Blog post on the occasion of Strack Stepper & Martin not replicating, and thoughts about what to do next.

Strack didn’t replicate. STRACK DIDN’T REPLICATE. If you wonder which Strack (which, really, one should as he is prolific), I’m clarifying – it is the one where you stick a pen in your mouth and it makes you think a cartoon is more (or less) amusing depending on how that pen-holding is screwing up your face. Correct is to call it Strack Martin & Stepper (1988).

And, I’m a bit sad. We were going to be part of the replication effort, but last fall semester hit hard, and I had to give up. We needed to collect data before students had heard of the experiment, and we just did not get it together in time. I had predicted there would be an effect.

But, perhaps that should have been a bit moderated. I believed SOMETHING would happen, based on work that were done in the Niedenthal lab, but that effect was a little bit different.

She did a series of morphing studies, where faces changed from one expression to another, and people had to detect the change. The main exploration was whether emotional state has an effect on perception of emotional stimuli. But, in one variant she used the Strack manipulation. For good reason. You want to tease out the edges of an effect. Would it be enough with just facial feedback, or did we need to do the full-blown emotion induction? But, what seems to have happened instead was that holding the pen in the mouth disrupted mimicry – that is the published story.

But, I really think we need to put the study in context. As I wrote in my blog on my beginning trace, the paper is just one tile in the mosaic of studies investigating the role of facial feedback in emotion  processing (and I’m deliberately vague).

One can easily trace this back all the way to the James-Lange theory of emotion, which crudely (and somewhat errouneously) is portrayed in introductory books as you feel afraid, because you are running away from the Bear.

But lets narrow it a bit more – the Strack experiment was part of a much larger body of research looking at the role of facial feedback.

The facial feedback story (as I tell it to my undergraduates) goes roughly like this (admittedly with plenty licence).

When Ekman, Friesen and Ellsworth were figuring out which facial movements could be considered primitives of expressions (the FACS), evidently they noticed that when they worked on furrowing brows, and gaping their mouths into snarly shapes, they got into more snapping and actual snarling * Could it possibly be that screwing up your face into emotional expressions resulted in a feedback to the emotion processing areas in the brain, possibly giving rise to a faint experience of that actual emotion. And, from there, they proceeded to experiment on that notion, usually by asking people to position their face in a certain way (e.g. pull down the outer corners of your mouth. Stick out your tounge. Wrinkle your nose).

I don’t think they were alone pursuing facial feedback. Zajonc has worked on this. Laird has worked on this. Hess has worked on this. Alan Fridlund looked at this. Levenson, Lanzetta, and Gross (the beginning of emotion regulation work), and on and on and on.

What the Strack paradigm specifically addressed was the objection that people may figure out that they were asked to screw up their face in disgust, and, being compliant participants (which my experience says is more common than the recalcitrant) they reported more disgust or amusement etc.

It really was addressing this  particular objection in a very clever way. According to the standards of the time, it worked. And, for some reason, it became THE experiment (in textbooks etc) which demonstrated the existence of facial feedback.

Which, of course it isn’t. No single study ever is!

If someone thinks this refutes the facial feedback hypothesis, or embodiment, that person is doing the same reasoning fallacy as when someone tests a gaggle of undergraduates in Georgia, and then claims to have found evidence for some universal principle of human function.

Instead, be more precise – sticking a pen in the mouth of an individual in order to make them pose their face in a semblance of smile or pout, without alerting them to the fact that you are interested in what happens when the face is put in different positions – seem to have no effect on how funny a (by now) fairly large sample of participants think funny cartoons are.

And, yes, after this experiment, I actually strongly believe just that – which is a very very narrow area.

If we really want to evaluate the veracity of the facial feedback thesis, we must do better than single directed RRR, because this is a web of experiments evaluating a theory.  We need to undertake a comprehensive review.

There needs to be a review of mimicry – human tendency to mimic the facial expressions they are exposed to. There are lots of experiments. Some filming faces, some measuring EMG, some looking at brain correlates, and there are a lot of papers here (I used to read this as a doctoral student).

Next, what happens when mimicry is disrupted? Through instruction (don’t show what you feel – keep a stone face), or physical disruption (e.g pens in mouth, botox).

Then, we need to review what we know this mimicry (or disrupted mimicry) results in for the individual. (Suggestions – mild experience of the same emotion, changes in physiological signatures, perceptual sensitivity to congruent materials, enhanced emotional reaction to other materials).

I don’t think the facial feedback hypothesis is stupid. Humans have a tendency to imitate and entrain (we think anyway), and it is a feasible first mechanism for trying to understand how we communicate, and how we understand one another. (Even my son has heard that mimicry is the basis of empathy – and he is 13 – it has face validity, but the evidence needs scrutiny). I tend to take an ecological/evolutionary view of things, which is why I think it is non-stupid.

Now, there is a lot of research on this. Why not evaluate it, see how strong (or not) it is, possibly do some very directed experiments once there is a better map (if warranted), and do it on more than undergraduates.

I think I will actually do this – but, of course, I will have to get help.

* I have no idea where I picked up this anecdote. Could be you-tube, could be the conference I went to 2003, could be some paper.)

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On Brannigan (rise and fall of Social Psych), and Henrich (the secret of our success) and psychological research in general.

