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COMPUTATIONAL NEUROSCIENCE
REVIEW ARTICLE
published: 03 April 2012
doi: 10.3389/fncom.2012.00020
Letting the daylight in: reviewing the reviewers and other
ways to maximize transparency in science
Jelte M. Wicherts*, Rogier A. Kievit, Marjan Bakker and Denny Borsboom
Department of Psychology, University of Amsterdam, Amsterdam, Netherlands
Edited by:
Nikolaus Kriegeskorte, Medical
Research Council Cognition and Brain
Sciences Unit, UK
Reviewed by:
Nikolaus Kriegeskorte, Medical
Research Council Cognition and
Brain Sciences Unit, UK
TalYarkoni, University of Colorado at
Boulder, USA
Jasper Jacobus FranciscusVan Den
Bosch, Goethe-Universität Frankfurt
am Main, Germany
*Correspondence:
Jelte M. Wicherts, Department of
Psychology, University of Amsterdam,
Weesperplein 4, 1018 XA Amsterdam,
Netherlands. e-mail:
j.m.wicherts@uva.nl
With the emergence of online publishing, opportunities to maximize transparency of scien-
tific research have grown considerably. However, these possibilities are still only marginally
used. We argue for the implementation of (1) peer-reviewed peer review, (2) transparent
editorial hierarchies, and (3) online data publication. First, peer-reviewed peer review entails
a community-wide review system in which reviews are published online and rated by peers.
This ensures accountability of reviewers, thereby increasing academic quality of reviews.
Second, reviewers who write many highly regarded reviews may move to higher editorial
positions. Third, online publication of data ensures the possibility of independent verifi-
cation of inferential claims in published papers. This counters statistical errors and overly
positive reporting of statistical results. We illustrate the benefits of these strategies by
discussing an example in which the classical publication system has gone awry, namely
controversial IQ research. We argue that this case would have likely been avoided using
more transparent publication practices. We argue that the proposed system leads to better
reviews, meritocratic editorial hierarchies, and a higher degree of replicability of statistical
analyses.
Keywords: peer review, scientific policy, data sharing, scientific integrity
INTRODUCTION
It has been argued, most famously by Karl Popper, that the open-
ness of the scientific system is what makes it such a success-
ful epistemic project, compared to other methods of gathering
knowledge. The open character of scientific arguments allows
the error-checking mechanisms of science, such as replication
research, to work. In turn, this eradicates incorrect claims effi-
ciently so that, in science, falsehoods tend to die young. It seems
safe to say that openness is so central to the value system of the
scientific community, that occasions where we choose not to pur-
sue an open system should be as rare as possible. In principle, such
occasions should only arise when there are overriding concerns of
a higher moral status, such as concerns with regard to the privacy
of patients participating in research and similar factors. From this
point of view, it is remarkable that one of the most important parts
of the scientific process, peer review, takes place behind closed
curtains.
This hidden part of science has some undesirable consequences.
For instance, it means that essential parts of the scientific discus-
sion are invisible to the general audience. In addition, the peer
review system is liable to manipulation by reviewers and editors.
For example, editors can influence the system by selecting subsets
of reviewers who, given their track record, are practically certain
to provide positive or negative reviews. Reviewers can manip-
ulate the system by “bombing” papers; especially top journals
tend to publish papers only if all reviewers judge a paper pos-
itively, so that a single dissenting vote can nip a submission in
the bud.
These and other problems with the peer review system have
been widely debated (e.g., Godlee et al., 1998;Smith, 2006;Benos
et al., 2007), yet the system has been subject to little change.
One reason may be that the peer review system is a case where
we are both “us” and “them”: practicing scientists both bear the
adverse consequences of its problems and are responsible for its
faults. Moreover, the editorial secrecy itself precludes the reviewing
scandals that occur from becoming public and creating sufficient
outrage to provide adequate momentum for change. A final prob-
lem is that scientists have grown accustomed to the system; so even
though many see it as a wicked labyrinth, at least it is one in which
they know how to navigate.
So general are the problems of the peer review system and so
(seemingly) hard to remedy that some have likened peer review
to democracy, in being “a bad system, but the best we have” (e.g.,
Moxham and Anderson, 1992;Van Raan, 1996). However, as is
the case for democracy, the fact that peer review is both inherently
imperfect (as is any human endeavor) and likely to remain at the
heart of scientific publishing does not imply it cannot be improved.
In fact, we will suggest a simple improvement that may go a long
way toward solving the current problems; namely, to open up
the peer review system itself. In this context, we will propose a
new system that is based on three pillars: (1) the publication of
reviews, (2) the public assessment of the quality of those reviews,
and (3) mandatory publication of data together with a published
paper.
