convinced by this argument.

Before I start I should say that I really appreciate that the authors of this paper make their point with reference to data and analyses thereof. I believe that this is a big improvement on the state of the replicability debate of a few years back when it was dominated by less substantiated opinions. Moreover, they share their key data and some analysis code, following good scientific practice. Still, I am not convinced by their argument. Here’s why:

1) No full engagement with the opposite side of the argument

Van Bavel et al.’s (2016) suggested influence of replication contexts on replication success cannot explain the following patterns in the data set they used (Open Science Collaboration, 2015):

a) replication effect sizes are mostly lower than original effect sizes. Effects might well “vary by [replication] context” (p. 2) but why the consistent reduction in effect size when replicating an effect?

b) internal conceptual replications are not related to independent replication success (Kunert, 2016). This goes directly against Van Bavel et al.’s (2016) suggestion that “conceptual replications can even improve the probability of successful replications” (p. 5).

c) why are most original effects just barely statistically significant (see previous blog post)?

I believe that all three patterns point to some combination of questionable research practices affecting the original studies. Nothing in Van Bavel et al.’s (2016) article manages to convince me otherwise.

2) The central result completely depends on how you define ‘replication success’

The central claim of the article is based on the correlation between one measure of replication success (subjective judgment by replication team of whether replication was successful) and one measure of the contextual sensitivity of a replicated effect. While the strength of the association (r = -.23) is statistically significant (p = .024), it doesn’t actually provide convincing evidence for either the null or the alternative hypothesis according to a standard Bayesian JZS correlation test (BF01 = 1). [For all analyses: R-code below.]

Moreover, another measure of replication success (reduction of effect size between original and replication study) is so weakly correlated with the contextual sensitivity variable (r = -.01) as to provide strong evidence for a lack of association between contextual sensitivity and replication success (BF01 = 12, notice that even the direction of the correlation is in the wrong direction according to Van Bavel et al.’s (2016) account).

Bevel_figure

[Update: The corresponding values for the other measures of replication success are: replication p < .05 (r = -0.18; p = .0721; BF01 = 2.5), original effect size in 95%CI of replication effect size (r = -.3, p = .0032, BF10 = 6). I could not locate the data column for whether the meta-analytic effect size is different from zero.]

3) The contextual sensitivity variable could be confounded

How do we know which original effects were plagued by hidden moderators (i.e. by unknown context sensitivity) if, well, these moderators are hidden? Three of the authors of the article simply rated all replicated studies for contextual sensitivity without knowing each study’s replication status (but after the replication success of each study was known in general). The authors provide evidence for the ratings to be reliable but no one knows whether they are valid.

For example, the raters tried not to be influenced by ‘whether the specific replication attempt in question would succeed’ (p. 2). Still, all raters knew they would benefit (in the form of a prestigious publication) from a significant association between their ratings and replication success. How do we know that the ratings do not simply reflect some sort of implicit replicability doubt? From another PNAS study (Dreber et al., 2015) we know that scientists can predict replication success before a replication study is run.

Revealing hidden moderators

My problem with the contextual sensitivity account claiming that unknown moderators are to blame for replication failures is not so much that it is an unlikely explanation. I agree with Van Bavel et al. (2016) that some psychological phenomena are more sensitive to replication contexts than others. I would equally welcome it if scientific authors were more cautious in generalising their results.

My problem is that this account is so general as to be nearly unfalsifiable, and an unfalsifiable account is scientifically useless. Somehow unknown moderators always get invoked once a replication attempt has failed. All sorts of wild claims could be retrospectively claimed to be true within the context of the original finding.

In short: a convincing claim that contextual factors are to blame for replication failures needs to reveal the crucial replication contexts and then show that they indeed influence replication success. The proof of the unknown pudding is in the eating.

— — —
Dreber, A., Pfeiffer, T., Almenberg, J., Isaksson, S., Wilson, B., Chen, Y., Nosek, B., & Johannesson, M. (2015). Using prediction markets to estimate the reproducibility of scientific research Proceedings of the National Academy of Sciences, 112 (50), 15343-15347 DOI: 10.1073/pnas.1516179112

Kunert, R. (2016). Internal conceptual replications do not increase independent replication success Psychonomic Bulletin & Review DOI: 10.3758/s13423-016-1030-9

Open Science Collaboration (2015). Estimating the reproducibility of psychological science Science, 349 (6251) DOI: 10.1126/science.aac4716

Van Bavel, J.J., Mende-Siedlecki, P., Brady, W.J., & Reinero, D.A. (2016). Contextual sensitivity in scientific reproducibility PNAS
— — —

########################################################################################################
# Script for article "A critical comment on "Contextual sensitivity in scientific reproducibility""    #
# Submitted to Brain's Idea                                                                            #
# Responsible for this file: R. Kunert (rikunert@gmail.com)                                            # 
########################################################################################################   
 
# source functions
if(!require(devtools)){install.packages('devtools')} #RPP functions
library(devtools)
source_url('https://raw.githubusercontent.com/FredHasselman/toolboxR/master/C-3PR.R')
in.IT(c('ggplot2','RColorBrewer','lattice','gridExtra','plyr','dplyr','httr','extrafont'))
 
if(!require(BayesMed)){install.packages('BayesMed')} #Bayesian analysis of correlation
library(BayesMed)
 
if(!require(Hmisc)){install.packages('Hmisc')} #correlations
library(Hmisc)
 
if(!require(reshape2)){install.packages('reshape2')}#melt function
library(reshape2)
 
if(!require(grid)){install.packages('grid')} #arranging figures
library(grid)
 
#get raw data from OSF website
info <- GET('https://osf.io/pra2u/?action=download', write_disk('rpp_Bevel_data.csv', overwrite = TRUE)) #downloads data file from the OSF
RPPdata <- read.csv("rpp_Bevel_data.csv")[1:100, ]
colnames(RPPdata)[1] <- "ID" # Change first column name
 
#------------------------------------------------------------------------------------------------------------
#2) The central result completely depends on how you define 'replication success'----------------------------
 
#replication with subjective judgment of whether it replicated
rcorr(RPPdata$ContextVariable_C, RPPdata$Replicate_Binary, type = 'spearman')
#As far as I know there is currently no Bayesian Spearman rank correlation analysis. Therefore, use standard correlation analysis with raw and ranked data and hope that the result is similar.
#parametric Bayes factor test
bf = jzs_cor(RPPdata$ContextVariable_C, RPPdata$Replicate_Binary)#parametric Bayes factor test
plot(bf$alpha_samples)
1/bf$BayesFactor#BF01 provides support for null hypothesis over alternative
#parametric Bayes factor test with ranked data
bf = jzs_cor(rank(RPPdata$ContextVariable_C), rank(RPPdata$Replicate_Binary))#parametric Bayes factor test
plot(bf$alpha_samples)
1/bf$BayesFactor#BF01 provides support for null hypothesis over alternative
 
#replication with effect size reduction
rcorr(RPPdata$ContextVariable_C[!is.na(RPPdata$FXSize_Diff)], RPPdata$FXSize_Diff[!is.na(RPPdata$FXSize_Diff)], type = 'spearman')
#parametric Bayes factor test
bf = jzs_cor(RPPdata$ContextVariable_C[!is.na(RPPdata$FXSize_Diff)], RPPdata$FXSize_Diff[!is.na(RPPdata$FXSize_Diff)])
plot(bf$alpha_samples)
1/bf$BayesFactor#BF01 provides support for null hypothesis over alternative
#parametric Bayes factor test with ranked data
bf = jzs_cor(rank(RPPdata$ContextVariable_C[!is.na(RPPdata$FXSize_Diff)]), rank(RPPdata$FXSize_Diff[!is.na(RPPdata$FXSize_Diff)]))
plot(bf$alpha_samples)
1/bf$BayesFactor#BF01 provides support for null hypothesis over alternative
 
#------------------------------------------------------------------------------------------------------------
#Figure 1----------------------------------------------------------------------------------------------------
 
#general look
theme_set(theme_bw(12)+#remove gray background, set font-size
            theme(axis.line = element_line(colour = "black"),
                  panel.grid.major = element_blank(),
                  panel.grid.minor = element_blank(),
                  panel.background = element_blank(),
                  panel.border = element_blank(),
                  legend.title = element_blank(),
                  legend.key = element_blank(),
                  legend.position = "top",
                  legend.direction = 'vertical'))
 
#Panel A: replication success measure = binary replication team judgment
dat_box = melt(data.frame(dat = c(RPPdata$ContextVariable_C[RPPdata$Replicate_Binary == 1],
                                  RPPdata$ContextVariable_C[RPPdata$Replicate_Binary == 0]),
                          replication_status = c(rep('replicated', sum(RPPdata$Replicate_Binary == 1)),
                                                 rep('not replicated', sum(RPPdata$Replicate_Binary == 0)))),
               id = c('replication_status'))
 
#draw basic box plot
plot_box = ggplot(dat_box, aes(x=replication_status, y=value)) +
  geom_boxplot(size = 1.2,#line size
               alpha = 0.3,#transparency of fill colour
               width = 0.8,#box width
               notch = T, notchwidth = 0.8,#notch setting               
               show_guide = F,#do not show legend
               fill='black', color='grey40') +  
  labs(x = "Replication status", y = "Context sensitivity score")#axis titles
 
