Most scientists are well aware of the need
to guard against potential sources of pressure toward bias,
particularly when work is conducted in contexts of litigation
and regulation, but it is not clear that the usual sources
of
concern are actually those that are most important. In this
article, I argue that, although overt pressures to slant
findings may well be problematic, more attention needs to be
devoted to the insidious but potentially more significant
pressures toward bias that go largely unnoticed, often because
they come from unseen or unexpected directions.
I present the argument
in four main sections: In the first I discuss my experience on
a scientific
review panel, illustrating that potential sources of bias in
science are more complex than is often assumed. In the second
section I discuss that experience and this article's
larger points in the context of existing professional
literature on the topic, noting that the literature offers
valuable contributions but also includes important oversights
and omissions. The third main section illustrates this point
by
drawing on another, more recent experience, in which I was able
to observe first-hand one of the ways in which a major
multinational corporation was actively seeding the scientific
literature. Finally, the fourth and closing section offers an
initial or draft typology of key ways in which the unseen
sources of potential bias may be considerably more significant
than those that are seen and/or actively resisted.
The committees of the National Academy of Sciences/National
Research Council (NAS/NRC) generally begin with closed-door
sessions, in which committee members are asked to disclose and
discuss their sources of bias or conflicts of interest,
including any business, research, or other interests or
positions that might be perceived by outside observers as
creating a potential for a conflict of interest. As NAS
staffers commonly explain, the most knowledgeable scientists
available on many issues also happen to be the ones who have
worked and published extensively on the topics in question,
so
the intention is not to exclude all scientists who might have
strong viewpoints. Instead, the goal is to have a balance of
viewpoints and experiences and to discuss openly any such
potential sources of bias, real or perceived, at the outset.
Safeguards such as these
are laudable, but as indicated by the literature discussed in
the next section
of
this article, they are also incomplete. One of the reasons is
illustrated by a bias discussion that occurred in connection
with a relatively recent NAS/NRC review of the scientific basis
for a proposed low-level radioactive waste facility in the
northeastern United States. One after another, the new
committee members discussed previous work they had performed
for the nuclear industry—and then announced a complete
absence of bias, generally doing so with considerable feeling.
Two points about these
self-assessments were particularly notable. First, in comparison
with the
agonizing and painstaking way in which social scientists
usually discuss potential sources of bias, the self-assessments
were characterized by a remarkable absence of reflection,
sensitivity, or in some cases, evidently even awareness of the
appearance of potential conflicts, even though the assessments
were being offered by scientists who were otherwise highly
perceptive. One scientist announced with total conviction, for
example, that no one could possibly accuse him of having any
biases about the site we were about to review, because he was
the top manager for a different low-level nuclear waste
site—one that was about a hundred miles away, in the next
state. Another announced that, although he had spent some 30 years
working in or as a consultant for the nuclear
industry—always for organizations that produced nuclear
wastes and/or needed to dispose of them—at least 5 years
had passed since he had done any work for the specific nuclear
contracting companies that happened to be involved with the
specific site we were being asked to review. Still another
reported that although she had worked extensively for the U.S.
Department of Energy—the federal agency with lead
responsibility for disposing of high-level nuclear
waste—that background had absolutely no relevance to a
review of a document that was intended to facilitate the
development of a site for low-level nuclear wastes.
So it went, around the
table. By the time the discussion had ended, 13 members of the
committee—including me—disclosed that we had done
work for the companies that generated or attempted to dispose
of nuclear waste. Only three members—again including
me—had done work for the communities, states, or
nongovernmental organizations that were opposed to nuclear
facilities in their areas.
In the most diplomatic
tones possible, I raised the issue of the appearance of balance.
I assured my
colleagues that, in the process of working with them, I was
already learning to have great respect for their intelligence
and integrity. Still, I reminded them, the key issue in the end
would have to do with our committee's
credibility—particularly in the eyes of people who,
unlike those of us in the room that day, would not have the
opportunity to become acquainted with the committee members in
person.
This was no minor issue.
The site faced intense opposition—much of it animated by
claims that previous work on the repository had been performed
by agencies
and consultants having far more commitment to the nuclear
industry than to fair or balanced science. If that original
work were to be given a clean bill of health by a committee
consisting largely of persons with long histories of employment
in that same nuclear industry, the net result might do more
to
damage the credibility of the committee, and possibly the NRC
itself, than to improve the credibility of the work being
reviewed.