When I read David Hull’s ”Science as a process (1988), he reiterated one controversy that I found interesting for Psychology. His area were systematics – how to best classify animals and plants (the stuff of Linnaeus – science is never done). The controversy were between those that thought classification needed to have an evolutionary grounding – species have a history, and that  ought to be reflected in the classification – and those that thought one needed to classify based on (more or less) observable features existing right now. (The controversy is discussed in the two chapters “Down with Darwinism-Long live Darwinism, and Down with Cladism – Long Live Cladism, if I recall right).

From my naïve outsider view I first thought that of course you want to use the evolutionary history to figure out how to classify living things, but as the opposing side pointed out – even if one doesn’t doubt the importance of evolution, the actual evidence available was so spotty that it wasn’t possible to use it as basis for classification. Instead, one should stick to what is observable now for classification. As Hull points out, what is observable is also not quite straight forward. (Visible traits? Genetic markers – which requires a whole lot of apparatus to detect?  Also, what a particular trait is had at one point been hotly debated – his example is what is the dorsal and ventral part of an animal. Observation of current traits is theory-laden, which perhaps we as scientists forget).

My mind went to social psychology/evolutionary psychology. Of course humans, and their psychology are a product of evolution, but, as many critics have pointed out, minds and behaviors don’t fossilize well, so much of the work has to be done by careful (but still in part speculative) theory applied to present day humans. Perhaps there is a real point in cataloging current humans and their traits and behaviors, before considering evolution. Or some iterative work combining the two.

This weekend I read two books (well, I’m not finished with one of them yet): August Brannigan’s “The rise & fall of Social Psychology (subtitle the Use and Misuse of the Experimental Method) published 2004, and Joseph Herich’s “The secret of our success: How culture is driving human evolution, published 2015.

I got the tip for Brannigan’s book in a Facebook discussion (from a European student). I think it is a must read. Of course, Social Psychology doesn’t seem to be in any kind of post-experimental wasteland, although it has been in the focus the current so called crisis following the refusal to publish a non-replication of Bem’s ESP work, and the vast fraud of Diederik Stapel.

I think it is a must read for anyone interested in social psychology, and anyone interested in psychology as a science. Did you know that Festinger left Social psychology to take up work on perception, and then eventually “exploring prehistoric and archaeological data” (as per the Wikipedia page here) , evidently being disappointed in psychology.

Did you know that there have, time and again, been accomplished researchers that critiqued Social Psychology scathingly? Decades ago? I recognized none of the names, possibly, as Hull also points out, that they were alone in the wilderness with no Deme advancing their position.

As a grad student, I felt frustrated that there seemed to be no larger theoretical framework from which to reason about psychology, and my adviser pointed out that, yes that is the case. The field is filled with mini-theories, but nothing over-arching. Evidently, from this book, far better scientists than I have noted this, complained about it (for example – chapters in a social psychology book could be shuffled, with no ill effect) thus, there is no cumulative understanding, no placing effects in a larger frame (e.g what can be attributed to situation, what to traits, what to larger social circumstances etc – Brannigan is a sociologist, and works in criminology).

He is especially critical about the sine qua non of the experiment in social psychology (at the exclusion of field work and other methods). This, he claims, has in part lent social psychology an air of proper hard science which has allowed it a great deal more influence in the actual world than he thinks is warranted (e.g. work on violence in movies). But, the experiments seem more to be performances and demonstrations rather than actual tests of theories. There are few falsifications (as we know). Positive supportive results are the only thing presented. In effect, the experiments are de facto anecdotes that support a narrative that is already decided.

As his cases in point he uses Festingers dissonance theory (there are aspects of it that are absurd – like the enormous payments some of the students get. 20 dollars then was quite a bit more than it is now – sometimes I first saw Tom Stafford point out); Muzafer Sherif’s work on the autokinetic effect, which was claimed as evidence for norms and and who one conforms to – but which is (per Brannigan) very much removed from actual social situations, and a rather minute piece of evidence for building a larger piece a theoretical narrative: Zimbardo’s Prison experiment – with the ethics problems; Milgrams work on obedience which perhaps is not so much about obedience to authority as it has to do with the expectations of an experiment (e.g. it is an experiment, they will not allow anything bad to happen, so it is OK to comply – this is not what happened in Nazi Germany); Asch’s work on group pressure, and all the work on the horrors of TV imparting violent behavior to our children/making guys watching Porn being more OK with rape – which he deems rather shallow (so many more interesting questions), an expression of class (we don’t belong to those nasty unwashed TV watchers) unduly influential (bans on violence on TV, bans on Porn), and neglecting truly interesting questions such as immersion, narrative, separation of story from reality (although I do think there is work on this – albeit maybe not so splashy in the news).

Yes, there is more to Social Psychology, but, no, we are much too enamored of the experiment, see earlier critiques by Paul Rozin (2001) Social Psychology and Science. Some Lessons from Solomon Asch, Robert Cialdini (2009) We have to break up, Martin Orne (1962) On the social psychology of the psychological experiment. We may not know enough about a phenomenon to actually do an experiment (difficulty falsifying, because we are making too long chains of assumptions between how we do it, and what we actually want an answer to), we do it on populations that already have an idea about how to be good subjects, and will thus behave in a manner that has to do with the experimental situation and not give us any answer to what we want to test, etc.

But, go read. Even if you don’t agree. As scientists, we need to have statements that we can use as foundation of our critique.