#add mean values and rhythm effect lines to box plot
 
#prepare data frame
dat_sum = melt(data.frame(dat = c(mean(RPPdata$ContextVariable_C[RPPdata$Replicate_Binary == 1]),
                                  mean(RPPdata$ContextVariable_C[RPPdata$Replicate_Binary == 0])),
                          replication_status = c('replicated', 'not replicated')),
               id = 'replication_status')
 
#add mean values
plot_box = plot_box +
  geom_line(data = dat_sum, mapping = aes(y = value, group = 1),
            size= c(1.5), color = 'grey40')+
  geom_point(data = dat_sum, size=12, shape=20,#dot rim
             fill = 'grey40',
             color = 'grey40') +
  geom_point(data = dat_sum, size=6, shape=20,#dot fill
             fill = 'black',
             color = 'black')
plot_box
 
#Panel B: replication success measure = effect size reduction
dat_corr = data.frame("x" = RPPdata$FXSize_Diff[!is.na(RPPdata$FXSize_Diff)],
                      "y" = RPPdata$ContextVariable_C[!is.na(RPPdata$FXSize_Diff)])#plotted data
 
plot_corr = ggplot(dat_corr, aes(x = x, y = y))+
  geom_point(size = 2) +#add points
  stat_smooth(method = "lm", size = 1, se = FALSE,
              aes(colour = "least squares regression")) +
  stat_smooth(method = "rlm", size = 1, se = FALSE,
              aes(colour = "robust regression")) +
  labs(x = "Effect size reduction (original - replication)", y = "Contextual sensitivity score") +#axis labels
  scale_color_grey()+#colour scale for lines
  stat_smooth(method = "lm", size = 1, se = FALSE,
              aes(colour = "least squares regression"),
              lty = 2)
plot_corr
 
#arrange figure with both panels
multi.PLOT(plot_box + ggtitle("Replication success = replication team judgment"),
           plot_corr + ggtitle("Replication success = effect size stability"),
           cols=2)

Created by Pretty R at inside-R.org

Yet more evidence for questionable research practices in original studies of Reproducibility Project: Psychology

The replicability of psychological research is surprisingly low. Why? In this blog post I present new evidence showing that questionable research practices contributed to failures to replicate psychological effects.

Quick recap. A recent publication in Science claims that only around 40% of psychological findings are replicable, based on 100 replication attempts in the Reproducibility Project Psychology (Open Science Collaboration, 2015). A few months later, a critical commentary in the same journal made all sorts of claims, including that the surprisingly low 40% replication success rate is due to replications having been unfaithful to the original studies’ methods (Gilbert et al., 2016). A little while later, I published an article in Psychonomic Bulletin & Review re-analysing the data by the 100 replication teams (Kunert, 2016). I found evidence for questionable research practices being at the heart of failures to replicate, rather than the unfaithfulness of replications to original methods.

However, my previous re-analysis depended on replication teams having done good work. In this blog post I will show that even when just looking at the original studies in the Reproducibility Project: Psychology one cannot fail to notice that questionable research practices were employed by the original discoverers of the effects which often failed to replicate. The reanalysis I will present here is based on the caliper test introduced by Gerber and colleagues (Gerber & Malhotra, 2008; Gerber et al., 2010).

The idea of the caliper test is simple. The research community has decided that an entirely arbitrary threshold of p = 0.05 distinguishes between effects which might just be due to chance (p > 0.05) and effects which are more likely due to something other than chance (p < 0.05). If researchers want to game the system they slightly rig their methods and analyses to push their p-values just below the arbitrary border between ‘statistical fluke’ and ‘interesting effect’. Alternatively, they just don’t publish anything which came up p > 0.05. Such behaviour should lead to an unlikely amount of p-values just below 0.05 compared to just above 0.05.

The figure below shows the data of the Reproducibility Project: Psychology. On the horizontal axis I plot z-values which are related to p-values. The higher the z-value the lower the p-value. On the vertical axis I just show how many z-values I found in each range. The dashed vertical line is the arbitrary threshold between p < .05 (significant effects on the right) and p > .05 (non-significant effects on the left).

RPP_density_plot

The independent replications in blue show many z-values left of the dashed line, i.e. replication attempts which were unsuccessful. Otherwise the blue distribution is relatively smooth. There is certainly nothing fishy going on around the arbitrary p = 0.05 threshold. The blue curve looks very much like what I would expect psychological research to be if questionable research practices did not exist.

However, the story is completely different for the green distribution representing the original effects. Just right of the arbitrary p = 0.05 threshold there is a surprising clustering of z-values. It’s as if the human mind magically leads to effects which are just about significant rather than just about not significant. This bump immediately to the right of the dashed line is a clear sign that original authors used questionable research practices. This behaviour renders psychological research unreplicable.

For the expert reader, the formal analysis of the caliper test is shown in the table below using both a Bayesian analysis and a classical frequentist analysis. The conclusion is clear. There is no strong evidence for replication studies failing the caliper test, indicating that questionable research practices were probably not employed. The original studies do not pass the caliper test, indicating that questionable research practices were employed.

 

over caliper

(significant)

below caliper (non-sign.) Binomial test Bayesian proportion test posterior median

[95% Credible Interval]1

10 % caliper (1.76 < z < 1.96 versus 1.96 < z < 2.16)

Original 9 4 p = 0.267 BF10 = 1.09 0.53

[-0.36; 1.55]

Replication 3 2 p = 1 BF01 = 1.30 0.18

[-1.00; 1.45]

15 % caliper (1.67 < z < 1.96 versus 1.96 < z < 2.25)

Original 17 4 p = 0.007 BF10 = 12.9 1.07

[0.24; 2.08]

Replication 4 5 p = 1 BF01 = 1.54 -0.13

[-1.18; 0.87]

20 % caliper (1.76 < z < 1.57 versus 1.96 < z < 2.35)

Original 29 4 p < 0.001 BF10 = 2813 1.59

[0.79; 2.58]

Replication 5 5 p = 1 BF01 = 1.64 0.00

[-0.99; 0.98]

1Based on 100,000 draws from the posterior distribution of log odds.

 

As far as I know, this is the first analysis showing that data from the original studies of the Reproducibility Project: Psychology point to questionable research practices [I have since been made aware of others, see this comment below]. Instead of sloppy science on the part of independent replication teams, this analysis rather points to original investigators employing questionable research practices. This alone could explain the surprisingly low replication rates in psychology.

Psychology failing the caliper test is by no means a new insight. Huge text-mining analyses have shown that psychology as a whole tends to fail the caliper test (Kühberger et al., 2013, Head et al., 2015). The analysis I have presented here links this result to replicability. If a research field employs questionable research practices (as indicated by the caliper test) then it can no longer claim to deliver insights which stand the replication test (as indicated by the Reproducibility Project: Psychology).

It is time to get rid of questionable research practices. There are enough ideas for how to do so (e.g., Asendorpf et al., 2013; Ioannidis, Munafò, Fusar-Poli, Nosek, & Lakens, 2014). The Reproducibility Project: Psychology shows why there is no time to waste: it is currently very difficult to distinguish an interesting psychological effect from a statistical fluke. I doubt that this state of affairs is what psychological researchers get paid for.

PS: full R-code for recreating all analyses and figures is posted below. If you find mistakes please let me know.

PPS: I am indebted to Jelte Wicherts for pointing me to this analysis.

Update 25/4/2015:

I adjusted text to clarify that caliper test cannot distinguish between many different questionable research practices, following tweet by .

I toned down the language somewhat following tweet by .

I added reference to Uli Schimmack’s analysis by linking his comment.

— — —

Asendorpf, J., Conner, M., De Fruyt, F., De Houwer, J., Denissen, J., Fiedler, K., Fiedler, S., Funder, D., Kliegl, R., Nosek, B., Perugini, M., Roberts, B., Schmitt, M., van Aken, M., Weber, H., & Wicherts, J. (2013). Recommendations for Increasing Replicability in Psychology European Journal of Personality, 27 (2), 108-119 DOI: 10.1002/per.1919

Gerber, A., & Malhotra, N. (2008). Publication Bias in Empirical Sociological Research: Do Arbitrary Significance Levels Distort Published Results? Sociological Methods & Research, 37 (1), 3-30 DOI: 10.1177/0049124108318973

Gerber, A., Malhotra, N., Dowling, C., & Doherty, D. (2010). Publication Bias in Two Political Behavior Literatures American Politics Research, 38 (4), 591-613 DOI: 10.1177/1532673X09350979

Gilbert, D., King, G., Pettigrew, S., & Wilson, T. (2016). Comment on “Estimating the reproducibility of psychological science” Science, 351 (6277), 1037-1037 DOI: 10.1126/science.aad7243

Head ML, Holman L, Lanfear R, Kahn AT, & Jennions MD (2015). The extent and consequences of p-hacking in science. PLoS biology, 13 (3) PMID: 25768323