Several other members of
the committee shared this concern, and several did not, but the
conversation
only became heated at the next step, when we tried to identify
potential committee members who might have as much credibility
in the eyes of industry opponents as the initial committee
members could be expected to have in the eyes of nuclear
industry supporters. Although several of the potential
candidates were exceptionally well-qualified scientists,
virtually all were denounced, most with a level of passion that
bordered on ferocity. A typical verdict—offered with a
memorable sneer, and with a degree of scorn that goes well
beyond what the printed word can convey—was that
Professor X was "one of those 'anti'
types." Most other potential candidates for the committee
were denounced with similar intensity, and the end result was
that committee's composition, although far from being
balanced, remained completely unchanged.
In the end, fortunately, the committee
managed to finish its work without creating credibility
problems for the NAS/NRC. No small part of the reason was that
the committee genuinely did carry out its work in a fair and
balanced manner, although another part of the reason had to
do
with the specific conclusions reached. As the committee looked
into the methods and calculations that had led to the proposed
waste site, signs of increasingly serious errors came to light,
and ultimately, the committee unanimously endorsed a report
that was highly critical. Although we found no evidence of
evil
or malicious intent, the final report clearly indicated that
the committee saw the analysis and conclusions as fatally
flawed.
Both halves of that committee's
experiences are directly relevant for understanding the
pressures on science in contexts of litigation and regulation.
On the one hand, the scientists on that committee—like
most others—truly did think of themselves, with good
reason, as being scrupulously fair and balanced, and they would
have rebuffed, vigorously, any overt efforts to buy or bias
their conclusions. At the same time, however, that
committee's members—almost certainly including
me—also shared with other scientists a significantly
lower level of ability to recognize, let alone to resist,
potential sources of bias that are harder to detect.
A comparable pattern is
evident in the common story about a boxer who loses a match not
so much
because he let his guard down, but because a punch came from
an unexpected direction, and he "didn't see it
coming." For science in contexts of litigation and
regulation, it may well be important to focus not just on the
obvious ways in which scientists need to be careful of not
letting down our scientific guard, but also on the more subtle,
gradual, yet perhaps ultimately more powerful ways in which
bias can creep into scientific thinking and conclusions,
precisely because even the best-intentioned of scientists can
fail to see it coming. After a brief review of the academic
literature that has emerged on this point, I examine the issue
with greater specificity, illustrating the potential dangers
by
using another first-hand experience that gave me an opportunity
to observe such a process at work.
For readers who are not
already familiar with existing analyses of relationships between
economic
interests and science, a useful starting point is to recognize
that the possibilities are generally considered worrisome, not
reassuring. Although relatively few concerns are raised in some
subsets of the existing literature, such as the classic or
Mertonian tradition in the sociology of science—where
most authors would see corporate intrusions into the orderly
progress of science as being inappropriate but relatively rare
[see e.g., Merton (1973)]—the more common patterns
involve expressions of concern (Dietz et al. 1989; Freudenburg
1996; Gieryn 1983; Kinchy and Kleinman 2005; Krimsky 2000;
Lawless 1993; Molotch 1970).
Much of the attention has
focused on relatively straightforward ethical considerations,
such as the
problems of potentially tainted sources of funding for
scientific laboratories, or the ways in which an interest in
product commercialization might influence applied research,
in
terms of either overstating benefits or steering away from
consideration of potential drawbacks and risks (Kleinman 1995;
Kloppenburg 1988; Levins and Lewontin 1985). One of the most
commonly noted and readily understood problems, for example,
involves cases where corporate interests have sought to keep
unfavorable evidence from coming to public attention or to
undermine the legitimacy of more critical work (Dietz et al.
1989; Krimsky 2000; Martin 1999; Rosner and Markowitz 1985).
Other analyses, however, have pointed to problems that are less
overt. In an analysis of logging on public lands, notably, Hirt
(1994) identified a long-standing pattern that he called a "conspiracy of optimism," involving estimates about
the rate at which new trees would grow up to replace the ones
removed by logging. My colleagues and I have referred to a
comparable pattern in less colorful language, calling attention
instead to what we have called the "asymmetry of
scientific challenge" [see e.g., Freudenburg (2001);
Freudenburg and Gramling (2002); and Freudenburg and Youn
(1999)].