Which brings me to the Henrich book.  His thesis (in my interpretation) is that our special feature is our capacity for cumulative cultural learning. More-over, that capacity is something that feeds back on genetic evolution. One example is lactose tolerance (which is fairly standard). If you have animals that give milk, there may be an advantage to those individuals that don’t shut down the lactase digesting hormone once weaning is done to get better nutrition and hydration from unprocessed milk (cheese and yoghurt chews up the lactose so you don’t have to be a lactase mutant).

Another example is the human as long-distance runner – in order to track down and kill large animals. He suggests a number of adaptations – one of particular interest is how to keep cool while running long distance in a hot climate – hairlessness and sweating. But, sweating means that there must be a good supply of water that can be sweated out to cool us. Now, that is not something we are born with, unlike, for example, camels. We can only store so much water. His point is that this adaptation must have occurred after humans figured out how to externally access water: Water pouches, straws to access pools in tree-trunks, recognition of plants and other signs that indicate where water or watery plants may be, lore to keep track of water-holes, etc.

By now, I’m reading about kinship, sharing rules, food preparation rules, imitation and faith. All of these abilities must hinge on some psychological capacity, some bred in bias on where it is best to look: who to imitate, who to listen to, how to police others to do the “right thing”, and all without us necessarily understanding the why. He claims cumulative cultural evolution is smarter than us.

Many of these “biases” do show up in Cialdini’s six ways to yes in persuasion (and I’m sure Cialdini is quite aware that there is an evolutionary quality to those). We reciprocate, we look to authority (possibly more the prestige type than the dominant type), we look to the crowd, tough rituals make us more committed, we look to those we like and like us and are like us. These little biased hooks are what allows us to accumulate culture over long times.

I’m thinking, here is a more overarching theoretical framework from which to reason about psychological phenomena. It may not be right, but it is useful, and it is something one could test. There will be cultural differences – where is the underlying invariant?

I’m a big fan of ecological psychology also – but it seems like it is still best applied to perception/action (although I have seen attempts at ecological social psychology). This is also, in many ways, grounded in an evolved thinking – minds and bodies have evolved to capitalize on our surroundings. Perhaps eventually these can be brought together (or not).

There is a point in doing research on contemporary beings (because, who else?), without necessarily using a deeper evolutionary thought. But, perhaps a though on what brought this part out could help guide where to look and what to attempt to falsify. I’m a little bit tired of the narratives in social psychology textbooks. The effects must be placed in the context of effects of traits/personality, class, social systems, cultural systems, etc., and I rarely see that. (Nazar Akrami has looked at the relative contribution of personality factors and more social psychological factors and found that personality dominates – but more like this is needed  ).

Cialdini, Influence.

Cialdini (2009). We have to break up. Perspectives on psychological science, 4, 5-6.

Orne, Martin (1962) On the social psychology of the psychological experiment. With particular reference to demand characteristics and their implications. American psychologist, 17 776-786.

Rozin, Paul (2001) Social psychology and science: Some lessons from Solomon Asch. Personality and Social Psychology Review, 5, 12-14.

Brannigan, Augustine (2004) The rise and fall of social psychology.

Henrich, Joseph (2015). The secret of our success.

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Tracing Strack, the preamble

I’ve started a second trace! A bit to pursue proof of concept, get a feel for extendability. A trace is, after all, a bit like a case study. I’ve selected the Strack, Martin and Stepper (1988). Better known as the one where participants get to hold a pen in their mouths to get their face shaped like a smile or a frown, without them really realizing this is happening. This is also a paper that is under PoPS registered replication. I was going to participate as one of the independent labs, but work hit me and my team (I became director of our international Masters), and I just had to give up. (Still feel a bit sad about that).

It is, to cite Jens Förster (citation # 102 in my trace) a Classic. * It is so generally well known that in the instruction for the registered replication we were asked to make sure that the population we tapped were not aware of the effect – that is, get the psych undergrads before the Emotion module, or tap other undergrads (we were planning on using the film/linguistics/humanities set). The paper has a reputation! Of course we want to replicate it.

I pulled the data for the trace on the 29th of April, 2016, and at that time, the paper had been cited 544 times (all social science citation index). Not as many as Srull & Wyer (1979) that I pulled a year before, but this was published a decade after. Not shabby.

I also decided to be more ambitious with the trace this time. Instead of the 5 first year (53 article), I decided to trace the first 150 articles. (I am going solo so far, and I am going the artisanal way. No automatic scraping of info here!)** First citation is in 1989, the last in 2006 so we are spanning over a decade and a half. I figure that might also be enough to find  possible citation distortions (I have). This actually includes a paper where I’m co-author. We used the Pen in the Mouth technique, but it didn’t seem to work as enhancement, but more as a mimicry-disruptor. (Niedenthal  et al 2001), which still is some kind of effect on Facial Feedback that is interesting.

I realized early on that the trace here had a different nature from the Srull & Wyer trace. The Srull & Wyer paper were very much an origin paper for subsequent work on Social Priming***, whereas the Strack et al is a relatively recent paper in the tradition of facial and bodily feedback, which can reasonably be traced back to the James-Lange theory of emotion, was under ongoing investigated by the Ekman Deme**** and the Zajonc Deme, and in many ways was an ingenious technical solution to the pesky demand objection that came from asking people to pose their faces in emotional configurations.