We argue that this system has several immediate payoffs. First,
it is likely to improve the overall quality of reviews, especially by
allowing the scientific community to discount reviews that are
clearly biased or which provide too little argumentation. Second,
the system remedies the lack of direct acknowledgment of the
work that goes into reviewing, which is a significant drawback
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of the current system, and one of the primary reasons that it is
becoming harder for editors to find reviewers. Third, making the
system public opens up further insights into the structure of the
scientific literature. Compared to current practices in scientific
publishing, the proposed system is based more strongly on the
key characteristics of the scientific enterprise: honesty, openness,
and rigor. As we illustrate in the next sections, current practice of
reviewing and dealing with research data do not always do well in
these regards.
We will delve more deeply into a specific example, but first
note that cases of controversial peer review decisions exist in
most if not all fields of science. In the last 2 years alone, there
have been several examples of high-profile research where peer
review has, seemingly, not functioned well. For instance, Sci-
ence accepted for publication a paper by Wolfe-Simon et al. (2011)
that claimed to have found evidence for arsenic-based life forms,
thereby overturning basic assumptions in (molecular) biology.
However, colleagues heavily criticized the paper almost instantly,
with several very critical commentaries appearing (e.g., Redfield,
2010). The paper was eventually published along with eight highly
critical comments and an editorial note (Alberts, 2011). Simi-
larly, Nature published a paper by influential theorists that argued
that kin selection is an outdated concept (Nowak et al., 2010). The
paper immediately sparked controversy, and was followed in a later
volume of the same journal by several critical replies, one of which
had 136 authors (Abbott et al., 2011). Arguably the most damag-
ing case of peer review gone awry was an article by Wakefield et al.
(1998) in The Lancet, allegedly demonstrating a link between vac-
cines and autism. The article, based on 12 patients, was ultimately
retracted, the lead author’s medical license revoked, and the claims
stricken from the academic record after an intensive investigation
revealed several cases of fraud. Although fraud cannot always be
detected by peer review, inspection revealed several grave errors
such as improper measures, lack of disclosure of conflicting inter-
ests, improper blinding procedures and a lack of controls that
could have been picked up by peer review (for an overview, see
Godlee et al., 2011).
The breadth of the critique in these controversial cases, gener-
ally representing the majority of scientists in the respective fields,
lends credence to the hypothesis that the reviewing process was, at
the very least, not as rigorous as is desirable. Several controversial
examples make clear that poorly reviewed papers, given the cur-
rent dearth of opportunity to correct such errors, can adversely
affect progress of science and in some cases (i.e., the Wakefield
paper) be damaging to the public. As science’s main method of
quality control, it is clear that all parties would benefit from a
peer review system that diminishes the chances of such errors
occurring.
We will illustrate the nature of the problems with current peer
review and our proposed solution on the basis of a case that, in
our view, represents the problems with the current system most
clearly. As the variety of examples above show, this particular case
is not of great importance. We chose it because (a) we are familiar
with its content and the context in which it appeared, (b) we feel
confident in judging the merits of the paper and the problems that
should have been picked up by reviewers, and (c) its problems
could have beensolvedinamoreopensystemofpeerreview.Ifwe
succeed in our goal, readers will be able to substitute our particular
case study with a relevant example from their field.
A CASE STUDY
THE CASE
On the basis of his theory of the evolution of intelligence
(Kanazawa, 2004), Kanazawa (2008) proposed that, during their
evolutionary travels away from the relatively stable and hence pre-
dictable environment of evolutionary adaptedness (EEA; i.e., the
African savanna of the late Pleistocene), the ancestors of Eurasians
encountered evolutionarily novel environments that selected for
higher intelligence. Therefore, Kanazawa (2008) predicted higher
average IQ scores in countries located farther away from the EEA.
Kanazawa (2008) tested this hypothesis against data gathered by
Lynn andVanhanen (2006), who estimated so-called “national IQ-
scores,” i.e., the average IQ of the inhabitants of nations in terms of
western norms. Kanazawa (2008) found a significant negative cor-
relation between countries’ national IQs and their distance from
three geographic locations in and around sub-Saharan Africa.
WHAT SHOULD HAVE HAPPENED?
We point to a number of indisputable issues that should have
precluded publication of the paper as constituted at the time of
review. First, Kanazawa’s (2008) computations of geographic dis-
tance used Pythagoras’ theorem and so the paper assumed that
the earth is flat (Gelade, 2008). Second, these computations imply
that ancestors of indigenous populations of, say, South America
traveled direct routes across the Atlantic rather than via Eurasia
and the Bering Strait. This assumption contradicts the received
view on evolutionary population genetics and the main theme of
the book (Oppenheimer, 2004) that was cited by Kanazawa (2008)
in support of the Out-of-Africa theory. Third, the study is based
on the assumption that the IQ of current-day Australians, North
Americans, and South Americans is representative of that of the
genetically unrelated indigenous populations that inhabited these
continents 10,000 years ago (Wicherts et al., 2010b). In related
work by others who share Kanazawa’s (2008) views on the nature
of race differences in IQ, the latter issue was dealt with by excluding
countries with predominantly non-indigenous populations (Te m -
pler and Arikawa, 2006). Thus, although Wicherts et al. (2010b)
raised additional issues that may the topic of debate (see below),
these three problems are beyond dispute.