As Hirt (1994) noted, such
patterns may be especially likely when the relevant government
agencies have
come to see their interests as being shared with those of an
organized industry, as in the case of the Atomic Energy
Commission and the nuclear power industry, or of the U.S.
Forest Service and the logging industry (Clarke 1985; Martin
1999). In recent years, however, a similar problem has been
identified in biomedical or health-related research. As noted
by Brownlee (2004), there have been growing concerns about
potential biases in these fields, due in part to the fact that
private funding of drug trials has grown so
spectacularly—from $26 million in 1984 to $2.3 billion in
the year 2000—with 60% of the clinical trials now being
funded by biomedical companies rather than by the government.
In a pattern with
an uncomfortable similarity to Hirt's "conspiracy of
optimism," one of the most striking implications of this
trend has involved what Brownlee (2004) calls "happy
talk" about medical products. In one case, for example,
Pfizer, the manufacturer of the prescription painkiller
Celebrex, supported a study comparing that drug against the
over-the-counter medicines ibuprofen and aspirin. The results
of a massive 6-month study that favored Celebrex were published
in the prestigious Journal of the
American Medical Association (Silverstein
et al. 2000). By contrast, when the final year-long study led
to less cheerful findings—showing the
sponsor's painkiller to be associated with more
gastrointestinal side effects and 3 times as high a level of
serious heart problems than the over-the-counter medicine
ibuprofen—those results were never published at all. By
the end of 2004, the National Cancer Institute halted a
Celebrex trial because high doses of the drug were linked to a
tripling of cardiovascular problems—a pattern that Pfizer
called "unexpected," even though one of
Pfizer's own studies had suggested comparable problems
(Henderson 2005). As these words were written, Celebrex was the
only one of the so-called Cox-2 inhibitors still on the market
in the United States, with others having been removed under a
cloud of legal and scientific suspicion that included a rare
"expression of concern" in the New England Journal of Medicine about evident withholding of data on heart attacks
related to another Cox-2 drug, Vioxx (Curfman et al. 2005;
Girion 2005).
In his more extensive
assessment of biomedical research, involving more than 60,000
articles from
more than 175 journals, Krimsky (2003) found that this pattern
may not be an isolated one. In fact, only 0.5% of the authors
revealed potential conflicts of interest, even though roughly
a
quarter of biomedical researchers were receiving industry
funding at the time. Another assessment—a meta-analysis
in the Journal of the American
Medical Association by
Bekelman et al. (2003), pulling together results from eight other
articles
that
collectively assessed a total of 1,140 studies—found
additional support for the "happy talk" hypothesis,
namely, a clear and statistically significant association
between industry sponsorship and pro-industry conclusions.
Bekelman et al. (2003) also found that roughly a quarter of
investigators had industry affiliations, that roughly
two-thirds of those investigators' academic institutions
held equity in startup companies that sponsored research being
done at the same institutions, and that industry sponsorship
was clearly associated with restrictions on publications and
data sharing.
These and other assessments
show that there is a certain degree of legitimacy in the usual
concern,
which has to do with what might be called the cynical version
of the Golden Rule—those who have the gold make the
rules. At this point, however, I return to a first-person
account—one that starts by acknowledging that this usual
concern was also the first one that occurred to me when I had
an unexpected opportunity to gain first-hand insights into the
potential pitfalls of litigation-related research [for a more
extensive discussion, see Freudenburg (2005)]. On the basis of
what I learned from my own experiences, I now see other
concerns as more worrisome, and I attempt to illustrate here
the reasons why that is so.
In essence, my first worry
at the time was that I might be agreeing to a Faustian bargain—selling my
scientific soul, with the role of the devil being played by
company lawyers who in the end would tell me what to publish.
What I experienced, I now believe, was just the
opposite—not that the corporation ever put strong or even
mild pressure on me to publish something with which I would be
uncomfortable, but instead, consistent praise for the fact that
they considered me to be such a principled, credible scientist.
The problem I failed to see, at the time, involved the
temptation to start changing my own judgments, in far more
subtle ways, in response to their repeated insistence that it
was precisely my independence and scientific credibility that
they valued.