Classifying the papers (based on the abstracts) also was different. For the Srull & Wyer trace I classified papers as either extending related or oblique. My intention was to particularly pay attention to those papers that extended the priming idea, whereas for other papers I would only look closer at the citation patterns. This was not so evident for the Strack Paper. Yes, there were clear obliques (Emotions and God, Education, Robots – although that turned out to actually fit within extension), but it was far less obvious which papers extended the work and which were related but not extending. This is quite possibly because the Strack Paper isn’t an origin paper for a particular area of research, but a paper that is mid-stream in ongoing research on bodily feedback on affective processes. Even if I did a rough sorting, I then went in and made a somewhat more fine-grained classification of the topics. The majority involve research on facial feedback (39), but there are also papers on Arm Flexion (17), emotional expression (7), Embodiment (7), Emotion regulation (6), mix of other types of bodily feedback including head nodding (11) and effects of induced mood or emotional states (25) which all seem to be somewhat relevant and could potentially be extending.

So far, I have pulled citations from all the papers I could find without having to go too far out of my way. (I have a handful from papers like Cognition and Emotion and Cortex which evidently I have to request prints rather than download PDF’s, and there are also a few non-english papers that I can’t get to – I included a bit more than just peer reviewed papers in this trace).

That is 128 papers. One thing I noticed when doing my Srull & Wyer (1979) trace was that in papers that extended their work, they tended to be cited multiple times  (both for the theoretical and empirical background as well as for methods and in the discussion). In the related and oblique papers they tended to be cited maybe one or two times.  This is the citation patterns so far for Strack et al.

Times cited in paper Frequency
1 90
2 15
3 12
4 7
5 0
6 1
7 1
8 0
9 1
10 0
11 0
12 0
13 0
14 0
15 1


As I actually go and pull the citations manually (with the help of the search function, when that works), I do get a quick feel for what is going on. The paper is highly cited, because this is an important addition in the ongoing work on bodily feedback, as it rules out demand. But, direct extensions of the technique are not that common. (The one with 15 cites most definitely did a replication).

In the trace, I’m most of all interested in the direct extension of the source work (it doesn’t have to be like that. Lots of questions can be asked of a trace), so what I’m directly scrutinizing may be rather small in the end. But, I’m starting to look closer at the various experiments on bodily feedback to see what that can yield.

Some refs

Förster, J (2004) How body feedback influences consumers’ evaluation of products. JOURNAL OF CONSUMER PSYCHOLOGY.

Hull, Davis (1988). Science as a process.

Niedenthal, PM; Brauer, M; Halberstadt, JB; Innes-Ker, AH (2001). When did her smile drop? Facial mimicry and the influences of emotional state on the detection of change in emotional expression. Cognition and Emotion.

Strack, F, Martin, L, & Stepper, S. (1988) Inhibiting and facilitationg conditions of the human smile: A nonobtrusive test of the facial feedback hypothesis. Journal of personality and Social Psychology, 54, 768-777.



*Förster collaborated with Strack quite a bit on similar questions, so I think he spoke about it from inside this particular Deme.

** because I haven’t spent time to figure out how to.

*** Yes, I know people object to this, because there are so many different variants that this doesn’t capture what it is about. But, it is useful to distinguish it from the type of priming that seem just focused on associative networks – like the doctor-nurse, apple-orange thing, which is quite robust.

**** A deme is, in biology, a local breeding population. I also found out (looking for definition) that it is an old greek word for a village or district (distinct from Polis). I got it from Hull (1988)  (who most likely got it from  biology. In his meaning a scientific Deme is a group of scientists that work more or less cooperatively on a particular idea in science (the cooperation doesn’t need to be uncontentious).

*****Simine Vazires penchant for asterisks are spreading. A bit of cultural evolution (the social copying kind).

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Tracing Srull & Wyer manuscript

I wrote a manuscript detailing my Srull & Wyer trace (the one I have been blogging about). If anybody cares to read and give some comment, I’d be grateful. At some point I’d like to submit it.

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All references are equal, but should some be treated as more equal than others? On the data-set authorship discussion.

There’s been an interesting discussion on data-sharing and how to properly give credit when you are using someone else’s data on both Facebook and Twitter. Candice and Richard Morey  did a nice blog-post on why sharing data should not automatically mean authorship. Talking to other researchers, that seems to be part of what the Vancouver and beyond suggests for criteria for authorship. The proper way to credit a shared data-set is to include a reference.

Authorship and references are the two traditional ways of assigning credit. For the individual scientist authorship signals origination, and reference signals the use other scientists find in the original work.

But, references are a strange measure of success of an idea/work. When I was going through my Srull & Wyer (1979) trace, I collected all the places in the manuscripts where they had been cited in the first 53 articles that cited them. The reason for citing them ranged from the peripheral to the profound. Examples of the peripherals was an opening sentence where the author cited them (along with others) as evidence social psychologists were now interested in cognitive explanations for social phenomena, and a foot-note where they stated that the current paper was not interested in the priming phenomenon, but one should look to Srull & Wyer 1979 if one was interested. In the profound, they were cited multiple times because the research essentially extended the original research.

This shouldn’t be surprising. We are trained to cite just about everything we have gotten from other researchers, be it trivial, profound or antagonistic, and this is perfectly fine. I like being able to look in the references to pursue ideas that may not be central to the present research. I even find it disconcerting when it doesn’t exist. I started reading William James “Principles of Psychology” and found it distracting that there were no references to statement that it was clear he had learned from others. But, of course, in our citing practices, papers will vary in their degree of centrality.

None of that is evident from a reference list.