WHAT DID HAPPEN?
The paper was accepted for publication in the journal Intelligence
3 weeks after first submission. Intelligence is the foremost jour-
nal on human intelligence and has an impact factor of 3.21.The
editor normally asks three experts to review original and revised
submissions. Editorial decisions concerning rejection, acceptance,
or revision are based on the majority vote, although one critical
reviewer may be sufficient to let authors revise the manuscript
several times. The average time lag for research papers that were
published in 2008 was 228 days (median =211) and so the
acceptance of Kanazawa’s (2008) paper was rapid.
1One of us (Jelte M. Wicherts) is proud to be a member of its editorial board
although he hastens to add he was not one of Kanazawa’s (2008) reviewers.
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AFTERMATH
Two of the authors of the present paper were involved in the prepa-
ration of a criticism that pointed out some of the undisputable
errors in the paper, and also raised doubts with respect to the
evidential relevance of present day correlations for evolutionary
theories of the kind Kanazawa (2004,2008) proposed. After we
had submitted the critique to Intelligence we received the following
feedback from two anonymous reviewers. According to Reviewer 1
of our critique: “The history of science tells us that a strong theory
that explains numerous phenomena, like that of [...] Kanazawa, is
generally overturned by a better theory, rather than by the wholly
negative and nitpicking criticisms of the present paper.”Reviewer
2 of our comment wrote that: “Any explanation of IQ biodiversity
must address itself to the totality of the evidence and not depend
on highlighting small scale criticisms.” A third reviewer was more
positive, but the use of the majority vote resulted in rejection of
our criticism.
ANALYSIS OF THE CASE
Because we have no access to the reviews of Kanazawa’s (2008)
paper, we can only speculate on how the review process unfolded.
Having a clear bearing on the controversial topic of race differences
in IQ one would expect Kanazawa’s (2008) study to be met with
scrutiny by reviewers (Hunt and Carlson, 2007). This does not
appear to have happened. It is possible that the reviewers were
busy and each hoped for other reviewers to scrutinize the paper
in detail. In psychology,such processes have been studied in detail
under the headers of social loafing and diffusion of responsibility
(Darley and Latané, 1968), and are known to negatively influence
the quality of task performance.
Another possibility is that Kanazawa’s (2008) reviewers per-
formed poorly because they felt the need to counter the unpopular-
ity of views associated with genetic hypotheses of group differences
in IQ. Our view is that the current state of knowledge of the neuro-
physiological, evolutionary, genetic, cognitive, and psychometric
nature of individual differences in IQ is insufficient to arrive at
clear answers about the nature of group differences in IQ. How-
ever, the topic is certainly a legitimate scientific endeavor, and we
take no issue with researchers who propose hypotheses that fea-
ture racial differences in genetic endowment for intelligence (as
long as these hypotheses are testable and consistent). Yet many
researchers consider those who hypothesize on such genetic dif-
ferences to be racist and not even entitled to publish their work
in a peer-reviewed journal. Dishonest reviews in this controversial
area are well documented on both sides of the debate (Hunt, 1999;
Gottfredson, 2010). Dishonest reviews are the atrocities in the
“wars of science” and their existence only sparks more dishonesty,
which does not really contribute to knowledge.
AN ALTERNATIVE HISTORY
The fate of our critique of Kanazawa’s (2008) paper (and of two
similar papers by others) is interesting, because it provides an alter-
native history by itself. The reason is that the journal Personality
and Individual Differences eventually published the paper, along
with a polite and open debate (Lynn, 2010;Rushton, 2010;Tem -
pler, 2010;Wicherts et al., 2010a,b) on the relevance of some of the
additional issues we had raised earlier (unfortunately Kanazawa
himself declined the invitation to comment). The exchange clearly
shows that opinions on Kanazawa’s (2008) findings differ. The dif-
ferences in tone and content between the negative reviews of our
earlier manuscript and the open exchange in the other journal
are striking. One likely reason is that the reviews were writ-
ten anonymously and in a system that is not sufficiently open
to scrutiny. Although editors play a moderating role in debates
between authors and reviewers (next to their main role in decid-
ing on publication), they are unlikely to disagree with reviewers
for several reasons. First, editors need to be able to fall back on the
reviewers’ assessments to make unpopular rejection decisions and
to be able to counter later criticisms of published work. Second,
the editors rely on these reviewers in the future to do more pro
bono reviewing. Similarly, it is impolite to ask busy scientists to
invest time to review a paper and subsequently downplay or ignore
the importance of their work. Writing peer reviews takes up valu-
able time but these writings are normally not published and so the
editors are unlikely to complain when the reviews are done hastily.
