For commentary on this article, go to
H. M. Collins, "Captives and victims: comment on Scott, Richards and Martin", Science, Technology, & Human Values, Vol. 16, No. 2, Spring 1991, pp. 249-250.
Brian Martin, Evelleen Richards and Pam Scott, "Who's a captive? Who's a victim? Response to Collins' method talk", Science, Technology, & Human Values, Vol. 16, No. 2, Spring 1991, pp. 249-250.
Brian Martin, Captivity and commitment", Technoscience, Vol. 11, No. 1, Winter 1998, pp. 8-9.
Go to
Brian Martin's publications on science, technology and society
Scientific controversies have long
excited both the passions of participants and the interest of social
scientists [1].
For researchers into the nature of science, controversies have the
advantage that social processes normally hidden in laboratories and
offices are brought into open view in a dramatic fashion. Assumptions
that are normally implicit are challenged by disputants, routine
procedures scrutinized and weak points in arguments attacked. The
disadvantage of studying controversies is that it may give an
unrealistic picture of the day-to-day operations of normal science
(Mulkay et al. 1983). In any case, controversy analysis is a thriving
field of study, no doubt due, in part, to the human drama and social
implications associated with many controversies.
The traditional social science approach to scientific controversies
has been to study the social dynamics of science, assuming that there
is a scientific truth underlying the debate. Usually one side is
believed to be much closer to this core truth, and the task of the
social scientist then becomes one of explaining why the other side
persists in its claims. The social scientist usually accepts the
judgment of the most authoritative scientists about scientific
realities.
This positivist approach, a "sociology of scientific error", has been
challenged by relativist analysts of science. In the strong program
in the sociology of scientific knowledge, the analyst is enjoined to
treat competing truth claims symmetrically (Bloor 1976). Instead of
looking only at the side considered wrong by scientific authorities,
the knowledge claims on both sides of the controversy are examined,
and an attempt is made to explain them using social categories [2].
The relativist program differs from the traditional approach in two
major, related ways. First, the social analysis is applied to
scientific knowledge claims, as well as to wider social dynamics.
Second, both sides in the controversy are examined using the same
repertoire of conceptual tools. This contrasts with the traditional
approach, in which scientific knowledge claims are seldom scrutinized
(that task is left to the scientists), and social explanations are
selectively applied to the side without authoritative scientific
backing. It should be noted that relativism is a set of
methodological specifications. Relativists may (or may not) believe
that there is an underlying scientific truth. But for the purposes of
social analysis, they set the issue of truth and falsity aside: it is
not treated as relevant to the social investigation.
Under both positivist and relativist approaches, the controversy is
normally treated as something external to the researcher. It is "out
there": the social research itself is not viewed as part of the
controversy. It is this pervasive assumption that is questioned in
this paper.
Within the traditional positivist interpretation of science, the role
of researchers in relation to scientific controversies appears to
raise few methodological problems. The conventional view is that
social researchers should be objective in their assessment of social
evidence. This usually implies that the social researcher is not
directly involved in the issue being studied.
However, because positivists treat scientific knowledge as different
from other sorts of belief such as religion or "public opinion",
objectivity in relation to scientific knowledge appears to mean, for
the social scientist, accepting received scientific facts and
theories as the truth. It can be argued that because science decides
which side is correct, it does not compromise the social scientist's
objectivity to become involved in support of the correct side.
Indeed, the social researcher may be attracted to the controversy
because of requests from participants, or be drawn to it by a duty to
support truth against misguided opponents. Martin Gardner's popular
treatment Fads and Fallacies in the Name of Science illustrates well the approach also adopted in more scholarly
treatments. From the point of view of those on the other side, social
scientists taking part in this way are definitely "captives of
controversy". From these social scientists' own point of view, and
that of the side of scientific orthodoxy, they are simply supporting
truth against falsity and are not compromised at all.
A relativist or social constructivist approach does not necessarily
raise dilemmas for social researchers either, but for an entirely
different reason. Within the strong program, researchers study
disputes "naturalistically", and this requires their epistemological
and social neutrality. Social researchers, we are told, should not
grind an evaluative axe. If researchers are "captured" by either side
and become part of the debate, then they are deemed to have failed to
maintain a symmetrical approach. It is this assumption within the
relativist perspective which is the main focus of our paper.
A leading instance of alleged "capturing" in relativist controversy
analysis is the study by Collins and Pinch of the dispute over the
existence of psychic phenomena. Their paper, "The Construction of the
Paranormal: Nothing Unscientific is Happening", analyzes the tactics
used by both parapsychologists and orthodox scientists in the course
of the controversy. According to Collins and Pinch, "controversy
highlights social processes with particular clarity" (Collins and
Pinch 1979, 238), and the study of the social processes involved in
these attempts to legitimate parapsychology also provides insights
into the maintenance of the dominant scientific culture.
