- Jensen, A. R. (1982). “The chronometry of intelligence”. In R. J. Sternberg (Ed.), Advances In The Psychology of Human Intelligence, Volume 1. Hillsdale, NJ: Erlbaum. Pp. 255-310.
A clearly formulated hypothesis, a well-designed experiment, and a generalizable conclusion of theoretical or practical importance are all products of much analysis and cogitation. But what initiates such analysis and cogitation in the first place? The answer calls for autobiographical retrospection, and so here, of course, I can only speak for myself. By way of introduction, it might be useful to try to discern what kinds of things get me going as an investigator. Some of these general reaction tendencies that seem to be recurrent throughout my career in psychological research also quite likely account for my current fascination with the connection between reaction time and intelligence, which is mainly what this chapter is about. In general, five things seem to arouse my research impulse. In no particular order of importance, they are:
1. In reading the psychological literature, if I repeatedly encounter what seems to be a popular or commonly accepted belief, generalization, or theory, which for some reason looks questionable to me or cries out to be debunked, I am apt to go to work on it (provided that its technical aspects as a research problem fall more or less within what I perceive as my sphere of competence or at least a competence that I think I could acquire without an unfeasible expenditure of time and effort). Certain topics in psychology are notably rich in this vein, and the literature on intelligence may well be the richest. At least it is difficult for me to think of any other major topic in psychology, as treated in general textbooks, that presents what seem to me more potentially debunkable popular beliefs than the topic of intelligence. Hence, the fact that my investigative tendency is aroused by anything I perceive (for whatever reason) as an unfounded belief is probably a factor in my attraction to intelligence as a research topic. It offers us many unfounded but popular beliefs, ad some of there apparently refuse to die even in the face of decisively contradictory evidence. In such a case, one, research efforts must simply move on to more genuinely unsealed questions, in the realization that there will always be some small carp of critics who will forever cling to the belief that the earth is flat.
2. This is almost a corollary of the first point: I am around by findings or phenomena that would seen) to contradict a common belief or explanation we had regarded as too obvious to question. The contradictory fact can be a springboard for investigations that may support a better scientific explanation. Any seemingly contradictory phenomenon must, of course. also be critically examined to rule out possible artifacts and to insure its replicability. lilt stands up, we have a new lead for investigate.
3. Another quality of a phenomena that enhances its interest for me is its being counterintuitive, surprising, or inexplicable in terms of my established principles. Once such a a phenomenon attracts my attention. Of course. the first job is to establish its reality and make sure it is not just a fluke—an experimental or statistical artifact. The researcher, nightmare, it seems to me, is the risk of squandering resources on the investigation of some apparently interesting phenomenon that rums out to be merely some kind of artifact. Almost as bad but even more likely is the risk that the phenomenon, although real, is so narrowly specific to a particular laboratory procedure, measuring device, or sample so unrepresentative of the general population that it is scientifically and theoretically trivial. I seek evidence that a phenomenon is fairly “robust” before making any strong research commitment, recognizing, however, that what at first may appear to be an ephemeral or unreliable phenomenon might be turned into a robust phenomenon by improved measurements, procedures, or analytic techniques.
4. A psychological phenomenon that can be measured reliably or has potentially quantifiable properties is thereby a more attractive subject for scientific study. It is not necessarily a more important phenomenon than one that does not lend itself so readily to quantification; but the study of measurable phenomena, I believe, nuns surely and quickly yields objective knowledge. Similarly, I am more closely drawn to a phenomenon when it displays what appears to be a simple, regular, or “lawful” relationship to some other variable or when it shows invariance over a wide range of conditions. (The well-known serial-position effect in serial rote learning is a good example of a highly invariant phenomenon.) Invariance usually signifies that the causal mechanisms are robust, general, and probably more biologically wired in rather than experiential. A phenomenon that shows essentially the same lawfulness and in in different species of animals, including humans, is thereby made even more attractive; this interspecies continuity of the phenomenon suggests that it is a product of biological evolution, which I find much more interesting than my predominantly cultural phenomenon. This preference for biological rather than cultural phenomena is merely a personal idiosyncracy to which I attach no general importance.
5. Psychology has many unsolved problems and unexplained phenomena that have been around for a very long time. There are basic, recurring questions. Unsuccessful early attempts to understand a phenomenon may lead to its abandonment as a topic of inquiry, but the basic questions that prompted investigation in the first place remain unanswered. On the other hand, there are short-lived fads in psychological research that distract from the enduring basic issues. Acquaintance with the history of the major topics of psychology affords one a perspective and context for appreciating a phenomenon. Over the years, research questions with little or no past history have seemed less and less interesting to me. Too many PhD dissertations deal with questions that have no history and, most likely, no future. A science cannot develop by a continual succession of unanswered or half-answered questions about an ever increasing multitude of phenomena. Hence, I am most attracted to the still unresolved questions in those topics that are strongly rooted in the history of our field. The nature of intelligence and the measurement of individual differences in intelligence are such topics. There are many phenomena in this domain that evince all the features of attractiveness for investigation that I have indicated. In addition, the topic of intelligence is commonly regarded as having great relevance to education and, indeed, to society and the quality of life. This is a bonus, but not the intrinsic attraction, from the standpoint of research.