CONCLUSION
In our view the case study illustrates a major problem with current
publication practices. Namely that the selection of reviewers, edi-
torial decision making, and the treatment of critiques are all done
behind closed curtains and that reviewers are often anonymous,
and so hardly accountable for their writings. The general audience
may thus read the paper in Intelligence without recognizing that it
is based on several faulty assumptions, and without ever knowing
that a criticism of the paper was rejected. Nor can the audience
ever retrace the arguments that led to the acceptance of Kanazawa’s
(2008) paper and rejection of the criticism voiced against it. The
general audience has no way of finding out how three reviewers
who are knowledgeable in their field had missed the publication
of obvious errors they were supposed to help avoid and how two
reviewers later prevented an exposition of these errors in the same
outlet. Peer reviews represent some of the most valuable and inter-
esting reflections on other peoples’ work and putting them away
in a closed system is often a waste of energy and information. Also,
the payoffs for reviewers to write high quality reviews are currently
minor.
Let us then consider a new system, based on the premise of
complete openness, discuss its possible merits and drawbacks, and
finally examine a brief counterfactual history of the case study to
illustrate how the peer reviewing system might work, and why this
is a benefit for all concerned.
THE BROAD DAYLIGHT PUBLICATION MODEL
Fortunately, there is an effective cure for all of these diseases: day-
light. The Broad Daylight Publication Model (BDPM) that we
advance here incorporates openness at three levels: transparency
of the editorial process, accountability of reviewers, and openness
with respect to data. The BDPM is illustrated in Figure 1.
THE EDITORIAL PROCESS
The BDPM first involves a soft change to current policy. It merely
requires giving up secrecy and opening up the scientific system as
it exists now to public scrutiny. This means that scientific jour-
nals should disclose all information by default, unless there are
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FIGURE 1 |Illustration of the Broad Daylight Publication Manual.
overriding concerns to preclude such practice. So journals should
minimally engage in the following steps:
1. Disclose submissions: All submissions should eventually be pub-
lished online, so that the public may see not only which papers
were accepted, but also which papers were rejected. Rejected
papers are published without the main text (to enable authors
to seek other options), but with titles, authors, and abstracts,
and full reviews.
2. Disclose reviews: All reviews of all papers, whether accepted or
rejected, should eventually be published online, along with all
editorial letters.
We think that the current secrecy regarding who submitted
what where and how the submission was evaluated is outdated.
Only rarely do authors have insurmountable reasons to remain
secret about their submitted work. Almost certainly, reviewers
would write their reviews differently if they knew that these reviews
will become public.
ACCOUNTABILITY OF REVIEWERS
A second step in promoting openness involves making reviewers
accountable for their actions and to give them due credit for their
hard reviewing work. This could be done by adding the following
elements:
3. Review the reviewers: All reviews of all papers can be rated by
the journal’s readership. Reviews are always signed.
4. Open up the editorial hierarchy: Reviewers who review often
and whose reviews get high ratings can ascend in the editorial
hierarchy.
We propose a system where every review can itself be rated by
the scientific community. We suggest some criterion that warrants
the ability to be able to rate reviews, such as “having at least one
published article in this journal.” Any person who fulfills this cri-
terion may then rate a review on a Likert scale that runs from, say,
1 to 5. These ratings represent the perceived quality, depth, exper-
tise of the review, and the extent to which it contributes to quality
control. After publishing the reviews alongside the manuscript,
these reviews will accumulate ratings. After some time, a review
may have scored an average of, say “4.2,” suggesting fairly high
average review quality. Similarly, a reviewer will start accruing
ratings and published reviews. We could think of some basic
metric (e.g., for instance an “R-index,” that summarizes “num-
ber of reviews written” times“average quality rating”) that reflects
both the amount and average quality of reviews someone has con-
ducted, which would be a relevant part of the resume of a working
scientist. This would allow the work that goes into reviewing to be
acknowledged more explicitly, and for funding agencies to judge
someone’s“presence”in the scientific community more accurately.
In this way, reviewing well will finally start to pay off for the
reviewers themselves. By writing many reviews that are published
alongside manuscripts, researchers may build their reputation in
the community. A good reputation as a reviewer should form the
basis for appointments in the editorial hierarchy (reviewing board,
editorial board, associate editors, and main editor).