Ioannidis JP, Munafò MR, Fusar-Poli P, Nosek BA, & David SP (2014). Publication and other reporting biases in cognitive sciences: detection, prevalence, and prevention. Trends in cognitive sciences, 18 (5), 235-41 PMID: 24656991

Kühberger A, Fritz A, & Scherndl T (2014). Publication bias in psychology: a diagnosis based on the correlation between effect size and sample size. PloS one, 9 (9) PMID: 25192357

Kunert R (2016). Internal conceptual replications do not increase independent replication success. Psychonomic bulletin & review PMID: 27068542

Open Science Collaboration (2015). Estimating the reproducibility of psychological science Science, 349 (6251) DOI: 10.1126/science.aac4716

— — —

##################################################################################################################
# Script for article "Questionable research practices in original studies of Reproducibility Project: Psychology"#
# Submitted to Brain's Idea (status: published)                                                                                               #
# Responsible for this file: R. Kunert (rikunert@gmail.com)                                                      # 
##################################################################################################################    
 
##########################################################################################################################################################################################
#-----------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------
#Figure 1: p-value density
 
# source functions
if(!require(httr)){install.packages('httr')}
library(httr)
info <- GET('https://osf.io/b2vn7/?action=download', write_disk('functions.r', overwrite = TRUE)) #downloads data file from the OSF
source('functions.r')
 
if(!require(devtools)){install.packages('devtools')} #RPP functions
library(devtools)
source_url('https://raw.githubusercontent.com/FredHasselman/toolboxR/master/C-3PR.R')
in.IT(c('ggplot2','RColorBrewer','lattice','gridExtra','plyr','dplyr','httr','extrafont'))
 
if(!require(BayesFactor)){install.packages('BayesFactor')} #Bayesian analysis
library(BayesFactor)
 
if(!require(BEST)){install.packages('BEST')} #distribution overlap
library(BEST)#requires JAGS version 3
 
if(!require(RCurl)){install.packages('RCurl')} #
library(RCurl)#
 
#the following few lines are an excerpt of the Reproducibility Project: Psychology's 
# masterscript.R to be found here: https://osf.io/vdnrb/
 
# Read in Tilburg data
info <- GET('https://osf.io/fgjvw/?action=download', write_disk('rpp_data.csv', overwrite = TRUE)) #downloads data file from the OSF
MASTER <- read.csv("rpp_data.csv")[1:167, ]
colnames(MASTER)[1] <- "ID" # Change first column name to ID to be able to load .csv file
 
#for studies with exact p-values
id <- MASTER$ID[!is.na(MASTER$T_pval_USE..O.) & !is.na(MASTER$T_pval_USE..R.)]
 
#FYI: turn p-values into z-scores 
#z = qnorm(1 - (pval/2)) 
 
#prepare data point for plotting
dat_vis <- data.frame(p = c(MASTER$T_pval_USE..O.[id],
                            MASTER$T_pval_USE..R.[id], MASTER$T_pval_USE..R.[id]),
                      z = c(qnorm(1 - (MASTER$T_pval_USE..O.[id]/2)),
                            qnorm(1 - (MASTER$T_pval_USE..R.[id]/2)),
                            qnorm(1 - (MASTER$T_pval_USE..R.[id]/2))),
                      Study_set= c(rep("Original Publications", length(id)),
                                   rep("Independent Replications", length(id)),
                                   rep("zIndependent Replications2", length(id))))
 
#prepare plotting colours etc
cols_emp_in = c("#1E90FF","#088A08")#colour_definitions of area
cols_emp_out = c("#08088a","#0B610B")#colour_definitions of outline
legend_labels = list("Independent\nReplication", "Original\nStudy")
 
#execute actual plotting
density_plot = ggplot(dat_vis, aes(x=z, fill = Study_set, color = Study_set, linetype = Study_set))+
  geom_density(adjust =0.6, size = 1, alpha=1) +  #density plot call
  scale_linetype_manual(values = c(1,1,3)) +#outline line types
  scale_fill_manual(values = c(cols_emp_in,NA), labels = legend_labels)+#specify the to be used colours (outline)
  scale_color_manual(values = cols_emp_out[c(1,2,1)])+#specify the to be used colours (area)
  labs(x="z-value", y="Density")+ #add axis titles  
  ggtitle("Reproducibility Project: Psychology") +#add title
  geom_vline(xintercept = qnorm(1 - (0.05/2)), linetype = 2) +
  annotate("text", x = 2.92, y = -0.02, label = "p < .05", vjust = 1, hjust = 1)+
  annotate("text", x = 1.8, y = -0.02, label = "p > .05", vjust = 1, hjust = 1)+
  theme(legend.position="none",#remove legend
        panel.grid.major = element_blank(),
        panel.grid.minor = element_blank(),
        panel.border = element_blank(),
        axis.line  = element_line(colour = "black"),#clean look
        text = element_text(size=18),
        plot.title=element_text(size=30))
density_plot
 
#common legend
#draw a nonsense bar graph which will provide a legend
legend_labels = list("Independent\nReplication", "Original\nStudy")
dat_vis <- data.frame(ric = factor(legend_labels, levels=legend_labels), kun = c(1, 2))
dat_vis$ric = relevel(dat_vis$ric, "Original\nStudy")
nonsense_plot = ggplot(data=dat_vis, aes(x=ric, y=kun, fill=ric)) + 
  geom_bar(stat="identity")+
  scale_fill_manual(values=cols_emp_in[c(2,1)], name=" ") +
  theme(legend.text=element_text(size=18))
#extract legend
tmp <- ggplot_gtable(ggplot_build(nonsense_plot)) 
leg <- which(sapply(tmp$grobs, function(x) x$name) == "guide-box") 
leg_plot <- tmp$grobs[[leg]]
#combine plots
grid.arrange(grobs = list(density_plot,leg_plot), ncol = 2, widths = c(2,0.4))
 
#caliper test according to Gerber et al.
 
#turn p-values into z-values
z_o = qnorm(1 - (MASTER$T_pval_USE..O.[id]/2))
z_r = qnorm(1 - (MASTER$T_pval_USE..R.[id]/2))
 
#How many draws are to be taken from posterior distribution for BF and Credible Interval calculations? The more samples the more precise the estimate and the slower the calculation.
draws = 10000 * 10#BayesFactor package standard = 10000
 
#choose one of the calipers
#z_c = c(1.76, 2.16)#10% caliper
#z_c = c(1.67, 2.25)#15% caliper
#z_c = c(1.57, 2.35)#20% caliper
 
#calculate counts
print(sprintf('Originals: over caliper N = %d', sum(z_o <= z_c[2] & z_o >= 1.96)))
print(sprintf('Originals: under caliper N = %d', sum(z_o >= z_c[1] & z_o <= 1.96)))
print(sprintf('Replications: over caliper N = %d', sum(z_r <= z_c[2] & z_r >= 1.96)))
print(sprintf('Replications: under caliper N = %d', sum(z_r >= z_c[1] & z_r <= 1.96)))
 
#formal caliper test: originals
#Bayesian analysis
bf = proportionBF(sum(z_o <= z_c[2] & z_o >= 1.96), sum(z_o >= z_c[1] & z_o <= z_c[2]), p = 1/2)
sprintf('Bayesian test of single proportion: BF10 = %1.2f', exp(bf@bayesFactor$bf))#exponentiate BF10 because stored as natural log
#sample from posterior
samples_o = proportionBF(sum(z_o <= z_c[2] & z_o >= 1.96), sum(z_o >= z_c[1] & z_o <= z_c[2]), p = 1/2,
                       posterior = TRUE, iterations = draws)
plot(samples_o[,"logodds"])
sprintf('Posterior Median = %1.2f [%1.2f; %1.2f]',
        median(samples_o[,"logodds"]),#Median 
        quantile(samples_o[,"logodds"], 0.025),#Lower edge of 95% Credible Interval
        quantile(samples_o[,"logodds"], 0.975))#Higher edge of 95% Credible Interval
#classical frequentist test
bt = binom.test(sum(z_o <= z_c[2] & z_o >= 1.96), sum(z_o >= z_c[1] & z_o <= z_c[2]), p = 1/2)
sprintf('Binomial test: p = %1.3f', bt$p.value)#
 
#formal caliper test: replications
bf = proportionBF(sum(z_r <= z_c[2] & z_r >= 1.96), sum(z_r >= z_c[1] & z_r <= z_c[2]), p = 1/2)
sprintf('Bayesian test of single proportion: BF01 = %1.2f', 1/exp(bf@bayesFactor$bf))#exponentiate BF10 because stored as natural log, turn into BF01
#sample from posterior
samples_r = proportionBF(sum(z_r <= z_c[2] & z_r >= 1.96), sum(z_r >= z_c[1] & z_r <= z_c[2]), p = 1/2,
                       posterior = TRUE, iterations = draws)
plot(samples[,"logodds"])
sprintf('Posterior Median = %1.2f [%1.2f; %1.2f]',
        median(samples_r[,"logodds"]),#Median 
        quantile(samples_r[,"logodds"], 0.025),#Lower edge of 95% Credible Interval
        quantile(samples_r[,"logodds"], 0.975))#Higher edge of 95% Credible Interval
#classical frequentist test
bt = binom.test(sum(z_r <= z_c[2] & z_r >= 1.96), sum(z_r >= z_c[1] & z_r <= z_c[2]), p = 1/2)
sprintf('Binomial test: p = %1.3f', bt$p.value)#
 
#possibly of interest: overlap of posteriors
#postPriorOverlap(samples_o[,"logodds"], samples_r[,"logodds"])#overlap of distribitions

Created by Pretty R at inside-R.org

10 things I learned while working for the Dutch science funding council (NWO)

 

The way science is currently funded is very controversial. During the last 6 months I was on a break from my PhD and worked for the organisation funding science in the Netherlands (NWO). These are 10 insights I gained.