It all began when I picked
up the telephone. At the other end was a gentleman I had not
previously known but who worked for a company I knew reasonably
well. Over the next several months, he and the experience would
teach me a good deal more about one of the ways in which
economic interests might influence the course of
science—one that had never before occurred to me or, for
that matter, to even the most radical and conspiratorially
oriented of my students. Given that I had conducted extensive
fieldwork and had the habit of recording my notes on a
hand-held tape recorder, I followed the same instincts after
this telephone call, and there is no better place to start the
reporting of what I learned than with the notes I recorded then:
I just got off the
telephone with [identifying reference]. He was calling me in
conjunction with
[his company's] appeal of the punitive damage awards in
[a lawsuit]. . . . [H]e said, he wanted to see if I might be
interested in writing an article that [his company] would be
able to use as part of its appeal of the punitive damages in
the case. As he put it (the following is as close as I can get
to a verbatim recording of his remarks from just a few minutes
ago):
Naturally, we have a range
of expert witnesses and so forth, but we find that it's also
helpful to have people working on articles that come out in
academic publications. We've often worked with
economists, for example. A lot of them feel that punitive
damage awards are very inefficient, compared to other
approaches such as regulation, and naturally, that's a
perspective we're quite comfortable in supporting. But
we're exploring whether we might want to work with
professors in publishing things from a few other perspectives,
too. . . .
Basically, what we're exploring is
whether it's feasible to get something published in a
respectable academic journal, talking about what punitive
damage awards do to society, or how they're not really a
very good approach. Then, in our appeal, we can cite the
article, and note that professor so-and-so has said in this
academic journal, preferably a quite prestigious one, that
punitive awards don't make much sense.
At this point, he and I
spent some time exploring various possibilities that might be
of interest both
to me and to his company. By the end of this conversation, I
was greatly intrigued, but also ambivalent. I had qualms about
doing this form of consulting work, but I found that my qualms
were calmed enough—both through ongoing interactions with
this caller and through learning what it was that I was or was
not asked to do—that those qualms never became a real
roadblock. In essence, I proposed only those topics that I
would feel comfortable in turning into journal submissions,
leaving to him and his company the question of what to support
and pursue. Similarly, although he suggested several topics to
me, he never pressured me to take on a topic that seemed to me
to be inappropriate. Powerfully counterbalancing the
ambivalence, at the same time, was the fact that I was very
curious to learn more. From the notes:
I was exploring
something I still don't fully comprehend, save perhaps at a strictly
intellectual level—how it is that a company as big as
[his] would actually want to pay a sociologist for doing
something that we normally think of as providing a useful
example of the word "obscure"—publishing in
an academic journal—and what good it could possibly do
them. . . .
Part of the answer on "what good it
could do them" had to do with the dynamics of the appeals
process. At the level of an initial or jury trial, the caller
explained, academic articles would have relatively little value
for his company—a judgment he based in part on research
by another one of his company's consultants. As he
summarized that research, ordinary jurors tend to be swayed by
nonfactual considerations, including the fact that it is easier
to sympathize with "little guy" victims than with a
massive corporation such as his, but also, he insisted,
"by a kind of lottery mentality . . . they (the jurors)
think that 'next time, that could be
me'"—the lucky person who might enjoy a
windfall of a similarly huge jury verdict. "Once it gets
to the judges," on the other hand, he said, "you
start to have a better shot. . . . With the judges,
there's at least a reasonably good chance that
they'll be able to see things as they ought to
be."
As the process was unfolding,
I asked myself the kinds of ethical questions that will occur
to many
readers of this article. In the end, I wound up concluding in
each case that I was in fact proceeding in a scientifically
appropriate, ethical way. In retrospect, however, I believe
that I was so focused on avoiding overt pressures to state
predetermined conclusions that I missed what is now the main
point of the present article—I failed to recognize the
power of more subtle forms of influence. To be more specific, I
was initially worried mainly about an issue that has been
raised, eloquently, by one of the reviewers of this article,
who argued in his/her review that scientists should establish
"a strong rule of thumb: Don't create academic
literature under contract." At least from that
reviewer's perspective, there is a clear difference
between research sponsorship versus preparation of journal
articles under contract, because "sponsorship should not
allow them [the corporate sponsors] to censor what the
researcher writes." At the outset, my main worry had to
do with this very possibility—the potential that the
corporate sponsors might try to censor what I wished to write.