Another important effect of opening up the review system
is that structure of the reviewing process can be analyzed. For
instance, it would become possible to examine patterns of friendly
reviewing and nepotism. In addition, reviewers can be statisti-
cally analyzed. It will be clear to everyone living in the scientific
machine that reviewers differ in how difficult it is to pass them.
Such differences can be analyzed and, in the future, it may even
be possible to account for them. In fact, the availability of such
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information enables a wealth of studies that contribute to sci-
entific self-reflection and improve the scientific practice, thereby
advancing knowledge.
Importantly, it is also possible to see who gave which ratings,
and if there are large discrepancies. All parties will benefit from
highly rated reviews: the authors of the or iginal manuscript as their
paper has withstood high quality scrutiny, the reviewers themselves
because their contribution has been acknowledged and reported
upon, possibly leading to editorial promotion, and the journal and
its editor as they have, in the perception of the larger community,
succeeded in appointing appropriate reviewers. Altogether, peer
review of reviews will improve the quality of the published work.
We also feel that this will improve the quality of reviews of rejected
papers toward being more constructive.
Another benefit is that the quality of the journal may be assessed
also by the reviewing standards it sets. The impact factor of a jour-
nal is commonly used as the predominant indicator of its quality.
However, we could easily envisage a situation where a journal
increases in stature for the overall quality of the reviews upon
which it bases its decisions. This average rating would represent
the expertise, fairness, and scientific judgment of the editor. This
would be especially relevant for journals that are highly specialized
and therefore generally have a low impact factor, such as Psychome-
trika in our own field. This journal has low citation statistics, but
is highly regarded by both applied and theoretically oriented psy-
chometricians for its rigor and high quality standards. The rating
of the reviews may offer such journals a new metric, on which
the community can base its judgment: one that reflects the rigor
and quality of its reviewing standards, and therefore the presumed
quality of its academic content, not just the popularity of the arti-
cles it publishes. Journals with many highly regarded reviews are
also expected to receive more submissions.
As is the case for papers (in which other theories are often
critiqued), people should be accountable for their assessment of
a paper. Currently, scientists are quite comfortable praising or
discrediting theories or techniques within the confines of their
own papers and/or commentaries, so there should be no rea-
son why people will suddenly refuse to critique (or compliment)
work openly in reviews. Ultimately, it is the editor who makes the
decision; the reviewers merely give a recommendation.
Consistently writing highly regarded reviews, regardless of the
decisions that they lead to, could and should be used as the
basis of appointing editors of journals. A reputation for rigor-
ous and fair reviews is probably not easily earned, and should be
rewarded. Published reviews could be considered publications in
their own right. Currently, commentaries are considered to be sep-
arate publications, even though they are shorter than conventional
manuscripts.
OPENING UP THE DATA
Finally, as the BDPM requires opening up the scientific system, not
only the submissions and reviews should be disclosed, but the data
should be published as well. Although the ethical guidelines of for
example the American Psychological Association (2010) require
data sharing on request, the current practice holds that data are
not shared unless exceptional circumstances hold (Wicherts et al.,
2006;Savage and Vickers, 2009). The right policy is clearly to
publish the empirical data on which empirical claims are based,
unless exceptional circumstances apply (e.g., privacy issues, data
ownership). Thus, we argue that the research data of studies should
be submitted to the journal as a matter of scientific principle as
soon as a paper is accepted for publication (Wicherts and Bakker,
2012), which leads to our fifth principle:
5. Disclose the data: Data should be published online along with
the papers whose empirical claims they support.
Several practical issues need to be dealt with. First, the confi-
dentiality of the human participants needs to be protected. This
can be dealt with in several ways. Data can be anonymized and
release of particular data can be restricted to those who can be
held responsible for protecting the confidentiality. Exemption can
be requested when data are overly sensitive or when legal issues
preclude the release of proprietary data. Second, researchers who
collected the data may wish to conduct future research with the
data after the first results are published. This problem can be dealt
with at the researchers’ request by imposing, say, an 18-month
moratorium on the release of the data (or a moratorium pro-
portional to the cost of acquiring a given dataset). This should
give the original researchers a reasonable head start on their com-
petition. Third, data require proper documentation. Fortunately,
there are several successful data archives in numerous fields of
science. Quality standards of data archiving are well developed
(e.g., see http://www.datasealofapproval.org/). However, it is of
importance to develop guidelines on documenting and archiving
neuroscientific data, which present specific challenges.
Considering data as an integral part of any publication has
been proposed by many, including Hanson et al. (2011, p. 649)
in a recent editorial in Science: “As gatekeepers to publication,
journals clearly have an important part to play in making data
publicly and permanently available.” Although research data lie
at the core of science, they are normally published only in highly
condensed form as the outcomes of the statistical analyses that the
researcher happened to report. Quite often the raw data can tell us
considerably more than a single p-value, or a single brain image
showing pooled differential activity. Specifically, researchers may
disagree on how the data should be analyzed, new analyses may
provide new insights on the findings, and independent re-analyses
of the data may expose errors in the statistical analyses (Wicherts
and Bakker, 2012).