12472348_10153473241208193_331748265476589914_n

1) Belangenverstrengeling

This is the first word I learned when arriving in The Hague. There is an anal obsession with avoiding (any potential for) conflicts of interest (belangenverstrengeling in Dutch). It might not seem a big deal to you, but it is a big deal at NWO.

 

2) Work ethic

Work e-mails on Sunday evening? Check. Unhealthy deadline obsession? Check. Stories of burn-out diagnoses? Check. In short, I found no evidence for the mythical low work ethic of NWO. My colleagues seemed to be in a perfectly normal, modern, semi-stressful job.

 

3) Perks

While the career prospects at NWO are somewhat limited, there are some nice perks to working in The Hague including: an affordable, good cantine, free fruit all day, subsidised in-house gym, free massage (unsurprisingly, with a waiting list from hell), free health check … The work atmosphere is, perhaps as a result, quite pleasant.

 

4) Closed access

Incredible but true, NWO does not have access to the pay-walled research literature it funds. Among other things, I was tasked with checking that research funds were appropriately used. You can imagine that this is challenging if the end-product of science funding (scientific articles) is beyond reach. Given a Herculean push to make all Dutch scientific output open access, this problem will soon be a thing of the past.

 

5) Peer-review

NWO itself does not generally assess grant proposals in terms of content (except for very small grants). What it does is organise peer-review, very similar to the peer-review of journal articles. My impression is that the peer-review quality is similar if not better at NWO compared to the journals that I have published in. NWO has minimum standards for reviewers and tries to diversify the national/scientific/gender background of the reviewer group assigned to a given grant proposal. I very much doubt that this is the case for most scientific journals.

 

6) NWO peer-reviewed

NWO itself also applies for funding, usually to national political institutions, businesses, and the EU. Got your grant proposal rejected at NWO? Find comfort in the thought that NWO itself also gets rejected.

 

7) Funding decisions in the making

In many ways my fears for how it is decided who gets funding were confirmed. Unfortunately, I cannot share more information other than to say: science has a long way to go before focussing rewards on good scientists doing good research.

 

8) Not funding decisions

I worked on grants which were not tied to some societal challenge, political objective, or business need. The funds I helped distribute are meant to simply facilitate the best science, no matter what that science is (often blue sky research, Vernieuwingsimpuls for people in the know). Approximately 10% of grant proposals receive funding. In other words, bad apples do not get funding. Good apples also do not get funding. Very good apples equally get zero funding. Only outstanding/excellent/superman apples get funding. If you think you are good at what you do, do not apply for grant money through the Vernieuwingsimpuls. It’s a waste of time. If, on the other hand, you haven’t seen someone as excellent as you for a while, then you might stand a chance.

 

9) Crisis response

Readers of this blog will be well aware that the field of psychology is currently going through something of a revolution related to depressingly low replication rates of influential findings (Open Science Framework, 2015; Etz & Vandekerckhove, 2016; Kunert, 2016). To my surprise, NWO wants to play its part to overcome the replication crisis engulfing science. I arrived at a fortunate moment, presenting my ideas of the problem and potential solutions to NWO. I am glad NWO will set aside money just for replicating findings.

 

10) No civil servant life for me

Being a junior policy officer at NWO turned out to be more or less the job I thought it would be. It was monotonous, cognitively relaxing, and low on responsibilities. In other words, quite different to doing a PhD. Other PhD students standing at the precipice of a burn out might also want to consider this as an option to get some breathing space. For me, it was just that, but not more than that.

— — —

This blog post does not represent the views of my former or current employers. NWO did not endorse this blog post. As far as I know, NWO doesn’t even know that this blog post exists.

— — —

Etz, A., & Vandekerckhove, J. (2016). A Bayesian Perspective on the Reproducibility Project: Psychology PLOS ONE, 11 (2) DOI: 10.1371/journal.pone.0149794

Kunert R (2016). Internal conceptual replications do not increase independent replication success. Psychonomic bulletin & review PMID: 27068542

Open Science Collaboration (2015). Estimating the reproducibility of psychological science Science, 349 (6251) DOI: 10.1126/science.aac4716

Is Replicability in Economics better than in Psychology?

Colin Camerer and colleagues recently published a Science article on the replicability of behavioural economics. ‘It appears that there is some difference in replication success’ between psychology and economics, they write, given their reproducibility rate of 61% and psychology’s of 36%. I took a closer look at the data to find out whether there really are any substantial differences between fields.

Commenting on the replication success rates in psychology and economics, Colin Camerer is quoted as saying: “It is like a grade of B+ for psychology versus A– for economics.” Unsurprisingly, his team’s Science paper also includes speculation as to what contributes to economics’ “relatively good replication success”. However, such speculation is premature as it is not established whether economics actually displays better replicability than the only other research field which has tried to estimate its replicability (that would be psychology). Let’s check the numbers in Figure 1.

RPP_EERP_replicability

Figure 1. Replicability in economics and psychology. Panel A displays replication p-values of originally significant effects. Note that the bottom 25% quartile is at p = .001 and p = .0047 respectively and, thus, not visible here. Panel B displays the effect size reduction from original to replication study.Violin plots display density, i.e. thicker parts represent more data points.

Looking at the left panel of Figure 1, you will notice that the p-values of the replication studies in economics tend to be lower than in psychology, indicating that economics is more replicable. In order to formally test this, I define a replication success as p < .05 (the typical threshold for proclaiming that an effect was found) and count successes in both data sets. In economics, there are 11 successes and 7 failures. In psychology, there are 34 successes and 58 failures. When comparing these proportions formally with a Bayesian contingency table test, the resulting Bayes Factor of BF10 = 1.77 indicates that the replicability difference between economics and psychology is so small as to be worth no more than a bare mention. Otherwise said, the replicability projects in economics and psychology were too small to say that one field produces more replicable effects than the other.

However, a different measure of replicability which doesn’t depend on an arbitrary cut-off at p = .05 might give a clearer picture. Figure 1’s right panel displays the difference between the effect sizes reported in the original publications and those observed by the replication teams. You will notice that most effect size differences are negative, i.e. when replicating an experiment you will probably observe a (much) smaller effect compared to what you read in the original paper. For a junior researcher like me this is an endless source of self-doubt and frustration.

Are effect sizes more similar between original and replication studies in economics compared to psychology? Figure 1B doesn’t really suggest that there is a huge difference. The Bayes factor of a Bayesian t-test comparing the right and left distributions of Figure 1B supports this impression. The null hypothesis of no difference is favored BF01 = 3.82 times more than the alternative hypothesis of a difference (or BF01 = 3.22 if you are an expert and insist on using Cohen’s q). In Table 1, I give some more information for the expert reader.

The take-home message is that there is not enough information to claim that economics displays better replicability than psychology. Unfortunately, psychologists shouldn’t just adopt the speculative factors contributing to the replication success in economics. Instead, we should look elsewhere for inspiration: the simulations of different research practices showing time and again what leads to high replicability (big sample sizes, pre-registration, …) and what not (publication bias, questionable research practices…). For the moment, psychologists should not look towards economists to find role models of replicability.

Table 1. Comparison of Replicability in Economics and Psychology.
Economics Psychology Bayes Factora Posterior median [95% Credible Interval]1
Independent Replications p < .05 11 out of 18 34 out of 92 BF10 = 1.77

0.95

[-0.03; 1.99]

Effect size reduction (simple subtraction)

M = 0.20

(SD = 0.20)

M = 0.20

(SD = 0.21)

BF01 = 3.82

0.02

[-0.12; 0.15]

Effect size reduction (Cohen’s q) M = 0.27

(SD = 0.36)

M = 0.22

(SD = 0.26)

BF01 = 3.22

0.03

[-0.15; 0.17]

a Assumes normality. See for yourself whether you believe this assumption is met.