As events unfolded, I discovered that those sponsors went out
of their way to avoid doing anything I might have interpreted
as raising even vague hints of censorship—and yet in the
end, that did not prevent the relationship from having a far
greater influence over my thinking and writing than I believe
I was able to recognize at the time.
My thinking at the time is perhaps
best-illustrated by an excerpt from field notes that, with the
benefits of hindsight, I now see as being insufficiently
self-critical or thoughtful, even though I remember seeing
myself as having been concerned with balance when I wrote these
words:
I must admit, I have quite
a complex set of reactions at the moment. Part of me is deeply
bothered by
the fact that this sort of thing is going on—at
all—let alone by the fact that I might become part of it.
Another part of me—the middle-of-the-road part—is
tapping me on the shoulder, reminding me that I've always
said I try to be a straight shooter, I call them as I see them,
and whether it's [his company, or his company's]
sworn enemies, if they can use my stuff, fine, and if not,
that's their choice. . . .
I see a clear potential
for ethical quagmires and quicksand, of the bottomless-pit variety,
but I
guess at least for the moment, so long as I continue to be
worried about those questions, there's at least some
reasonable hope that I'll continue to learn more, while
not completely selling my soul. . . . I guess I simply need to
remain true to my ethnographic principles, but also my
researcher principles . . . performing a remarkable balancing
act at the same time—giving [his company] a quality
product for the money . . . while not sending anything off to a
peer-reviewed journal that I'm not comfortable signing
my name to.
Soon after that, his company
flew me down to their headquarters for a face-to-face meeting.
At that
meeting, I remember saying to them that, although I had written
some articles that would warm their hearts and others that
would be more likely to bring them heartburn, the ones they had
in front of them before I arrived were mostly of the "heartburn" variety. Under the circumstances, I
wondered, why had they invited me down anyway? Their answer,
offered without hesitation: "How do you suppose we could
find somebody credible who hasn't said some critical
things about us?" That response, and the good-natured way
in which it was presented, did a good deal to put me at ease,
as did the congenial tone of our conversations more broadly.
They made it clear that day—and reinforced the point in
many ways in subsequent interchanges—that they had
absolutely no intention of censoring my work. They never did
censor my work, or even drop vague hints that they might be
so
inclined. Instead, they emphasized repeatedly that they saw me
as the kind of principled, independent scientist who could
never be swayed by nonscientific factors such as threats or
dollars. The problem seems to have been that, each time they
offered such assurances, I came to believe them more.
By the end of that visit,
we agreed that we would examine several different possibilities,
and that I
would work to develop one or more of those ideas for an
article. Over the next several weeks, I did in fact develop
several outlines for potential article submissions. The one
that the company found most interesting had to do with some
thoughts I had already "been thinking about writing up
some day," arguing that the adversarial approaches of the
legal system ran precisely counter to the prescriptions for
sensible risk management that were beginning to emerge from the
literature on risk analysis and risk management at the time. In
essence, although adversarial procedures encourage secrecy, the
findings from the literature on "highly reliable
organizations" were beginning to suggest the importance
of "organizational permeability" and other forms
of openness, for improving organizational performance in general
and risk management in particular (Clarke 1993; LaPorte 1996;
LaPorte and Keller 1996; Shrader-Frechette 1993). I did a quick
write-up of a draft paper and sent it to my contact at the
company.
Neither my contact nor
anyone else at his company expressed any strongly negative reactions,
although at
least one of the company's lawyers did point out later
that more openness could be bothersome for his
corporation—it could increase the number of people who
would know enough about the company to be able to sue it. The
larger problem, as my contact ultimately explained to
me—in an explanation that I believe to have been
genuine—simply came down to the value of my argument to
his company. He thought the article would be
"nice," he said, but it would not really help their
case enough to be worth spending the additional dollars that
would be required, at my consulting rate, to turn it from a
draft into a published article.
I stress again at this
point that, far from raising any hints about censorship at that
time, he made
a point of encouraging me to submit the article to a journal
if I
wished to do so—his was a concern not about the content
of the paper, but about paying me to work on it. At the time, I
remember thinking that his reaction was similar to a rating of
"good" on a grant proposal to the National Science
Foundation: Even if a reviewer might check the box that says,
"Fund this proposal if resources are plentiful," few
scientists have ever encountered cases where resources are that
plentiful. I need to add that my own evaluation was not
that different from his: Even after all these years, I still
have not invested the time that would be needed to rewrite that
draft paper and submit it to a journal. It remains buried in
a
file cabinet, and unless I encounter some new reason to revise
and refine that early draft paper, it may ultimately be less
likely to go into a journal than to go into university
recycling bins.