Straightforward checks on the basis of basic information in
papers show an alarmingly high prevalence of statistical errors,
even in the most prestigious journals (Rossi, 1987;Garcia-Berthou
and Alcaraz, 2004;Murphy, 2004;Berle and Starcevic, 2007;
Strasak et al., 2007;Kriegeskorte et al., 2009;Nieuwenhuis et al.,
2011). For instance, after a simple check of the consistency between
reported test statistics and p-values in a fairly representative sam-
ple of 257 papers published in psychology, Bakker and Wicherts
(2011) found that nearly half of these papers contained at least
one error in the reporting of statistical results. In roughly one
in seven papers they found a result that was unjustly reported as
being significant. In another study it was found that researchers
who report such erroneous results are less likely to share their data
for reanalysis (Wicherts et al., 2011). As these errors were identi-
fiable from just the information present in the published studies,
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they could have been prevented by sound statistical review. By
making reviews both public and accountable, more errors might
get identified (e.g., because spotting of such errors is likely to be a
straightforward way to gain a high profile as a statistical reviewer.)
However, these errors might just be the tip of the iceberg. Other
statistical errors can only be exposed with access to the raw data.
In addition, availability of the raw data may help prevent scientific
misconduct (Wicherts, 2011).
Apart from statistical errors, the details of statistical analyses
typically affect what can be concluded from the data. Results are
often dependent on decisions like how to transform the data, the
methods used in averaging across subjects or over time, or the iden-
tification of outliers. Analyzing neuroscientific data in particular
can be a complex task in which statistical decision making may lead
to published effects that appear to be inflated (Kriegeskorte et al.,
2009;Vul et al., 2009). On top of that, researchers often have a lot
to gain in finding and being able to report an interesting (and often
significant) result. Since in many scientific fields (with the notable
exception of some medical fields; ICH, 1996) statistical choices are
not explicated in advance in statistical protocols, the researcher
often has a lot of room to maneuver in doing the analyses. The fact
that many actually do capitalize on this freedom is evidenced by
the statistically unlikely (Sellke et al., 2001) overrepresentation of
p-values just below the typical 0.05 threshold for significance that
has been documented in various fields that involve traditional data
analyses (Ioannidis and Trikalinos, 2007;Ridley et al., 2007;Gerber
and Malhotra, 2008a,b). If contention exists about the decisions
and analyses, the only scientific way to resolve the issue is to have
the raw (or pre-processed) data available for anyone to examine.
At the end of the day, whether such re-analyses should be consid-
ered nitpicking or pertinent to the hypothesis of the paper is to be
judged by the scientific community.
Of course, data sharing will not only serve as a quality control
device (although this is a crucial aspect). There are many positive
incentives for the scientific community. One of those clear benefits
is the more efficient (re)use of existing data. Especially in fields that
rely on complex, computationally heavy analyses such as behav-
ior genetics, (cognitive) neuroscience, and global climate models,
sharing data will vastly increase the availability of data to vali-
date new techniques and uncover previously unnoticed empirical
phenomena in existing data. Examples of successful data sharing
programs are the Human Genome Project2, Neurosynth3, and the
BrainMap Project4. Data that have alreadybeen published could be
used for additional studies without much additional cost. Reusing
data will perhaps shift the focus away from “new data” (several
high-impact journals explicitly state that data should not have
been published before) and toward new findings.
THE FATE OF A PAPER IN THE BDPM
Given the above, what would happen if one submitted a paper
in the broad daylight paper system? A paper is submitted to the
desired journal, including the dataset (stripped of any identi-
fiers and pre-processed if necessary) on which the conclusions
2http://www.ornl.gov/sci/techresources/Human_Genome/home.shtml
3http://neurosynth.org
4www.brainmap.org
are based. This paper, including the dataset, is sent to a selection
of reviewers with the necessary expertise. After an appropriate
timeframe, they submit their reviews and the recommendations
(reject, revise and resubmit, accept) that follow from their reviews.
The editor then decides on the basis of these reviews whether or
not to accept the paper, possibly weighing the reviews on the basis
of previous reviewer quality ratings (i.e., one of the reviewers may
have a high average rating for his or her previous reviews). If the
paper is ultimately published, it is published on the website of the
journal. The website contains the manuscript, the editorial deci-
sion, the reviews, and the raw (or pre-processed) data. Colleagues
can then, after reading the manuscript and the reviews, rate those
reviews on a scale of 1–5 (based on the “at least one publication”
rule). These ratings represent a guide for a new reader of the
manuscript, both to its virtues and possible problematic compo-
nents. Finally, readers may comment on the manuscript and so
review the paper themselves after it has been published. Although
such later reviews play no role in decisions concerning acceptance
of the paper, they do allow the community to comment on it.
