Starting up a new journal is an excellent occasion to reflect not only on the directions
into which the targeted field is currently heading but also on the remaining challenges
to be met and the shortcomings to be overcome. We will do so by putting research on
human cognition (the field that we as the new specialty editors of Frontiers in Cognition
represent) into a broader perspective and consider, among other things, the central
role this research plays, or at least has the potential to play, in connecting other
scientific areas and disciplines, as well as the social and infrastructural changes
that will be necessary to successfully tackle the challenges that remain on our way
to a truly integrative science of human cognition.
Exploiting Neuroscience
When one of us (Bernhard Hommel) first met John Gabrieli in the early 1990s on a very
interdisciplinary and (thus) very exciting meeting in Berlin, he was still skeptical
about the use of the back then increasingly popular neuroimaging methods for the functional
understanding of cognitive processes. “But however you think about it”, Gabrieli replied,
“you got to admit that the cognitive neurosciences have made cognitive psychology
so much more interesting”. And this is certainly true: neuroscientific observations
have sparked numerous cognitive theories, approaches, and discoveries, just think
of research on the binding problem and the notorious mirror neurons. Hence, the cognitive
neurosciences have strongly affected cognitive psychology but they also keep challenging
it and call for, so we argue, a reconsideration of how cognitive psychologists organize
and carry out their research, both technically and socially.
The great success of the cognitive neurosciences has already begun to shape the way
psychologists ask their research questions, at least if they make use of modern neuroscientific
techniques. Instead of asking the traditional question of how a particular cognitive
mechanism works, increasing numbers of studies are targeting the “neural correlates”
of these mechanisms or of the phenomenon under study. The outcome of such endeavors
is pointers to particular brain areas, as if this would tell us anything about how
the mechanism works or what algorithm it applies. It is certainly true that knowing
about the brain areas involved can provide a first step toward the investigation of
a mechanism, to be followed by the study of the interactions between such areas, and
the mapping of these interactions to particular cognitive algorithms. But these following
steps rarely take place and many psychologists are ready to accept the outcome of
the localization enterprise as an important observation in itself. Moreover, studies
that are linking a particular brain area to a particular cognitive process commonly
neglect the fact that the same area is also involved in numerous other, often unrelated
types of processes, and attempts to explain why that is are extremely rare as well.
Hence, the cognitive neurosciences do not only provide us with interesting new observations
but their success and attraction for psychological students also tends to push psychological
theorizing toward a reductionist perspective that “explains” cognitive mechanisms
by equating them with the brain structures that might be hosting them.
It will be crucial for the future of cognitive psychology and the cognitive sciences
in general how we deal with this challenge. One possibility is self-chosen splendid
isolation and, indeed, numerous cognitive psychologists are developing an often emotionally
colored antipathetic attitude against the neurosciences and their methods. Unfortunately,
this trend is facilitated by the fact that we are facing an increasing number of symposia
and conferences to choose from at times of financial crisis and tight travel budgets,
so that many of us are to decide whether to go to more “behavioral” or more “neuroscientific”
meetings. As a consequence, meetings with a traditionally strong behavioral emphasis
are losing sight of the cognitive neurosciences, while hard-core neuroscientific meetings
are no longer visited by many colleagues with a strong behavioral and theoretical
background.
The other alternative takes much more effort, money, and possibly even changes in
our social behavior. In principle, cognitive psychology has a lot to offer to the
cognitive neurosciences and many discoveries in this area would not have been possible
without the systematic development of tasks, paradigms, and analytical methods of
cognitive psychologists. However, the steadily growing neuroscientific machinery poses
very high demands in terms of technical, methodological, and analytical skills on
the individuals using it, and only few, if any single researcher could ever master
even the main techniques (say, EEG, fMRI, TMS, and PET) to a satisfying degree. Depending
on background, abilities, age, money, and teaching load, some individuals may be successful
working themselves into one of these techniques or perhaps two, but even this individual
achievement would be insufficient to reach what should be the ideal situation: to
flexibly pick the method that is suited best to address a particular research question.
