I’ve just discovered a stinging but insightful critique of modern scientific psychology from cognitive scientist Paul Rozin, who accuses the field of being blinded by fancy experimental methods while devaluing the importance of capturing new and interesting phenomena.
Rozin makes a striking comparison to biology, where curiosity-driven studies that simply try and describe a new species, effect or behaviour are widely published, alongside experimental studies that aim to test a specific idea.
In contrast, psychology has become a largely lab-based science where your career is made by running countless variations on an established effect to the point where it is now virtually impossible to publish a descriptive account or case study in psychology or psychiatry.
Consequently, the most lauded studies are usually statistically robust, very well controlled, and largely removed from a context which makes them directly relevant to real world issues and problems.
Rosin outlines seven types of descriptive studies which he thinks are under-valued and notes their importance in the scientific understanding human thought and behaviour:
‘‘Here’s what happens in the world.’’ This paper consists of raw description, carefully documented, and motivated by what I will call ‘‘informed curiosity’’ (Rozin, 2001). Ethologists do a lot of this, as did Erving Goffman and Darwin. Much of molecular biology takes this form.
‘‘Here is a functional relation between two variables.’’ [Rozin argues that lots of interesting effects occur due to unusual relationships between two things - such as the U-shaped relationship between arousal and performance - and we wouldn't always see by splitting things up into distinct groups. He argues that reporting these interesting but unexplained relationships is important but neglected]
‘‘Here’s something interesting that no one has noticed, and it is not easily susceptible to explanation by the principles available to us.’’ [Exceptions to established rules, even if described just to be highlighted as interesting]
‘‘Here’s something we haven’t studied, but it looks like it can be subsumed under something we already know.’’ [New things that are probably explained by existing theories - even when the theories were not intended to apply to this new domain. In other words, establishing an analogy between one problem and another]
‘‘Hey, someone did this really interesting study decades ago, and no one seems to have noticed it.’’ This paper would call readers’ attention to something already in the literature that is important and unknown or ignored.
‘‘Everyone assumes Effect X, but is X robust and generalizable?’’ [Taking an established effect and seeing how well it applies to other situations. If it doesn't replicate very well outside the lab, this tell us something interesting about how fragile and context-sensitive the effect is]
‘‘This is a messy, criticizable experiment reporting something new and interesting.’’ This type of study usually involves an interesting idea, with some admittedly far from conclusive evidence for it. The famous Schachter and Singer (1962) attribution study is an example.
It’s worth reading the piece in full as Rozin gives lots of great examples where new phenomena clearly contribute to our understanding of the mind but are very difficult to publish in the psychology literature, despite similar examples (tool using crows, coconut carrying octopi, spear throwing chimpanzees) making headlines in top biology journals.
I also recommend a commentary on the piece from Cognition and Culture who nail some of the take-home points.