It seems we may need to look over how we are apportioning credit, especially when authorship and references are given so much weight in important measures of success. I don’t have a clear thought on how to do this, because there are always downsides, and simply complicating things by grading the importance of a cite is something that I instinctively think can become problematic.

Perhaps one needs to abandon the traditional ways of indexing success is the way to go (I doubt that will be the case).

But, should we distinguish between peripheral and central contributions from earlier research? Sharing stimuli or sharing data-sets or using tested paradigms, questionnaires, analysis schemes – are they “worth” more than the more peripheral citations, or do we run other risks of conflict and credit arbitrage?

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A longish tl;dr conclusion of Srull & Wyer trace

Social Priming is in the news again. Well, Pashler et al published a critique of a recent money-priming paper, and Neuroskeptic wrote it up. So, I figured I would advertise for my Srull & Wyer trace from last spring, where I follow citations forward from Srull & Wyer (1979) – the Ur-Donald paper (and, possibly along with Higghins Rholes & Jones 1977, one of the papres that started the social priming area). I’m still working on a manuscript for this. Not so easy when you use non-traditional (for psychology) methods. (Plus teach too much).


I got a tweet message from Michael Inzlicht asking for the TL;dr (or, take-home message as he said). It isn’t that easy. No tweet-size take-home really. But, I thought I should try to summarize a little bit about what I have learned.

First, I think priming happens – when the priming is strong, relentless and conscious. Srull & Wyer had participants unscramble an awful lot of hostile sentences, and the more they unscrambled, the more they judged Donald to be hostile. The effect was similar for kind, but somewhat weaker. There is nothing subtle about this. What people did not guess was that the rating of Donald had anything to do with the sentences.

I’m much more doubtful about the subtle primes. The few instances, the oblique influence chains, the outside awareness primes. The difference in means there are smaller. In fact, sometimes they seem more like published null results than anything else. But, with only 11 studies in total, and just a handful doing subtle primes, there isn’t much I can say.

But, putting it differently –I think Srull & Wyer would replicate. I’m guessing those that show films or pictures might (but am less certain), and I have big doubts about the subtle/outside consciousness would do so.

Few other interesting things:

The early papers being inspired by Srull & Wyer don’t really work on extensions, rather than, in essence saying “oooooh, look at this cool paper. Wonder if we can adapt it for our own purposes).

The number of participants in each cell is very small in general, so most of the experiments are underpowered.

Standard deviations are only reported in one of the 11 extension papers. It is also the only paper that report effect sizes. It is also never cited… But, there are also a few papers that publish the F-table, which actually is nice.

When I try the R-index and p-curving, it appears that there is over-reporting of significant results, but there may be some evidential value in the lot (but it is so heterogeneous, it is hard to tell).

It is also surprising how quickly the subtle primes dominate.

Some of the papers make me sad. So much careful work, such low power.

Others irritate me with their handwavey confidence, noice inducing methods, and certainty in pronouncing results that, for all I can see, is analyzing noise.

So, shorter: I believe what happened right before will influence how you see the next thing, even if you don’t think they go together (a kind of pathdependence), especially if the next thing is kind of ambiguous. Especially if the former thing is kind of strong and conscious. But, I severely doubt the more subtle kinds as a general effect.

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A past crush passes.

When I was eleven, my parents were involved with a school-Theatre Project for my province: Dala-teatern. This meant that we were visited by the actors and the director working on setting this up, having discussion and what not.

I was particularly taken by the Young director. He was skinny, Brown-eyed with long-swoopy dark hair, and looked all dashing, smoking his pipe.

He occupied my fantasies, and I kind of knew that I was still not quite old enough to understand all the parts of this, but if he could just wait until I was a bit older.

He was 22, it was obvious to everybody that I was having a crush. I’d fetch his ashtray, I’d sit in the room listening to him and my parents talking. My mom even commented that he obviously had a Little slave in me.

Nothing really came of the project. I guess a few attempts, and then the big ideas petered out and the actors and the dashing director stopped visiting.

I knew Before i moved to the US that he had kept working in Theatre and published some book, because you know someone, you just notice the name.

Even the first time I returned to Sweden my sister told me he was doing directing, and had continuted writing books, and that was interesting that my old crush were kind of a public person.

Actually, at some later visit, I got some of his books – mostly murder mysteries. Ripping yarns, but very gruesome murders. Some were set up North, others way down South.

As time passed, I realized that his books were now translated into many many languages – an american friend of mine recommended one. Once back, I also realized that the murder mysteries set down South had also been turned into several TV series on Swedish television.

Then the BBC did one with Kenneth Branagh starring as Kurt Wallander.

And, today, a push-notice on my phone told me he had died. From cancer. 67 years old. RIP Henning Mankell.

(I thought of bringing this Little story up in my class on basking in others glory, but I was way too embarrassed. It was my 11 year old crush. I had a few others, and none of them became internationally famous. I’d be sad finding out they died, too, but I’m unlikely to find out via push-notices)

On Edit:

I found a Picture. From a few years later. Click the Dalateatern – second from the left.

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R-index and p-curve of the Srull & Wyer trace.

I have been continuing playing with the data on the Srull & Wyer (1979) trace. First the R-index

Median FHT
Success Rate Obs. Power Inflation Rate R-Index r(N,d)
All 0,808 0,607 0,201 0,405 -0,510
Sub-set 0,883 0,710 0,173 0,536 0,074
P-App 0,78 0,66 0,12 0,54

For the first two I used Ulrich Schimmach’s Excel-sheet*.The first one uses all the studies (including S & W 1979) that pursue priming. (I leave out the Lord Foti & Devader, because priming didn’t work, and results were left out).