1 Log odds for proportions. Difference values for quantities.

— — —

Camerer, C., Dreber, A., Forsell, E., Ho, T., Huber, J., Johannesson, M., Kirchler, M., Almenberg, J., Altmejd, A., Chan, T., Heikensten, E., Holzmeister, F., Imai, T., Isaksson, S., Nave, G., Pfeiffer, T., Razen, M., & Wu, H. (2016). Evaluating replicability of laboratory experiments in economics Science DOI: 10.1126/science.aaf0918

Open Science Collaboration (2015). Estimating the reproducibility of psychological science Science, 349 (6251) DOI: 10.1126/science.aac4716
— — —

PS: I am indebted to Alex Etz and EJ Wagenmakers who presented a similar analysis of parts of the data on the OSF website: https://osf.io/p743r/

— — —

R code for reproducing Figure and Table (drop me a line if you find a mistake):

# source functions
if(!require(devtools)){install.packages('devtools')} #RPP functions
library(devtools)
source_url('https://raw.githubusercontent.com/FredHasselman/toolboxR/master/C-3PR.R')
in.IT(c('ggplot2','RColorBrewer','lattice','gridExtra','plyr','dplyr','httr','extrafont'))

if(!require(BayesFactor)){install.packages('BayesFactor')} #Bayesian analysis
library(BayesFactor)

if(!require(BEST)){install.packages('BEST')} #distribution overlap
library(BEST)#requires JAGS version 3

if(!require(xlsx)){install.packages('xlsx')} #for reading excel sheets
library(xlsx)

#How many draws are to be taken from posterior distribution for BF and Credible Interval calculations? The more samples the more precise the estimate and the slower the calculation.
draws = 10000 * 10#BayesFactor package standard = 10000

##########################################################################################################################################################################################
#-----------------------------------------------------------------------------------------------------------------------------------------------------------------------------------------
#Figures 1: p-values

#get RPP raw data from OSF website
RPPdata &amp;amp;lt;- get.OSFfile(code='https://osf.io/fgjvw/',dfCln=T)$df
# Select the completed replication studies
RPPdata &amp;amp;lt;- dplyr::filter(RPPdata, !is.na(T.pval.USE.O),!is.na(T.pval.USE.R))

#get EERP raw data from local xls file based on Table S1 of Camerer et al., 2016 (just write me an e-mail if you want it)
EERPdata = read.xlsx(&amp;amp;quot;EE_RP_data.xls&amp;amp;quot;, 1)

# Restructure the data to &amp;amp;quot;long&amp;amp;quot; format: Study type will be a factor
df1 &amp;amp;lt;- dplyr::select(RPPdata,starts_with(&amp;amp;quot;T.&amp;amp;quot;))
df &amp;amp;lt;- data.frame(p.value=as.numeric(c(as.character(EERPdata$p_rep),
df1$T.pval.USE.R[df1$T.pval.USE.O &amp;amp;lt; .05])),
grp=factor(c(rep(&amp;amp;quot;Economics&amp;amp;quot;,times=length(EERPdata$p_rep)),
rep(&amp;amp;quot;Psychology&amp;amp;quot;,times=sum(df1$T.pval.USE.O &amp;amp;lt; .05)))))

# Create some variables for plotting
df$grpN &amp;amp;lt;- as.numeric(df$grp)
probs &amp;amp;lt;- seq(0,1,.25)

# VQP PANEL A: p-value -------------------------------------------------

# Get p-value quantiles and frequencies from data
qtiles &amp;amp;lt;- ldply(unique(df$grpN),function(gr) quantile(round(df$p.value[df$grpN==gr],digits=4),probs,na.rm=T,type=3))
freqs &amp;amp;lt;- ldply(unique(df$grpN),function(gr) table(cut(df$p.value[df$grpN==gr],breaks=qtiles[gr,],na.rm=T,include.lowest=T,right=T)))
labels &amp;amp;lt;- sapply(unique(df$grpN),function(gr)levels(cut(round(df$p.value[df$grpN==gr],digits=4), breaks = qtiles[gr,],na.rm=T,include.lowest=T,right=T)))

# Check the Quantile bins!
Economics &amp;amp;lt;-cbind(freq=as.numeric(t(freqs[1,])))
rownames(Economics) &amp;amp;lt;- labels[,1]
Economics

Psychology &amp;amp;lt;-cbind(freq=as.numeric(t(freqs[2,])))
rownames(Psychology) &amp;amp;lt;- labels[,2]
Psychology

# Get regular violinplot using package ggplot2
g.pv &amp;amp;lt;- ggplot(df,aes(x=grp,y=p.value)) + geom_violin(aes(group=grp),scale=&amp;amp;quot;width&amp;amp;quot;,color=&amp;amp;quot;grey30&amp;amp;quot;,fill=&amp;amp;quot;grey30&amp;amp;quot;,trim=T,adjust=.7)
# Cut at quantiles using vioQtile() in C-3PR
g.pv0 &amp;amp;lt;- vioQtile(g.pv,qtiles,probs)
# Garnish
g.pv1 &amp;amp;lt;- g.pv0 + geom_hline(aes(yintercept=.05),linetype=2) +
ggtitle(&amp;amp;quot;A&amp;amp;quot;) + xlab(&amp;amp;quot;&amp;amp;quot;) + ylab(&amp;amp;quot;replication p-value&amp;amp;quot;) +
mytheme
# View
g.pv1

## Uncomment to save panel A as a seperate file
# ggsave(&amp;amp;quot;RPP_F1_VQPpv.eps&amp;amp;quot;,plot=g.pv1)

#calculate counts
sum(as.numeric(as.character(EERPdata$p_rep)) &amp;amp;lt;= .05)#How many economic effects 'worked' upon replication?
sum(as.numeric(as.character(EERPdata$p_rep)) &amp;amp;gt; .05)##How many economic effects 'did not work' upon replication?
sum(df1$T.pval.USE.R[df1$T.pval.USE.O &amp;amp;lt; .05] &amp;amp;lt;= .05)#How many psychological effects 'worked' upon replication?
sum(df1$T.pval.USE.R[df1$T.pval.USE.O &amp;amp;lt; .05] &amp;amp;gt; .05)#How many psychological effects 'did not work' upon replication?

#prepare BayesFactor analysis
data_contingency = matrix(c(sum(as.numeric(as.character(EERPdata$p_rep)) &amp;amp;lt;= .05),#row 1, col 1
sum(as.numeric(as.character(EERPdata$p_rep)) &amp;amp;gt; .05),#row 2, col 1
sum(df1$T.pval.USE.R[df1$T.pval.USE.O &amp;amp;lt; .05] &amp;amp;lt;= .05),#row 1, col 2
sum(df1$T.pval.USE.R[df1$T.pval.USE.O &amp;amp;lt; .05] &amp;amp;gt; .05)),#row 2, col 2
nrow = 2, ncol = 2, byrow = F)#prepare BayesFactor analysis
bf = contingencyTableBF(data_contingency, sampleType = &amp;amp;quot;indepMulti&amp;amp;quot;, fixedMargin = &amp;amp;quot;cols&amp;amp;quot;)#run BayesFactor comparison
sprintf('BF10 = %1.2f', exp(bf@bayesFactor$bf))#exponentiate BF10 because stored as natural log

#Parameter estimation
chains = posterior(bf, iterations = draws)#draw samples from the posterior
odds_ratio = (chains[,&amp;amp;quot;omega[1,1]&amp;amp;quot;] * chains[,&amp;amp;quot;omega[2,2]&amp;amp;quot;]) / (chains[,&amp;amp;quot;omega[2,1]&amp;amp;quot;] * chains[,&amp;amp;quot;omega[1,2]&amp;amp;quot;])
sprintf('Median = %1.2f [%1.2f; %1.2f]',
median(log(odds_ratio)),#Median for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)
quantile(log(odds_ratio), 0.025),#Lower edge of 95% Credible Interval for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)
quantile(log(odds_ratio), 0.975))#Higher edge of 95% Credible Interval for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)
#plot(mcmc(log(odds_ratio)), main = &amp;amp;quot;Log Odds Ratio&amp;amp;quot;)

# VQP PANEL B: reduction in effect size -------------------------------------------------

econ_r_diff = as.numeric(as.character(EERPdata$r_rep)) - as.numeric(as.character(EERPdata$r_orig))
psych_r_diff = as.numeric(df1$T.r.R) - as.numeric(df1$T.r.O)
df &amp;amp;lt;- data.frame(EffectSizeDifference= c(econ_r_diff, psych_r_diff[!is.na(psych_r_diff)]),
grp=factor(c(rep(&amp;amp;quot;Economics&amp;amp;quot;,times=length(econ_r_diff)),
rep(&amp;amp;quot;Psychology&amp;amp;quot;,times=length(psych_r_diff[!is.na(psych_r_diff)])))))

# Create some variables for plotting
df$grpN &amp;amp;lt;- as.numeric(df$grp)
probs &amp;amp;lt;- seq(0,1,.25)

# Get effect size quantiles and frequencies from data
qtiles &amp;amp;lt;- ldply(unique(df$grpN),function(gr) quantile(df$EffectSizeDifference[df$grpN==gr],probs,na.rm=T,type=3,include.lowest=T))
freqs &amp;amp;lt;- ldply(unique(df$grpN),function(gr) table(cut(df$EffectSizeDifference[df$grpN==gr],breaks=qtiles[gr,],na.rm=T,include.lowest=T)))
labels &amp;amp;lt;- sapply(unique(df$grpN),function(gr)levels(cut(round(df$EffectSizeDifference[df$grpN==gr],digits=4), breaks = qtiles[gr,],na.rm=T,include.lowest=T,right=T)))

# Check the Quantile bins!
Economics &amp;amp;lt;-cbind(freq=as.numeric(t(freqs[1,])))
rownames(Economics) &amp;amp;lt;- labels[,1]
Economics