Like the original reviews, these later comments entail a manner to
make a career as a reviewer/commenter. After a period of time, this
would create a dynamic representation of the validity and quality
of the paper. Does it stand up to scrutiny? Are the reviews upon
which publication was based considered to be rigorous? Are any
potential flaws pointed out in the later comments? Let us now
re-examine the Kanazawa (2008) case from the perspective of this
new system, and how this is an improvement.
A COUNTERFACTUAL HISTORY OF THE CASE STUDY
What then, in our system, would have become of the case study,
and why is it an improvement? The paper would have been sub-
mitted to the same journal. We consider it quite likely that it would
have been met with more criticism and that the indisputable errors
discussed above would have been averted in earlier phases of the
review. Perhaps reviewers would have opposed publication, but let
us suppose that they would have recommended publication. Sub-
sequently, the paper and its reviews would have become available
for all to read. If the system works as we envisage it, several things
that we consider an improvement could happen.
Firstly, anyone (including journalists) will be able to read the
paper, but also the reviews on which the acceptance was based,
the ratings these reviews received, and whether they were suf-
ficiently critical. This will go a long way in judging whether to
accept the (possibly controversial) views put forth. On the basis
of this assessment, people may then rate those reviews in terms
of thoroughness, scientific credibility, and general quality. We
expect many readers of Intelligence to not have rated the reviews
of Kanazawa’s (2008) paper highly.
Secondly, readers may comment informally (and under their
own names) on the paper as much as is currently possible in jour-
nals like PLoS ONE. This would allow for instantaneous feedback,
both positive and negative, on the merits and possible flaws of the
manuscript and its reviews. Currently, it is no exaggeration to state
that the impact factor of the journal is often considered the most
important factor in judging the merits of an individual paper. This
is clearly a rather crude heuristic, better replaced by discussions
and feedback on the actual paper.
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Wicherts et al. Transparency in science
Finally, readersmay use the data (that was made available along-
side the manuscript) to evaluate the data, to consider alternative
hypotheses and perhaps to even be inspired to re-analyze the data
in a way that provides even more, or different, support of the the-
ory under consideration. Unlike many other instances in which
data are unavailable after publication (Wicherts et al., 2006,2011),
Kanazawa’s (2008) data could be submitted to secondary analyses.
These analyses cast some doubt on his hypotheses (Wicherts et al.,
2010b;Hassal and Sherrat, 2011).
Over time, this would lead to a changing and dynamic con-
sideration of the merits of the paper, based on the quality of the
reviews (as judged by readers), the general tone of comments and
whether or not any convincing counterarguments are put forth
over time, possibly based on new analyses. Or, of course, some-
one might find a fatal flaw. Notably, the converse may also be
the case: if all the negative comments are only based on ideolog-
ical critiques, and not on substantive or scientific arguments, this
may be considered implicit support for the claims in the paper,
regardless of their (un)popularity. Of course, the best possible
scenario is that the open nature and dynamics of the BDPM cre-
ate a community where there are clear incentives for thorough
reviewing. We hope that all readers would consider this alterna-
tive history to be preferable over what actually happened in this
specific case.
FEASIBILITY OF THE BDPM
One could argue that our system may sound good in theory, but
that the reality of incentives and the sociological dynamics of
science are such that they are not compatible with a fully open
system. We think that although this has some superficial plausi-
bility, a closer inspection of specific problems shows that none are
insurmountable, and that these problems are outweighed by its
benefits.
OPENNESS
Will people be willing to review openly? Although the fear that
people will not be willing to sign their reviews openly seems rea-
sonable, empirically, this does not seem to be the case. Smith
(2009) has an interesting empirical finding: “Interestingly, when
we asked a sample of reviewers whether they would review openly
about half said yes and half no. When we conducted the trial, very
few people declined to review openly and when we introduced the
policy only a handful of reviewers in a database of around 5,000
refused to sign reviews.” Medical journals published by BioMed
Central have successfully introduced a system in which signed
reviews are published alongside the published papers. Although
Godlee et al. (1998) did not find clear benefits of having reviewers
sign their reviews, such benefits may well appear when the reviews
are published and subsequently rated by readers.
HONESTY
Will people be equally honest? Another fear may be that the visi-
bility of reviews will lead people to sugarcoat their reviews, where
they would have criticized sub-par work more harshly in the past.