Unfortunately, these enormous challenges tend to make the first alternative much more
attractive to quite a few. As a consequence, there is a real danger for a schism between
theoretically guided, functionally oriented (but mainly behavioral) cognitive psychology
on the one hand and an increasingly atheoretical, data-driven cognitive neuroscience
on the other. In our view, it will be crucial for the future success of cognitive
psychology to tackle this problem. No doubt, this will need aggressive efforts and,
presumably, substantial changes in social networking and the infrastructural requirements
for conducting and funding research. Given the increasing technical demands posed
by research techniques (even if these will be alleviated by software development to
some degree), flexibly constructed social networks of researchers with very different
backgrounds, expertise, and interests will be necessary – networks that will be tailored
to the research question at hand and, thus, likely to change from one question to
the other. To some degree, this is trivial to say and reflects what successful research
teams are practicing already. However, it is also true that the ways research is academically
organized and funded, and individual researchers are evaluated, often do not fit with
the requirements of this research style (e.g., by favoring competition over cooperation).
Moreover, exposing oneself to interdisciplinary research environments and networks
has very unfortunate psychological side effects: researchers who have worked very
hard to reach a particular level of expertise and self-confidence are now thrown back
to a beginner's level in several respects. This is difficult to bear without having
been trained to overcome the resulting frustrations, and to acquire an interdisciplinary
attitude and the necessary social skills from the start. This attitude and these skills
can only be acquired in respective interdisciplinary environments, BA and MA programs,
and research schools – which are still hard to find.
Apart from these more administrative and political challenges, cognitive psychologists
need to assume a more assertive, self-confident attitude with respect to the cognitive
neurosciences. Here the challenge will be to exploit neuroscientific knowledge and
techniques without giving up the very high theoretical standards that cognitive psychology
has developed and that it can be proud of. This will no doubt be difficult and require
the acquisition of at least basic knowledge about neuroimaging and related techniques,
but might become easier to manage though expansive social networking. In any case,
however, it will be important that cognitive psychologists expand their methodological
toolbox and raise their voice more distinctly in debates regarding the implications
of neuroscientific evidence for the functional understanding of cognitive mechanisms
and the brain processes underlying them.
Bridging Humanities and Natural Sciences
The recent decades have shifted the focus from the humanities to the natural sciences,
so that, for just one of many examples, the general public is now more interested
in the brain areas involved in moral decision-making than in the development, justification,
and societal implementation of the moral guidelines on which these decisions are being
based. This has put the academic organization of the humanities under substantial
economic pressure (as witnessed by the cancellation of many chairs and study programs
in that area) and sometimes triggered discussions about their societal function and
use. This is not the place for a discussion of that issue but we would like to emphasize
an interesting and, from the perspective of cognitive psychology, perhaps very fruitful
side effect of this process.
Being under pressure, many disciplines in the humanities are opening up in terms of
scope and approach to their topics. Given the noticeable success of the natural sciences,
it is not surprising that new ways are considered to bring humanities and natural
sciences into closer contact and to create overlap wherever possible – some countries
(e.g., Germany) have even launched dedicated funding programs to achieve that. This
provides unique opportunities for cognitive psychology, as it lies right at the interface
between the humanities and the natural sciences. Other disciplines and subdisciplines
have made ample use of this particular position already, and freely borrowed cognitive
concepts, models, and paradigms to become more empirical, experimental, and in part
biological. There are many examples, ranging from the development of the social cognition
approach in social psychology (cf., Hommel, 2006a) over the search for the neural
correlates of consciousness to neuroeconomics. Even though the resulting interdisciplinary
endeavors are exciting and highly promising, cognitive psychologists could have played
a more active and proactive role in these and other developments, and could do so
in the future. Many more bridges are needed indeed, just think of the cognitive implications
of religion, literature, ethics, and more. It seems important to us that cognitive
psychologists become more expansive with respect to the borders of their (sub)discipline
and make more active use of the fact that they are interfacing with almost any area
covered by the humanities. Their experimental expertise and often broad theoretical
knowledge seems much more precious and have more potential for bridging other disciplines
than many of us are aware of. Fulfilling his potential is likely to strongly increase
the breadth and validity of our theories and models and provide interesting avenues
for testing them.