Psychology &amp;amp;lt;-cbind(freq=as.numeric(t(freqs[2,])))
rownames(Psychology) &amp;amp;lt;- labels[,2]
Psychology

# Get regular violinplot using package ggplot2
g.es &amp;amp;lt;- ggplot(df,aes(x=grp,y=EffectSizeDifference)) +
geom_violin(aes(group=grpN),scale=&amp;amp;quot;width&amp;amp;quot;,fill=&amp;amp;quot;grey40&amp;amp;quot;,color=&amp;amp;quot;grey40&amp;amp;quot;,trim=T,adjust=1)
# Cut at quantiles using vioQtile() in C-3PR
g.es0 &amp;amp;lt;- vioQtile(g.es,qtiles=qtiles,probs=probs)
# Garnish
g.es1 &amp;amp;lt;- g.es0 +
ggtitle(&amp;amp;quot;B&amp;amp;quot;) + xlab(&amp;amp;quot;&amp;amp;quot;) + ylab(&amp;amp;quot;Replicated - Original Effect Size r&amp;amp;quot;) +
scale_y_continuous(breaks=c(-.25,-.5, -0.75, -1, 0,.25,.5,.75,1),limits=c(-1,0.5)) + mytheme
# View
g.es1

# # Uncomment to save panel B as a seperate file
# ggsave(&amp;amp;quot;RPP_F1_VQPes.eps&amp;amp;quot;,plot=g.es1)

# VIEW panels in one plot using the multi.PLOT() function from C-3PR
multi.PLOT(g.pv1,g.es1,cols=2)

# SAVE combined plots as PDF
pdf(&amp;amp;quot;RPP_Figure1_vioQtile.pdf&amp;amp;quot;,pagecentre=T, width=20,height=8 ,paper = &amp;amp;quot;special&amp;amp;quot;)
multi.PLOT(g.pv1,g.es1,cols=2)
dev.off()

#Effect Size Reduction (simple subtraction)-------------------------------------------------

#calculate means and standard deviations
mean(econ_r_diff)#mean ES reduction of economic effects
sd(econ_r_diff)#Standard Deviation ES reduction of economic effects
mean(psych_r_diff[!is.na(psych_r_diff)])#mean ES reduction of psychological effects
sd(psych_r_diff[!is.na(psych_r_diff)])#Standard Deviation ES reduction of psychological effects

#perform BayesFactor analysis
bf = ttestBF(formula = EffectSizeDifference ~ grp, data = df)#Bayesian t-test to test the difference/similarity between the previous two
sprintf('BF01 = %1.2f', 1/exp(bf@bayesFactor$bf[1]))#exponentiate BF10 because stored as natural log, turn into BF01

##Parameter estimation: use BEST package to estimate posterior median and 95% Credible Interval
BESTout = BESTmcmc(econ_r_diff,
psych_r_diff[!is.na(psych_r_diff)],
priors=NULL, parallel=FALSE)
#plotAll(BESTout)
sprintf('Median = %1.2f [%1.2f; %1.2f]',
median(BESTout$mu1 - BESTout$mu2),#Median for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)
quantile(BESTout$mu1 - BESTout$mu2, 0.025),#Lower edge of 95% Credible Interval for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)
quantile(BESTout$mu1 - BESTout$mu2, 0.975))#Higher edge of 95% Credible Interval for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)

#Effect Size Reduction (Cohen's q)-------------------------------------------------

#prepare function to calculate Cohen's q
Cohenq &amp;amp;lt;- function(r1, r2) {
fis_r1 = 0.5 * (log((1+r1)/(1-r1)))
fis_r2 = 0.5 * (log((1+r2)/(1-r2)))
fis_r1 - fis_r2
}

#calculate means and standard deviations
econ_Cohen_q = Cohenq(as.numeric(as.character(EERPdata$r_rep)), as.numeric(as.character(EERPdata$r_orig)))
psych_Cohen_q = Cohenq(as.numeric(df1$T.r.R), as.numeric(df1$T.r.O))
mean(econ_Cohen_q)#mean ES reduction of economic effects
sd(econ_Cohen_q)#Standard Deviation ES reduction of economic effects
mean(psych_Cohen_q[!is.na(psych_Cohen_q)])#mean ES reduction of psychological effects
sd(psych_Cohen_q[!is.na(psych_Cohen_q)])#Standard Deviation ES reduction of psychological effects

#perform BayesFactor analysis
dat_bf &amp;amp;lt;- data.frame(EffectSizeDifference = c(econ_Cohen_q,
psych_Cohen_q[!is.na(psych_Cohen_q)]),
grp=factor(c(rep(&amp;amp;quot;Economics&amp;amp;quot;,times=length(econ_Cohen_q)),
rep(&amp;amp;quot;Psychology&amp;amp;quot;,times=length(psych_Cohen_q[!is.na(psych_Cohen_q)])))))#prepare BayesFactor analysis
bf = ttestBF(formula = EffectSizeDifference ~ grp, data = dat_bf)#Bayesian t-test to test the difference/similarity between the previous two
#null Interval is positive because effect size reduction is expressed negatively, H1 predicts less reduction in case of internally replicated effects
sprintf('BF01 = %1.2f', 1/exp(bf@bayesFactor$bf[1]))#exponentiate BF10 because stored as natural log, turn into BF01

#Parameter estimation: use BEST package to estimate posterior median and 95% Credible Interval
BESTout = BESTmcmc(econ_Cohen_q,
psych_Cohen_q[!is.na(psych_Cohen_q)],
priors=NULL, parallel=FALSE)
#plotAll(BESTout)
sprintf('Median = %1.2f [%1.2f; %1.2f]',
median(BESTout$mu1 - BESTout$mu2),#Median for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)
quantile(BESTout$mu1 - BESTout$mu2, 0.025),#Lower edge of 95% Credible Interval for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)
quantile(BESTout$mu1 - BESTout$mu2, 0.975))#Higher edge of 95% Credible Interval for increase in independent replication success due to internal replication\n(internally replicated versus not internally replicated)

How language changes the way you hear music

In a new paper I, together with Roel Willems and Peter Hagoort, show that music and language are tightly coupled in the brain. Get the gist in a 180 second youtube clip and then try out what my participants did.

The task my participants had to do might sound very abstract to you, so let me make it concrete. Listen to these two music pieces and tell me which one sounds ‘finished’:

I bet you thought the second one ended a bit in an odd way. How do you know? You use your implicit knowledge of harmonic relations in Western music for such a ‘finished judgement’. All we did in the paper was to see whether an aspect of language grammar (syntax) can influence your ability to hear these harmonic relations, as revealed by ‘finished judgements’. The music pieces we used for this sounded very similar to what you just heard:

It turns out that reading syntactically difficult sentences while hearing the music reduced the feeling that music pieces like this did actually end well. This indicated that processing language syntax draws on brain resources which are also responsible for music harmony.

Difficult syntax: The surgeon consoled the man and the woman put her hand on his forehead.

Easy syntax: The surgeon consoled the man and the woman because the operation had not been successful.

Curiously, sentences with a difficult meaning had no influence on the ‘finished judgements’.

Difficult meaning: The programmer let his mouse run around on the table after he had fed it.

Easy meaning: The programmer let his field mouse run around on the table after he had fed it.

Because only language syntax influenced ‘finished judgements’, we believe that music and language share a common syntax processor of some kind. This conclusion is in line with a number of other studies which I blogged about before.

What this paper adds is that we rule out an attentional link between music and language as the source of the effect. In other words, difficult syntax doesn’t simply distract you and thereby disables your music hearing. Its influence is based on a common syntax processor instead.

In the end, I tested 278 participants across 3 pre-tests, 2 experiments, and 1 post-test. Judge for yourself whether it was worth it by reading the freely available paper here.

— — —

Kunert R, & Slevc LR (2015). A Commentary on: “Neural overlap in processing music and speech”. Frontiers in human neuroscience, 9 PMID: 26089792

Kunert, R., Willems, R., & Hagoort, P. (2016). Language influences music harmony perception: effects of shared syntactic integration resources beyond attention Royal Society Open Science, 3 (2) DOI: 10.1098/rsos.150685

Are pre-registrations the solution to the replication crisis in Psychology?

Most psychology findings are not replicable. What can be done? In his Psychological Science editorial, Stephen Lindsay advertises pre-registration as a solution, writing that “Personally, I aim never again to submit for publication a report of a study that was not preregistered”. I took a look at whether pre-registrations are effective and feasible [TL;DR: maybe and possibly].

[I updated the blog post using comments by Cortex editor Chris Chambers, see below for full comments. It turns out that many of my concerns have already been addressed. Updates in square brackets.]

A recent study published in Science found that the majority of Psychological research cannot be reproduced by independent replication teams (Open Science Collaboration, 2015). I believe that this is due to questionable research practices (LINK) and that internal replications are no solution to this problem (LINK). However, might pre-registrations be the solution? I don’t think so. The reason why I am pessimistic is three-fold.