The second is on the subset of studies that I think are directly exending Srull & Wyer.

The last one is the R-index result I got from the subset I used when creating the P-curve on the nice Shiny Apps p-checker.

Which brings me to the P-curve.


Which I got off the P-curve app (before it decided to not work today.). I tried to scrape off the results that test whether priming works (comparing different degrees of priming, or priming with control) – which is not entirely easy to find. Hopefully I haven’t messed up too much.

*(He kindly provided me with some answers to things I didn’t quite understand).

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Srull & Wyer trace – some global stuff.

Back in February, I wrote that I was curious about tracing Srull & Wyer (1979) forward. So, actually, I decided to do it. You may have noticed, as I have summarized some of the interesting papers in this trace. (They come right before this post, so I don’t bother to link).

The idea is in part from David Hull (science as a process, you need to look at how the idea develops), and in part because Social Science Citation index. I figure we have all used it to see if something interesting came of that paper that we could incorporate in our own review. Or possibly, if something interesting came of ones own paper.

I must say, the site has a lot of nice tools for summarizing cites.

So, here are some taken directly from Web of Science (or is it Thomson Reuters now).

Citation graph

Impressive amounts of cites for this paper, so I think I’m right in considering it a classic.

And, look who the top citing authors are!

Did you startle at number two?


But, back to what I decided to do.

Obviously, I’m not going to painstakingly collect and categorize 800 papers all by myself. (Or, maybe not so obvious, come to think about it). But, I wanted to be quite formal about what I set out to do.

I wanted to see how this idea has evolved over time, and tracing citations may be a way to do this. I began to think about it as a Golgi Stain, but in the virtual felt of science rather than cortex.

I decided to pull all the papers in the first 5 years. (Turns out that was 53.) I could find all but one of them (A swiss paper, barely cited).

Through the loveliness of PDF, I screenshot the Abstract, and found and screenshot every time that Srull & Wyer 1979 was cited in the paper.

In two it was only cited in the reference list…

Median number of times cited is 1.

Then I did some rough classifications based on the Abstract. I noted whether it reported an experiment, if it was a review or some other type of theoretical paper (there were a few proposed models and measures). I also noted down if I thought it actually extended Srull & Wyer, whether I thought the topic was related but not directly extending, and whether I thought it was more oblique.

Here’s a Time line.


There were 11 papers that looked like they pursued an extension, out of the 53 I pulled, so I began looking at them more closely. I blogged my initial scrutiny of just about all of them (Except Srull & wyer 1980, for some reason).

Extending papers 1

Extending papers 2

(I think you can click on them to make them readable).

These are some simple classifications of type of priming, priming measures and construct primed.

Priming task and measure Primed constructs

It gives a somewhat, well, motely impression. The extensions go in all sorts of directions, and are not quite extensions, but more inspired by the work. Patterns are emerging, but perhaps it would be worth it going 50 more papers (or 5 more years) in the future for a more coherent trace.

I’m now working on pulling together something more coherent with these papers. (Turns out one of them found no priming effect, and was oblique enough that I won’t include it).

I’m working on learning the R-index, which I think is reasonable even across such a motely bunch of papers (I do have a very rigid rule for what is pulled in), and possibly trying the p-curve and v-index.

N-s are on the small side. There are lots of places where error can creep in. Some papers are more trust-inspiring than others.

I’ll be updating, as I proceed. I’m planning to make a paper out of it, because it is interesting, but the method for selecting papers is a little unusual, at least for something formal.

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Wyer, Bodehausen and Gorman. Final paper in the trace of Srull & Wyer 1979

The final paper in this early sampling that directly look at social priming is one on Rape judgment by Wyer, Bodenhausen and Gorman. “Cognitive Mediators of Reactions to Rape”

This is another complex design with not many participants. As I mentioned on twitter, lots of sparsely populated cells.

They do mention that they consider the work exploratory rather than confirmatory. I kinda like that.

The idea here, like much of this literature is that when you are faced with making a judgment about a situation or a person or an item that is somewhat uncertain (in this case, descriptions of rape-cases), you won’t take the time searching through all of your memory to find some matching prototype, but most likely stop with some information that you have already in mind. Such as something that was presented in that earlier experiment that has absolutely nothing to do with this experiment….

As with the others, there is a great deal of reasoning about how different kinds of primes may push around judgments, and I won’t really go into these here, because I really don’t think a cell size of 5 can properly answer those, but instead be more focused on what they did.

They recruited an equal number of men and women – students. 35 of each to be exact.

The cover story for the priming was that they wanted to investigate reactions to pictures that are shown in public media, that some people may think are morally objectionable. The priming materials consisted of 10 slides of pictures, where the “to be primed” concept was placed in the 3, 8th and 10th position.

They came up with 7 different priming conditions!

  1. Negative outcomes of aggression (basically, dead people)
  2. Aggressive acts that are considered socially OK (e.g. police subduing a criminal)
  3. Non-sexual intimacy between man and woman (e.g. holding hands)
  4. Female sex object (photos and cartoons)
  5. Sexual arousal (for men, or whoever digs women)
  6. Sexual arousal again – even more explicit

In the actual task, they first viewed all 10 slides without doing anything. In the second viewing, they reported their reactions to the slides using a checklist. They are not entirely clear what the checklist consists of, but they correspond to the following 5 factors:

  1. People are cruel and inhumane
  2. Aggression is socially sanctioned
  3. Intimate relations are desirable
  4. Women are sex objects
  5. Sexual arousal.