Investigating Processes, not Paradigms
Experimental paradigms are at the core of our trade. It is to a large extent paradigms
that have made cognitive psychology so successful – well-understood tasks that have
been carefully developed and systematically extended. This knowledge about paradigms
and their theoretical implications is what neighboring areas and disciplines are after,
what has been adopted from the clinical sciences in the search for process-pure measures
of particular cognitive impairments and by the social sciences to make abstract theoretical
concepts empirically fruitful. Paradigms are also one of the main contributions of
cognitive psychology to the emerging cognitive sciences, and most of the important
contributions to the functional understanding of human cognition from neuroimaging
research would have been impossible without the employment of well-developed cognitive
paradigms.
And yet, cognitive psychology tends to overdo with respect to the enthusiasm for paradigms,
which often stands in the way of theoretical progress in a wider sense. We devote
whole research careers to one single experimental task or effect that often has very
little if any ecological validity. There are obvious advantages of this strategy.
Becoming truly proficient in applying and making optimal use of a given paradigm takes
a lot of time and effort, which should not be wasted by jumping from one paradigm
to another. Moreover, sticking to one paradigm or effect makes it much easier to develop
a unique research profile and acquire a solid scientific standing, and it is often
tasks and effects that bring together researchers in special issues and lively scientific
symposia. And yet, the resulting over-emphasis on paradigms and effects has a number
of serious consequences that we need to overcome on our way to a truly integrated
approach to human cognition.
Paradigm-driven research necessarily aims at understanding whatever effects the paradigm
produces. This has many disadvantages. For one, a given paradigm might be an excellent,
close to process pure measure of one cognitive process or mechanism but it is likely
to be a lousy measure of numerous other processes or mechanisms. If so, why would
one even try to understand the role of the latter in this particular task rather than
using another, better-suited task to assess those other processes? And yet, given
our fixation on tasks and effects, many models we develop are trying to capture all
the processes involved therein and, indeed, we as reviewers and editors would insist
that authors include all these processes in their model. Would it not be better to
follow the exact opposite strategy? That is, to try to capture one given process across
as many paradigms and effects as possible, thereby explicitly ignoring the fact that
these paradigms and effects are not equivalent with respect to a number of other processes.
And to try to evaluate our favorite paradigms and effects much more in terms of how
well they capture one given process. Of course, this strategy would by no means be
foolproof and likely to generate a new kind of “specialist” that is narrow-minded
not in terms of tasks but in terms of processes. And yet, it seems essential to us
that we at least try to reduce our present fixation on paradigms and effects. One
of several benefits of such a strategy is that we could be much more certain that
our research topic has external validity. Indeed, it is much easier to explain how
important it is to investigate, say, the human will or decision-making under uncertainty
than to try relating the task-switching paradigm or the Stroop effect to the real
world.
The lesson to be learned, we think, is to reconsider our paradigms and effects as
what they are: means to an end but not ends by themselves. The true goal of an integrated
cognitive science is the understanding and modeling of cognitive mechanisms (measured
as purely as possible) and the understanding of psychological phenomena, that ideally
are either taken from, or are at least modeled after behavior that can be found outside
of our labs.
Integrating Modeling and Experimentation
A discipline's level of maturity is often measured by the degree to which the phenomena
it addresses can be captured by mathematical models. Even though one can argue whether
this is a particularly important or even the crucial criterion, it would certainly
advance our discipline if empirical research, theoretical reasoning, and computational
modeling would integrate better. And yet, it seems fair to say that computational
models do not play a particularly dominant role in most areas of cognitive psychology.
How can that be improved?
There are likely to be numerous answers, and many will have to do with the types of
models, the ways they are tested, and how they are communicated, but there is one
answer that we would like to emphasize. As developed in some more detail elsewhere
(Hommel, 2006b), computational models are much more successful and influential if
they come with new and unexpected empirical data, that is, if model construction and
model testing go hand in hand and if the data do not only serve to justify the model.
Instead, models that merely redescribe old or replicated data from highly particular
paradigms commonly fail to impress experimental researchers sufficiently to adopt
and work with them.
However, being a good modeler and a good, broadly experienced experimentalist at the
same time is quite a challenge that most of us are not up to, a problem that is similar
to our cognitive and time restrictions with regard to the acquisition of neuroscientific
methods, as discussed above. This is why we consider it essential for computational
modelers to team up with experimentalists, probably even from diverse areas, to get
the intended cycle from modeling to testing to model modification to testing etc.
really going and for making it really interesting. What is also likely to help is
to provide interested colleagues with the software tools necessary to generate model
predictions and to test the model, as in the ACT-R community (act-r.psy.cmu.edu).