We did discuss other possible
article topics before parting company, but my reactions to his
suggestions were no more enthusiastic than were his reactions
to mine, in large part because his company was interested in
articles concluding that punitive damages were irrational and "out of control," and
the actual research findings on that point tended not to support
their preferred conclusion
[see e.g., Eisenberg (2001) and Galanter (1983)]. After a few
more conversations, but in quite a cordial fashion, we agreed
to a parting of ways. He closed by reminding me that he fully
intended to pay me for the hours I had put in, and I reassured
myself that I had indeed remained true to my principles,
because I never did allow the potential for income to tempt me
into writing something that I felt to be inconsistent with the
available evidence.
Most readers of this article
are likely to be familiar the old story about the boiling frog—the
observation that a frog will leap out immediately if it is
dropped into a cauldron of boiling water, but that it might not
even notice (and might thus boil to death) being placed into
cool water that is warmed up only gradually. That, however, may
not be quite the right metaphor. The larger problem, instead,
may have to do with needing to ask how we can see what it is
that we fail to see. Part of the answer may lie in being able
to think more carefully about the reasons for failing to see
something. Just as a magician can make things seem to disappear
by getting the audience to focus on something else (Freudenburg
and Alario 2007), part of the answer may be that it may be
easier to influence scientists' thinking by praising
their independence than by seeking to limit it.
Based in part on the first-hand
experience summarized in this article, I now rarely question
scientists
who claim that they have never been subjected to (overt)
pressure to change their findings, or that they are genuinely
proud of just how independent they (honestly) believe they are.
Although I believe they are doing their best to tell the truth
about their own perceptions, however, I am less ready to
believe that those perceptions will offer completely reliable
information about their actual levels of scientific
impartiality. The concern in some ways parallels the issue of "gifts of nominal value"—a specific and
specialized quotation that nevertheless generated more than
32,000 "hits" in a Google search performed August
2007. By far, the majority of the "top" hits
endorsed the appropriateness of small gifts, in contrast to
anything involving greater economic value. As noted in a
biomedical context by Kupersanin (2002), however, "many
studies have shown that even minor gifts have an impact on
clinical decisions." Despite this commonality, however,
my concerns are more specific, relating to the reason why I am
less sanguine than the reviewer quoted above about the
distinction between corporate support for research versus
corporate support for the writing of journal articles.
Somewhat ironically, my
revised reasoning is associated with a less cynical version of
the Golden Rule,
involving the norm of reciprocity and, more specifically, the
forms of reciprocity that do not necessarily even involve
money. If the companies that support our scientific research
are very careful to respect what is important to us in
nonfinancial terms—namely, our objectivity and
independence—then it may seem only fair for us to ask
what we can do for them, "without compromising" our
objectivity.
In some ways, such accommodations
are little different from the ones we all make every day, when
a
colleague asks for extra help on a manuscript or a student is
in extra need of advice. In contexts of litigation and
regulation, however, the consequences can be much more
substantial—and as in the case of the NAS/NRC bias
discussion that I summarized at the start of this article, the
resultant drift of scientists' self-perceptions can have
a cumulative impact that is significantly more systematic in
one direction rather than another.
Table 1.
|
Table 2.
|
Given that self-perceptions
are inherently personalistic, I am offering this article's warnings not
as hard-and-fast rules that deserve to be seen as established
but in the form of possibilities that deserve closer attention
in the future. As a way of adding specificity to my overall
concerns, and potentially providing clearer guidance for future
research, Table 1 identifies five more specific categories of
pressures toward bias that may deserve greater attention. To
switch metaphors, Table 1 suggests that if it is useful to
think of science in any context as being a hunt for truth,
there are at least five ways in which the unseen hazards or
pressures toward bias may be more insidious or more dangerous
than the overt hazards that most scientists have learned to
expect. The first has to do with each scientist's own
internal sense of direction. The second concerns the mental
maps that tell each of us where to look. The third involves the
rules by which we believe we are hunting, and the fourth
concerns the broader "region" or context in which
we believe we are hunting. The fifth set of pressures, finally,
pertains to the ways in which we ultimately measure or assess
whatever quarry we "bag." Of all these pressures,
perhaps the fifth and final set of pressures is the one that
is
in greatest need of further discussion [see also Freudenburg
et al. (in press) and Michaels and Monforton (2005)].