What is a pre-registration? A pre-registered study submits its design and analysis before data is acquired. After data acquisition the pre-registered data analysis plan is executed and the results can confidently be labelled confirmatory (i.e. more believable). Analyses not specified before are labelled exploratory (i.e. less believable). Some journals offer peer-review of the pre-registration document. Once it has been approved, the chances of the journal accepting a manuscript based on the proposed design and analysis are supposedly very high. [Chris Chambers: “for more info on RRs see https://osf.io/8mpji/wiki/home/”%5D

 

1) Pre-registration does not remove all incentives to employ questionable research practices

Pre-registrations should enforce honesty about post hoc changes in the design/analysis. Ironically, the efficacy of pre-registrations is itself dependent on the honesty of researchers. The reason is simple: including the information that an experiment was pre-registered is optional. So, if the planned analysis is optimal, a researcher can boost its impact by revealing that the entire experiment was pre-registered. If not, s/he deletes the pre-registration document and proceeds as if it had never existed, a novel questionable research practice (anyone want to invent a name for it? Optional forgetting?).

Defenders of pre-registration could counter that peer-reviewed pre-registrations are different because there is no incentive to deviate from the planned design/analysis. Publication is guaranteed if the pre-registered study is executed as promised. However, two motives remove this publication advantage:

1a) the credibility boost of presenting a successful post hoc design or analysis decision as a priori can still be achieved by publishing the paper in a different journal which is unaware of the pre-registration document.

1b) the credibility loss of a wider research agenda due to a single unsuccessful experiment can still be avoided by simply withdrawing the study from the journal and forgetting about it.

The take-home message is that one can opt-in and out of pre-registration as one pleases. The maximal cost is the rejection of one peer-reviewed pre-registered paper at one journal. Given that paper rejection is the most normal thing in the world for a scientist these days, this threat is not effective.

[Chris Chambers: “all pre-registrations made now on the OSF become public within 4 years – so as far as I understand, it is no longer possible to register privately and thus game the system in the way you describe, at least on the OSF.”]

2) Pre-registrations did not clean up other research fields

Note that the argument so far assumes that when the pre-registration document is revealed, it is effective in stopping undisclosed post hoc design/analysis decisions. The medical sciences, in which randomized control trials have to be pre-registered since a 2004 decision by journal editors, teach us that this is not so. There are four aspects to this surprising ineffectivetiveness of pre-registrations:

2a) Many pre-registered studies are not published. For example, Chan et al. (2004a,b) could not locate the publications of 54% – 63% of the pre-registered studies. It’s possible that this is due to the aforementioned publication bias (see 1b above), or other reasons (lack of funding, manuscript under review…).

2b) Medical authors feel free to frequently deviate from their planned designs/analyses. For example 31% – 62% of randomized controlled trials changed at least one primary outcome between pre-registration and publication (Mathieu et al., 2009; Chan et al., 2004a,b). If you thought that psychological scientists are somehow better than medical ones, early indications are that this is not so (Franco et al., 2015).

pre-registration deviations in psych science

2c) Deviations from pre-registered designs/analyses are not discovered because 66% of journal reviewers do not consult the pre-registration document (Mathieu et al., 2013).

2d) In the medical sciences pre-registration documents are usually not peer-reviewed and quite often sloppy. For example, Mathieu et al., (2013) found 37% of trials to be post-registered (the pointless exercise of registering a study which has already taken place), and 17% of pre-registrations being too imprecise to be useful.

[Chris Chambers: “The concerns raised by others about reviewers not checking protocols apply to clinical trial registries but this is moot for RRs because checking happens at an editorial level (if not at both an editorial and reviewer level) and there is continuity of the review process from protocol through to study completion.”]

3) Pre-registration is a practical night-mare for early career researchers

Now, one might argue that pre-registering is still better than not pre-registering. In terms of non-peer-reviewed pre-registration documents, this is certainly true. However, their value is limited because they can be written so vaguely as to be not useless (see 2d) and they can simply be deleted if they ‘stand in the way of a good story’, i.e. if an exploratory design/analysis choice gets reported as confirmatory (see 1a).

The story is different for peer-reviewed pre-registrations. They are impractical because of one factor which tenured decision makers sometimes forget: time. Most research is done by junior scientists who have temporary contracts running anywhere between a few months and five years [reference needed]. These people cannot wait for a peer-review decision which, on average, takes something like one year and ten months (Nosek & Bar-Anan, 2012). This is the submission-to-publication-time distribution for one prominent researcher (Brian Nosek):

hist_publication_times

What does this mean? As a case study, let’s take Richard Kunert, a fine specimen of a junior researcher, who was given three years of funding by the Max-Planck-Gesellschaft in order to obtain a PhD. Given the experience by Brain Nosek with his articles, and assuming Richard submits three pre-registration documents on day 1 of his 3-year PhD, each individual document has a 84.6% chance of being accepted within three years. The chance that all three will be accepted is 60.6% (0.8463). This scenario is obviously unrealistic because it leaves no time for setting up the studies and for actually carrying them out.

For the more realistic case of one year of piloting and one year of actually carrying out the studies, Richard has a 2.2% chance (0.2823) that all three studies are peer-reviewed at the pre-registration stage and published. However, Richard is not silly (or so I have heard), so he submits 5 studies, hoping that at least three of them will be eventually carried out. In this case he has a 14% that at least three studies are peer-reviewed at the pre-registration stage and published. Only if Richard submits 10 or more pre-registration documents for peer-review after 1 year of piloting, he has a more than 50% chance of being left with at least 3 studies to carry out within 1 year.

For all people who hate numbers, let me put it into plain words. Peer-review is so slow that requiring PhD students to only perform pre-registered studies means the overwhelming majority of PhD students will fail their PhD requirements in their funded time. In this scenario cutting-edge, world-leading science will be done by people flipping burgers to pay the rent because funding ran out too quickly.

[Chris Chambers: “Average decision times from Cortex, not including time taken by authors to make revisions: initial trial = 5 days; Stage 1 provisional acceptance = 9 weeks (1-3 rounds of in-depth review); Stage 2 full acceptance = 4 weeks”]

What to do

The arrival of pre-registration in the field of Psychology is undoubtedly a good sign for science. However, given what we know now, no one should be under the illusion that this instrument is the solution to the replication crisis which psychological researchers are facing. At the most, it is a tiny piece of a wider strategy to make Psychology what it has long claimed to be: a robust, evidence based, scientific enterprise.

 

[Please do yourself a favour and read the comments below. You won’t get better people commenting than this.]

— — —

Chan AW, Krleza-Jerić K, Schmid I, & Altman DG (2004). Outcome reporting bias in randomized trials funded by the Canadian Institutes of Health Research. CMAJ : Canadian Medical Association journal = journal de l’Association medicale canadienne, 171 (7), 735-40 PMID: 15451835

Chan, A., Hróbjartsson, A., Haahr, M., Gøtzsche, P., & Altman, D. (2004). Empirical Evidence for Selective Reporting of Outcomes in Randomized Trials JAMA, 291 (20) DOI: 10.1001/jama.291.20.2457

Franco, A., Malhotra, N., & Simonovits, G. (2015). Underreporting in Psychology Experiments: Evidence From a Study Registry Social Psychological and Personality Science DOI: 10.1177/1948550615598377

Lindsay, D. (2015). Replication in Psychological Science Psychological Science DOI: 10.1177/0956797615616374

Mathieu, S., Boutron, I., Moher, D., Altman, D.G., & Ravaud, P. (2009). Comparison of Registered and Published Primary Outcomes in Randomized Controlled Trials JAMA, 302 (9) DOI: 10.1001/jama.2009.1242

Mathieu, S., Chan, A., & Ravaud, P. (2013). Use of Trial Register Information during the Peer Review Process PLoS ONE, 8 (4) DOI: 10.1371/journal.pone.0059910

Nosek, B., & Bar-Anan, Y. (2012). Scientific Utopia: I. Opening Scientific Communication Psychological Inquiry, 23 (3), 217-243 DOI: 10.1080/1047840X.2012.692215

Open Science Collaboration (2015). PSYCHOLOGY. Estimating the reproducibility of psychological science. Science (New York, N.Y.), 349 (6251) PMID: 26315443
— — —

Are internal replications the solution to the replication crisis in Psychology? No.

Most Psychology findings are not replicable. What can be done? Stanford psychologist Michael Frank has an idea : Cumulative study sets with internal replication. ‘If I had to advocate for a single change to practice, this would be it.’ I took a look whether this makes any difference.

A recent paper in the journal Science has tried to replicate 97 statistically significant effects (Open Science Collaboration, 2015). In only 35 cases this was successful. Most findings were suddenly a lot weaker upon replication. This has led to a lot of soul searching among psychologists. Fortunately, the authors of the Science paper have made their data freely available. So, soul searching can be accompanied by trying out different ideas for improvements.

What can be done to solve Psychology’s replication crisis?