Come to think about it, could you really consider showing pictures of dead peeps, officers subduing perps, and women masturbating as priming? I can kind of see them thinking of it like that in 1985 (or prior, as the research must have been done before), but these are the types of stimuli that are used to induce momentary affect – such as Lang’s IAPS.

After this, they went on to the second experiment, which was more of a forensic experiment. Each participant was asked to judge 5 different descriptions of rape-cases on 10 different factors.

Each case described a rape. In each case, there was one section that described the perpetrator as either a stranger or an acquaintance. Another section stated that the woman had either resisted or not resisted (“fearing that she might provoke more serious injury to herself”).

A final fifth version omitted both types of statements. It wasn’t analyzed but was simply there so they could present the order of the cases in a latin-square manner across the 5 individuals per cell.

The participants rated each case according to following (using a 0-10 scale)

  1. a) extent which woman provoked rape
    b) likelihood she could have avoided
    c) likelihood she responded correctly
    d) extent her life in danger
    e) how emotionally upset she was
    f) how harmful effect rape had
    g) belief defendant should be convicted
    h) likelihood he will be convicted
    i) likelihood story is true

The ratings were aggregated into 4 composites
1) Perception of Crime (d, e, f)
2) Perception of victim – true (i)
e) Perception of victim – responsibility (a, b, c*)
4) Conviction judgment (g, h)

* means reverse scored.

In this judgment task, we are up in what would now be considered appropriate levels of observations. All 70 participants rated all of the cases, which were all properly randomized/latin-squared. They do report, very briefly, on what they consider the effect of the situational variations, but the inferential statistics consists simply of “All results to be noted were significant at F(1, 56) > 4,40, p < .05.” They also note the means for only one of these results.

I won’t go into detail here about what they found. It could be interesting, but it is aggregated across 7 different types of primes, so that should add some systematic noisiness (and it also isn’t my main concern).

Then they go on to analyze the effects of priming on the 4 composite judgments. They divide this up in three sections: The first looks at the two types of aggressive priming – comparing to control. The second looks at priming of relationship, and the third on priming women as sex-objects.

Remember. There are 5 individuals in each cell, because they are looking at men and women differently. (and not reporting any standard deviations).

Let’s start with the aggressive acts priming, and judged responsibility of the victim

Victims responsibility for rape
Aggressive outcomes Aggressive acts Control
Defendant stranger
males 3,7 3,4 2,33
females 4,1 3,4 2,7
Defendant acquainntance
males 5,23 2,5 2,47
females 3,77 2,7 3,73
Aggressive outcomes Aggressive acts Control
Victim resisted
Males 2,93 3,2 1,37
females 3,97 2,33 2,3
Victim did not resist
Males 6 3 3,43
Females 3,9 3,77 4,13

I have circled the two ratings that stick out – both in the aggressive outcome priming, and both by the male group (5 individuals) when the defendant ins an acquaintance and the victim did not resist. Means here are above the half-way point (which they are not for the other). They also report that there is significant interactions between priming type, sex of subjects and both of those types (remember these are two different analyses).

Both F’s are actually the same: F(2,56) = 4.09, p < .05.

I’m wondering if that was a typo, though. I’m not sure what the likelihood is that the actual F value would be exactly the same.

But, with only 5 in each cell, who knows if this is due to one particular individual in that particular cell.

Conviction of defendant

When they report their analysis of conviction of the defendant, they actually separate the responses (ought to be convicted vs will be convicted), but collapse across gender. As the two measures are within subjets, this means that the cells are now 10 individuals.

Should be convicted
Aggressive outcomes Aggressive acts Control
Victim resists 9,3 9,9 9,3
Victim does not resist 8,6 9,6 9,5
Victim resists 9,4 9,9 8,8
Victim does not resist 7,5 9,1 8,3
Will be convicted
Aggressive outcomes Aggressive acts Control
Victim resists 5,4 4,2 4,5
Victim does not resist 6,4 2,6 3,9
Victim resists 5,5 3,5 4,7
Victim does not resist 3,1 3,6 2,7

Priming doesn’t do anything to the ratings whether the defendant should be convicted, regardless of whether it is a stranger or an acquaintance.

They report two interactions for this – one 3 way, and one 4 way.

priming x acquaintance x resistance F(2,56) = 5.81, p < .01
Priming x acquaintance x resistance x type of judgment F(2,56) = 4,37, p < .05.

(Yes, I have a hard time understanding what is going on too.)

Priming aggression seems to not have had any discernible effects on the other two types of judgments.

Reading through the discussion, they are appropriately mute about interpreting the results. The make a little flag for possibly this is consistent with a just world. Being primed with aggressive outcomes resulted in higher ratings that the defendant ought to be convicted. But, as I keep harping on, 10 participants in each cell.

They do an interpretation about the “is she partially responsible” results – where the five guys together judged females who were raped by an acquaintance and did not resist the rape were judged as more responsible. We have to recall that this involves 3 different scenarios, although each measure involves two. When the defendant is an acquaintance, there is one scenario where the woman resisted, and one where she didn’t resist. Likewise, when the defendant is a stranger, there is one scenario where she resisted, and one where she didn’t. One of these overlap both judgments.