One of the potential blind
spots of science relates back to statistical training. The problem
is
that, at least until very recently, few scientists learned much
about statistical power—the likelihood of failing to
recognize a pattern that is actually present. Partly for that
reason, even well-known and careful scientists will often
emphasize that a "finding" may be statistically
significant through chance alone while overlooking the equally
true point from the other side of the coin—the fact that
even a "statistically insignificant" pattern may
nevertheless be substantively important.
A major source of the problem
has to do with the difference between "pure" and
"applied" science, although this difference, again,
is largely unrecognized. In a world of pure science, it can be
prudent to concentrate mainly on type I errors and
"significance." The salient risk in such work is
that if scientists are not sufficiently careful—that is,
careful about type I risks—other scientists may waste
time disproving a hypothesis that is simply a random fluke. For
decisions that involve real-world risks, on the other hand, the
most important risk may well be just the opposite one—the
risk of assuming that a chemical compound or a technology is
"safe" when in fact it is not. At least in
real-world regulatory and/or litigation-related debates,
however, regulators rarely ask whether we know enough to allow
the public to be subjected to unknown risks [the type II or
"statistical power" concern—see Freudenburg
et al. (in press)]. Instead, as suggested in Table 2, even
among those who have reasonably sophisticated scientific
training, the more common tendency has been to ask whether the
scientific findings are strong enough to justify the imposition
of regulations in the absence of definitive
"proof."
A relatively new line of
work on this problem, drawing on the literature in the sociology
of science
and technology, responds with a four-part argument. First,
science is capable of offering only three kinds of
answers—yes, no, and maybe. Second, contrary to the
widespread assumption that science is neat and
definitive—in line instead with the common finding in the
sociology of science that it is not—most scientific work
in contexts of litigation and regulation falls into the
"maybe" category. In the relatively few cases where
the evidence becomes clear enough that the parties stop
fighting over a given question, in other words, the battles
usually just move on to the next questions that are still in
the "maybe" category. Third, in most real-world
cases of conflicts over litigation and/or regulation, the net
result is that victory goes to the side that wins when the
answer is "maybe." Fourth and finally, even
well-trained scientists are often remarkably unaware of this
pattern. The net result is a reasonably consistent (and
generally but not always helpful) scientific tendency to do
work that will permit clearer yes/no answers—clear
support or rejection of whatever hypotheses are currently being
debated—rather than focusing on what may be a more
important question in contexts of litigation and regulation,
namely, how decisions could be made more rationally and
even-handedly in the absence of just such definitive answers.
When I began to think back
to the colleagues on the NAS/NRC committee who were so adamant
about
their freedom from bias in assessing a low-level waste site,
my
first reaction was the one mentioned in the opening pages of
this article—a sense that those colleagues were not being
sufficiently thoughtful about potential sources of bias. Having
spent more time reflecting on the matter, I think today that
all scientists, myself included, may have more resemblance to
the colleagues on that committee than I originally recognized.
All of us seem to believe, with good reason, that we do a good
job of resisting overt or flagrant pressures toward bias, but
such clear-cut cases may be far more rare than we often assume.
Instead, those clear-cut cases may have more than a passing
resemblance to simplified Hollywood villains—the ones
that wear black hats may be the easiest to recognize, but they
are rarely encountered except in fiction.
At the same time, we often
learn that many of our problems and challenges are at least partly
of our own
making—and partly due to problems that we
"didn't see coming." A recently deceased but
much-beloved colleague used to joke that he specialized in
"pointing out the hidden assumptions in other
people's arguments," and of course, the rest of us
often do so as well. For the future, on the other hand, we may
all do a better job of recognizing and dealing with threats to
scientific balance if we begin to devote more attention to the
ways in which scientific rigor and balance can be
undermined—in our colleagues and in
ourselves—precisely at those times when we see no black
hats, and when we are being praised for our balance and
integrity instead of feeling a need to defend it.