One idea to improve the situation is to demand study authors to replicate their own experiments in the same paper. Stanford psychologist Michael Frank writes:

If I had to advocate for a single change to practice, this would be it. In my lab we never do just one study on a topic, unless there are major constraints of cost or scale that prohibit that second study. Because one study is never decisive.* Build your argument cumulatively, using the same paradigm, and include replications of the key effect along with negative controls. […] If you show me a one-off study and I fail to replicate it in my lab, I will tend to suspect that you got lucky or p-hacked your way to a result. But if you show me a package of studies with four internal replications of an effect, I will believe that you know how to get that effect – and if I don’t get it, I’ll think that I’m doing something wrong.
If this argument were true, then the 41 studies which were successfully, conceptually replicated in their own paper should show higher rates of replication than the 56 studies which were not. Of the 41 internally replicated studies, 19 were replicated once, 10 twice, 8 thrice, 4 more than three times. I will treat all of these as equally internally replicated.

Are internal replications the solution? No.

internal_external_replication

So, does the data by the reprocucibility project show a difference? I made so-called violin plots, thicker parts represent more data points. In the left plot you see the reduction in effect sizes from a bigger original effect to a smaller replicated effect. The reduction associated with internally replicated effects (left) and effects which were only reported once in a paper (right) is more or less the same. In the right plot you can see the p-value of the replication attempt. The dotted line represents the arbitrary 0.05 threshold used to determine statistical significance. Again, replicators appear to have had as hard a task with effects that were found more than once in a paper as with effects which were only found once.

If you do not know how to read these plots, don’t worry. Just focus on this key comparison. 29% of internally replicated effects could also be replicated by an independent team (1 effect was below p = .055 and is not counted here). The equivalent number of not internally replicated effects is 41%. A contingency table Bayes factor test (Gunel & Dickey, 1974) shows that the null hypothesis of no difference is 1.97 times more likely than the alternative. In other words, the 12 %-point replication advantage for non-replicated effects does not provide convincing evidence for an unexpected reversed replication advantage. The 12%-point difference is not due to statistical power. Power was 92% on average in the case of internally replicated and not internally replicated studies. So, the picture doesn’t support internal replications at all. They are hardly the solution to Psychology’s replication problem according to this data set.

The problem with internal replications

I believe that internal replications do not prevent many questionable research practices which lead to low replication rates, e.g., sampling until significant and selective effect reporting. To give you just one infamous example which was not part of this data set: in 2011 Daryl Bem showed his precognition effect 8 times. Even with 7 internal replications I still find it unlikely that people can truly feel future events. Instead I suspect that questionable research practices and pure chance are responsible for the results. Needless to say, independent research teams were unsuccessful in replication attempts of Bem’s psi effect (Ritchie et al., 2012; Galak et al., 2012). There are also formal statistical reasons which make papers with many internal replications even less believable than papers without internal replications (Schimmack, 2012).

What can be done?

In my previous post I have shown evidence for questionable research practices in this data set. These lead to less replicable results. Pre-registering studies makes questionable research practices a lot harder and science more reproducible. It would be interesting to see data on whether this hunch is true.

[update 7/9/2015: Adjusted claims in paragraph starting ‘If you do not know how to read these plots…’ to take into account the different denominators for replicated and unreplicated effects. Lee Jussim pointed me to this.]

[update 24/10/2015: Adjusted claims in paragraph starting ‘If you do not know how to read these plots…’ to provide correct numbers, Bayesian analysis and power comparison.]

— — —
Bem DJ (2011). Feeling the future: experimental evidence for anomalous retroactive influences on cognition and affect. Journal of personality and social psychology, 100 (3), 407-25 PMID: 21280961

Galak, J., LeBoeuf, R., Nelson, L., & Simmons, J. (2012). Correcting the past: Failures to replicate psi. Journal of Personality and Social Psychology, 103 (6), 933-948 DOI: 10.1037/a0029709

Gunel, E., & Dickey, J. (1974). Bayes Factors for Independence in Contingency Tables. Biometrika, 61(3), 545–557. http://doi.org/10.2307/2334738

Open Science Collaboration (2015). PSYCHOLOGY. Estimating the reproducibility of psychological science. Science (New York, N.Y.), 349 (6251) PMID: 26315443

Ritchie SJ, Wiseman R, & French CC (2012). Failing the future: three unsuccessful attempts to replicate Bem’s ‘retroactive facilitation of recall’ effect. PloS one, 7 (3) PMID: 22432019

Schimmack U (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological methods, 17 (4), 551-66 PMID: 22924598
— — —

code for reproducing the figure (if you find mistakes, please tell me!):

## Estimating the association between internal replication and independent reproducibility of an effect

#Richard Kunert for Brain's Idea 5/9/2015

# a lot of code was taken from the reproducibility project code here https://osf.io/vdnrb/

# installing/loading the packages:
library(devtools)
source_url('https://raw.githubusercontent.com/FredHasselman/toolboxR/master/C-3PR.R')
in.IT(c('ggplot2','RColorBrewer','lattice','gridExtra','plyr','dplyr','httr','extrafont'))

#loading the data
RPPdata <- get.OSFfile(code='https://osf.io/fgjvw/',dfCln=T)$df
RPPdata <- dplyr::filter(RPPdata, !is.na(T.pval.USE.O),!is.na(T.pval.USE.R), complete.cases(RPPdata$T.r.O,RPPdata$T.r.R))#97 studies with significant effects

#prepare IDs for internally replicated effects and non-internally replicated effects
idIntRepl <- RPPdata$Successful.conceptual.replications.O > 0
idNotIntRepl <- RPPdata$Successful.conceptual.replications.O == 0

# Get ggplot2 themes predefined in C-3PR
mytheme <- gg.theme("clean")

#restructure data in data frame
dat <- data.frame(EffectSizeDifference = as.numeric(c(c(RPPdata$T.r.R[idIntRepl]) - c(RPPdata$T.r.O[idIntRepl]),
                                                          c(RPPdata$T.r.R[idNotIntRepl]) - c(RPPdata$T.r.O[idNotIntRepl]))),
                  ReplicationPValue = as.numeric(c(RPPdata$T.pval.USE.R[idIntRepl],
                                                   RPPdata$T.pval.USE.R[idNotIntRepl])),
                  grp=factor(c(rep("Internally Replicated Studies",times=sum(idIntRepl)),
                               rep("Internally Unreplicated Studies",times=sum(idNotIntRepl))))
  )

# Create some variables for plotting
dat$grp <- as.numeric(dat$grp)
probs   <- seq(0,1,.25)

# VQP PANEL A: reduction in effect size -------------------------------------------------

# Get effect size difference quantiles and frequencies from data
qtiles <- ldply(unique(dat$grp),
                function(gr) quantile(round(dat$EffectSizeDifference[dat$grp==gr],digits=4),probs,na.rm=T,type=3))
freqs  <- ldply(unique(dat$grp),
                function(gr) table(cut(dat$EffectSizeDifference[dat$grp==gr],breaks=qtiles[gr,],na.rm=T,include.lowest=T,right=T)))
labels <- sapply(unique(dat$grp),
                 function(gr)levels(cut(round(dat$EffectSizeDifference[dat$grp==gr],digits=4), breaks = qtiles[gr,],na.rm=T,include.lowest=T,right=T)))

# Get regular violinplot using package ggplot2
g.es <- ggplot(dat,aes(x=grp,y=EffectSizeDifference)) + geom_violin(aes(group=grp),scale="width",color="grey30",fill="grey30",trim=T,adjust=.7)
# Cut at quantiles using vioQtile() in C-3PR
g.es0 <- vioQtile(g.es,qtiles,probs)
# Garnish (what does this word mean???)
g.es1 <- g.es0 +
  ggtitle("Effect size reduction") + xlab("") + ylab("Replicated - Original Effect Size") + 
  xlim("Internally Replicated", "Not Internally Replicated") +
  mytheme + theme(axis.text.x = element_text(size=20))
# View
g.es1


# VQP PANEL B: p-value -------------------------------------------------

# Get p-value quantiles and frequencies from data
qtiles <- ldply(unique(dat$grp),
                function(gr) quantile(round(dat$ReplicationPValue[dat$grp==gr],digits=4),probs,na.rm=T,type=3))
freqs  <- ldply(unique(dat$grp),
                function(gr) table(cut(dat$ReplicationPValue[dat$grp==gr],breaks=qtiles[gr,],na.rm=T,include.lowest=T,right=T)))
labels <- sapply(unique(dat$grp),
                 function(gr)levels(cut(round(dat$ReplicationPValue[dat$grp==gr],digits=4), breaks = qtiles[gr,],na.rm=T,include.lowest=T,right=T)))

# Get regular violinplot using package ggplot2
g.pv <- ggplot(dat,aes(x=grp,y=ReplicationPValue)) + geom_violin(aes(group=grp),scale="width",color="grey30",fill="grey30",trim=T,adjust=.7)
# Cut at quantiles using vioQtile() in C-3PR
g.pv0 <- vioQtile(g.pv,qtiles,probs)
# Garnish (I still don't know what this word means!)
g.pv1 <- g.pv0 + geom_hline(aes(yintercept=.05),linetype=2) +
  ggtitle("Independent replication p-value") + xlab("") + ylab("Independent replication p-value") + 
  xlim("Internally Replicated", "Not Internally Replicated")+
  mytheme + theme(axis.text.x = element_text(size=20))
# View
g.pv1

#put two plots together
multi.PLOT(g.es1,g.pv1,cols=2)</pre>
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