I don’t know what to make of it. I don’t think anybody should, considering how few participants there are.

Intimacy priming

Here they are comparing the 10 people who were primed with the couples to the control group.

They report a whole bunch of effects. First, how priming may have altered the perception of harm to the victim

Priming control
General percpetion 8,2 7,2 F(1,56) = 8,21, p < .01
acquaintance 8 6,5
Stranger 8,3 7,8 F(1,56) = 4,51, p < .01

Means are overall higher on the scale for those that were primed.

Also seems to have increased the degree to which the participants though the victim told the truth.

priming control
truth 8,5 7,7

They separate this out in men and women, as well as the circumstances, and report a significant effect. Men seemed to move around a bit here, but they report to means, just an F statistic. F(1,56) = 5,67, p < .02- The claim is that for men who judged a victim that resisted a rape by an acquaintance (that is, one scenario only) did not show an elevated belief in truth compared to control. Got that?

So, in other words, the 5 men in the priming condition judged the degree of truth of one story more like the ones in the control group, but we have no idea by how much. Is it close to the 7,7 overall? Does it even make sense to parse it down like this.

Finally victims responsibility (the conviction judgments did not yield any differences).

Priming Control
Males 3,6 2,4
Females 2 3,2 F(1,56) = 6,88, P < .01
Priming Control
Resist 2,6 1,8
Not resist 3 3,8 f(1,56) = 4.20, P < .05

I think what I want to point out first, is that all of the values are on the low end. In the text, they suggest that males judged the victim more responsible than in the control, but the reverse was true for the females.

Then, in the other analysis, they pool across gender to look at the effect of resisting, and they report it weirdly (although technically I can see it being correct). The primed rated the responsibility of the resisting victim higher than for control. The reverse was the case for judging responsibility of the non-resisters. Yes, technically that is true, but non-resisters are overall judged more responsible (or less non-responsible). But, can you even say anything with so few points? (I know, I keep harping on this).

Women as sex objects.

I actually have no idea how they aggregated this. They start with the three sex primes (sex object and two different sexual arousal ones) and then the control, which they put together in a 2 x 2 design. And, from this they find out that the sexual arousal only have a couple of effects that are independent of the sexual object so, as they say “therefore, all results to be presented are independent of the effects of priming stimuli on sexual arousal).

Did they throw out the nudie primed? Or what did they do? I suspect this, as the df is 1, 56 in their analyses, so what I present here seems to use only those individuals that were primed with sex-objects (and the controls).

There were nothing on perception of crime.

However, there were effects on belief that the story was truthful, and on responsibility. 4-way interactions between type of prime (object, control) sex of perceiver, whether rapist was acquaintance or stranger, and whether the woman resisted or not.

So here, for each data point, you have 5 individuals making two judgments,

First, truthfulness

Truth of testimony
Defendant stranger . Defendant acquaintance
Resisted did not resist . Resisted did not resist
Sex object 7,6 6,2 . 7,3 6,7
control 8,7 7,8 . 8,4 5,9
Sex object 9,2 9,3 . 9,1 8,2
Control 8,1 7,4 . 7,2 7,8

One result I could possibly believe is that men and women rate the victim differently when primed with women as a sex-object in that the women tend to believe her more and men to believe her less than compared to control. Yes, things are moving around due to the acquaintance and resistance factors, but geez….

The inferential evidence is this 4-way interaction

priming x sex of subjext x acquaintance x resistance F(1,56) 0 7,45 P < .01.

They also found an effect – same type of 4 way interaction – for victim responsibility.

Vicim responsibility .
Defendant stranger . Defendant acquaintance
Resisted did not resist Resisted did not resist
sex obj prime 2,1 3,4 . 2,9 2,7
no sex obj prime 2,4 2,6 . 1,2 3,7
sex obj prime 2,1 2 . 2 3,9
no sex obj prime 2,5 3,6 . 3,1 4,2

Again, here is the 4-way statistic.

priming x sex of subjext x acquaintance x resistance F(1,56) = 9,31 p < .01

What does this say? Aggregate of 3 ratings, but for 2 vignettes, and still only 5 participants in each point.

Possibly the most striking is that women that were primed held the defendant very low on responsibility, except when it was an acquaintance and she did not resist. But, I am really not sure what the results from 5 women can say here.

The judgment of conviction yielded nothing. They reported an “uninterpretable interaction approaching significance”. P-value was .10. I think we’ll well satisfied calling that not significant.

conviction judging does nothing. They report an “uninterpretable interaction approaching significance” that is a p .10
I’d say, there is nothing.

I kind of feel exhausted after having gone through this. It is, in a way, such a complex design, with the 7 different primes, the 4 different variants of stories, and the four types of questions where some were aggregated and others not. And, with 5 people in each cell, and no standard deviations anywhere, what can you say? Other than this is interesting to follow up on to see if these effects hold. The paper has been cited 61 times, so it is up for a forward trace.

But, as I mentioned, I’m not so sure these are primes rather than emotion inductions, and they differ from the verbal primes earlier.

I’ve gone through and noted the results in such detail, as I want to try to pull something together on these, but mainly I feel depressed over so much work done with so few participants.

Wyer, Robert S., Bodenhausen, Galen V., Gorman, Theresa F. (1985). Cognitive mediators of reactions to rape. Journal of Personality and Social Psychology, 48, 324-338.

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