Only then, we think, would it be possible to achieve what most models promise but
actually fail to achieve: the generation of really new and relevant, but unexpected
and counterintuitive predictions that can be demonstrated to stand empirical test,
ideally across different tasks and paradigms. Only if that level could be reached
at a broader scale, computational models would impact our theorizing to a degree that
goes beyond mere existence proofs or the demonstration of computational principles
(which of course will also remain important).
Creating Suitable Research Contexts
Progress in science is often associated with competition, and competition is undeniably
a particularly strong motivating factor. And yet, there are reasons to believe that
overemphasizing this factor may seriously limit progress in science. Performing research
is increasingly complex and complicated, especially if one is trying to go beyond
single effects and paradigms but to integrate multiple ideas and concepts. To deal
with this complexity, we have argued, will often require teaming up with other colleagues,
sometimes with different types of expertise and background, and even from different
disciplines. To do so effectively presupposes solid social skills. Even though that
might be trivial to say we don't think it is. Many of us grew up in academic systems
that comprised of surprisingly many, commonly male “specialists” with surprisingly
few skills and motivation to communicate and to spark enthusiasm for their research
topics in others. This attitude may have sufficed for a scientific career in the past,
but we suspect that decidedly stronger emphasis on skills in communication and social
networking will be necessary to advance our discipline in the future.
Fortunately, there are at least two factors our discipline has benefited from in this
respect. First, the development and widespread availability of software packages for
the easy-to-access programming of psychological experiments has opened the door for
increasing amounts of non-nerdy, socially proficient cognitive students and increased
the ratio of female to male students in cognitive psychology. Second, the increasing
amount of interaction between cognitive psychology and the cognitive neurosciences
has attracted many students – many more students than traditional cognitive psychology
and students with much more diverse backgrounds in scientific perspective. This greater
diversity is likely to make discussions livelier and increase our tolerance and appreciation
for seemingly weird out-of-the-box ideas.
Fully exploiting this interdisciplinary attitude and the creative potential it provides
requires strong efforts. For one, we need to counteract the centrifugal forces that
are driving behavioral cognitive psychology and the cognitive neurosciences apart.
Among other things, this means that we need to succeed in keeping or creating interesting
scientific conferences or other types of meetings that are attractive for and thus
visited by both behavioral and neuroscientific researchers. It also means that more
interdisciplinary study programs and graduate schools will need to be launched, including
programs that integrate psychological subdisciplines. But we also need to reconsider
the reward systems handled by universities and funding agencies to see whether more
could be done to facilitate collaboration and flexible networking.
Games Without Frontiers
To conclude, the recent developments in and around our field have the potential to
bring us much closer to a well-integrated science of human cognition. Fulfilling this
potential, so we have argued, will be much easier if we are strongly expanding or
even doing away with at least four types of frontiers:
Methodological frontiers, by including neuroscientific techniques and machinery in
our experimental toolbox – not to trade our functional theories for neuroanatomical
or neurophysiological hypotheses but to have more instruments at our disposal to test
them.
Paradigmatic frontiers, by tracing interesting cognitive mechanisms across various
experimental paradigms and by making models focusing on these mechanisms but not on
the paradigms assessing them.
Disciplinary frontiers, by getting in closer touch to neighboring psychological subdisciplines
and other disciplines, so to make productive use of our unique position as an interface
between the humanities and the natural sciences.
Personal frontiers, by engaging more in social networking and creating flexible, quickly
changing research groups that cover a broad range of expertise and theoretical background.
Sure enough, tackling these challenges requires activities that go way beyond the
mission of a scientific journal, even if Frontiers’ interactive editorial style does
provide new opportunities in this context. Nevertheless, we will do what we can in
order to facilitate these processes, be it in the form of the editorial policy, which
will emphasize innovation and courage, interdisciplinarity and theoretical breadth,
or in the form of special issues that, in terms of topic or style, will help to turn
our science from Newell's (1973) game of 20 questions with nature that we can't win
into a cumulative science that provides us with an increasingly comprehensive understanding
of human cognition and action.
Conflict of Interest Statement
The authors declare that the research was conducted in the absence of any commercial
or financial relationships that could be construed as a potential conflict of interest.