One plausible fear may be the imbalance of power in the com-
munity. For instance, a young and upcoming researcher may not
want to make any enemies, thus “pulling punches.” This may be
the case, but we cannot envisage this to be a big problem. Even
a cursory glance at the literature shows that scientists are gener-
ally not reluctant to criticize one another. In fact, in our view it
is far more likely that the scientific community appreciates hon-
est, well-founded critique, regardless of whether someone is a
scientific veteran or a starting graduate student. And if someone
does tend to pull his or her punches, this will become appar-
ent in the BDPM as overly tame signed reviews from this person
accumulate. An “accept as is” from someone who is also occa-
sionally critical and regularly rejects papers may be more valuable
than an “accept as is” from someone who always recommends
publication.
PARTICIPATION
A glance at some of the existing online possibilities of post-
publication commenting (e.g., at PLoS ONE) shows that not all
papers will be heavily commented on. Perhaps not all reviews will
be rated. This is not a problem of the new system, but a simple
fact concerning the sheer volume of scientific production. Not all
papers will be widely read, not all papers will be cited, and not
all papers will have a large impact. This already applies to even
the highest impact-journals (e.g., Mayor, 2010). The greatest ben-
efit of the BDPM is that it offers the tools and opportunities for
correction, falsification and quality control, and gives increased
insight into the background of a paper. Moreover, by introducing
a system in which the ratings of reviews have an influence on the
selection of reviewers and even editorial positions, we expect a
stronger involvement by the community.
ABUSE
Some may fear that a reward system based on ratings is easily
exploitable. However, given that users can view ratings by name,
we think the simple fact of having traceable ratings will largely
diminish this problem. Everyone can see where the ratings of the
reviews come from. This may serve to expose an excessive degree of
nepotism. Although it is perfectly natural (and highly likely) that
people rate the work of their colleagues highly, insight into who
gave which votes will again allow people to judge what they think
of a manuscript. If, say, all the people with a statistics background
rate a review poorly, that may be an incentive to partly discount a
review that argues that inappropriate analyses were used.
LOGISTICAL ISSUES IN DATA SHARING
Although data files from many studies in the medical and behav-
ioral sciences are quite straightforward and are readily archived,
this does not apply to most multidimensional data files from neu-
roscience. There is a clear need for guidelines and best practices
of the sharing of such complex data files. The extensive pre-
processing of neuro-imaging data should be documented in ways
that enable replication on the basis of the raw data, whereas pre-
processed data that were used in the published analyses could be
submitted to the journal. Rigorous documentation of data han-
dling and the archiving of the raw data (even if these data are
submitted to more specialized repositories or simply stored at the
academic institution) is essential for replication and is required
by ethical guidelines. Major funding organizations increasingly
demand that data are shared (Wicherts and Bakker, 2012) and so
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Wicherts et al. Transparency in science
the costs associated with sharing of data should become an integral
part of research funding. We are aware of previous failed attempts
of journals (like the Journal of Cognitive Neuroscience in the mid
1990s) to implement policies of data sharing, but we feel that the
times are changing. As the number of (high-impact) journals with
such policies increases so will researchers’ willingness to share.
CONCLUSION
In sum, we do not see insurmountable problems in setting up a
truly open scientific publication system. Our moral principle of
openness as a default mode of science, rather than as an exception,
thus suggests that we should simply start implementing such a sys-
tem. Increased transparency at various levels would, in our view,
eradicate a number of practices that arise under the current shroud
of secrecy. Editorial manipulation through choice of reviewers
would be exposed almost immediately. Low quality and/or biased
reviews would, in our view, quickly disappear under the pres-
sure of daylight. Accepting papers that include gross errors would
certainly become more difficult. Due to the possibility of earning
credits through good reviewing, reviewing itself would finally start
to pay off. Data would become publicly accessible,which not only
allows for replicating the statistical analyses, but also archives the
data for use by future generations of scientists. There is no system
without drawbacks. However, all things considered the proposed
ways of increasing transparency appear desirable. It remains to
be seen how researchers react to increased openness; it is entirely
possible that they will happily embrace it. There is only one way
to find out: just do it.
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Conflict of Interest Statement: The
authors declare that the research was
conducted in the absence of any com-
mercial or financial relationships that
could be construed as a potential con-
flict of interest.
Received: 14 May 2011; accepted: 16
March 2012; published online: 03 April
2012.
Citation: Wicherts JM, Kievit RA, Bakker
M and Borsboom D (2012) Letting the
daylight in: reviewing the reviewers and
other ways to maximize transparency in
science. Front. Comput. Neurosci. 6:20.
doi: 10.3389/fncom.2012.00020
Copyright © 2012 Wicherts, Kievit,
Bakker and Borsboom. This is an open-
access article distributed under the terms
of the Creative Commons Attribution
Non Commercial License, which per-
mits non-commercial use, distribution,
and reproduction in other forums, pro-
vided the original authors and source are
credited.
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