From the perspective of their relativist stance, Collins and Pinch
argue that the "actual existence" of the paranormal phenomena is
redundant and that their position on the existence of the
phenomena is neutral (Collins and Pinch 1979, 262). However, in an
added note we learn that Collins and Pinch's paper has been drawn
into the debate and used to support the parapsychologists' case.
Parapsychologists commended the paper, while critics of the field
charged the authors with "selective reporting" rather than scientific
inquiry (Collins and Pinch 1979, 263).
Defending themselves against these charges, Collins and Pinch claim
they are "professional sociologists" who are "disinterested in these
questions" (Collins and Pinch 1979, 263). This defence is not
accepted by the discourse analysts Mulkay, Potter and Yearley, who
sought to undermine the relativist analysis of parapsychology by
Collins and Pinch by alleging that the latter were "in a disguised
fashion, constructing their analysis from the point of view of (some)
parapsychologists" (Mulkay et al. 1983, 187). That partisans on both
sides of the controversy saw Collins and Pinch's analysis as favoring
the parasychologists' case is used by the discourse analysts to
support their criticism (Mulkay et al. 1983, 188). According to
Mulkay, Potter and Yearley, the reason for this lack of social
neutrality is that Collins and Pinch uncritically adopted the
parapsychologists' perspectives and terminology.
This methodological demand for a separation between researcher and
researched may appear to work for historical studies and for disputes
contained within the scientific community. In such cases the research
subjects cannot, or may not want to, deploy the social research in
their struggles: historical subjects, being dead, cannot bite back,
and social scientists have little perceived status in technical
disputes between scientific experts. But this convenient separation
between researcher and researched breaks down in current
controversies which involve matters of public policy or some other
strong link to the broader community. We will use our own experiences
in controversy analysis to illustrate this claim. For convenience,
each of the three case studies is presented in the first person,
though each presentation has been shaped by our mutual discussions
and comments.
When I began my study into the
establishment of the Australian Animal Health Laboratory (AAHL), I
knew almost nothing about the topic apart from a few brief newspaper
reports. The establishment of the laboratory was initially thought to
provide a good case study for looking at how government decisions
about "big" science and technology are made in Australia.
The idea that Australia needed a laboratory to diagnose exotic animal
diseases was raised in the late 1950s. Investigations into the
feasibility and desirability of establishing such a facility were
conducted at various stages throughout the 1960s and 1970s by the
Commonwealth Scientific and Industrial Research Organization (CSIRO)
and the Commonwealth (federal government) Departments of Health and
Primary Industry, and these groups very actively lobbied for support
from the government. Government approval was given for the AAHL in
1974; building commenced in 1978 and was completed in 1985[3].
There was little public debate about the need to establish a
laboratory for diagnosing and studying livestock diseases which, by
the good fortune of geographical isolation and the good management of
strict quarantine regulations, Australia had avoided. The reason for
this lack of attention was that most of the planning was not made
public. Most citizens, including farmers who had a particular
interest in animal health, were unaware of the plans to build the
laboratory and of its functions.
It was not until 1981 that farmers' interest was captured when they
learnt that CSIRO had sought and received government approval to
import live foot-and-mouth disease virus into the laboratory when it
was completed. It should be understood that foot-and-mouth disease is
especially feared by farmers. It is highly infectious, and an
outbreak would result in the immediate closure of Australia's export
market for meat and livestock, thereby costing the Australian economy
millions of dollars and ruining many farmers.
The controversy which developed over the importation of the live
virus contained a number of elements. First, there was the debate on
risk: some claimed there was no risk from having the virus at AAHL;
others (mainly farmers) argued that any risk was unacceptable.
Structural security of the laboratory, the likelihood of human error,
and the consequences of not having the live virus were all hotly
debated. Then there was the debate on the need to have live virus.
Proponents argued that the laboratory could not function effectively
without live virus, while opponents (who included scientists) claimed
live virus was not needed. CSIRO, which was to administer the
laboratory and was its main advocate, unwittingly called into
question the need for the laboratory itself when some of its
scientists claimed that without live virus the facility would be a "white elephant" (Scott 1989).
Laboratory proponents claimed that farmers' fears were irrational and
emotional and were fanned along by a few scientists who feared their
research budgets would be adversely affected by AAHL's research
program. Opponents pointed to "empire-building" and stubbornness as
CSIRO's motivation. So the battle lines were drawn and the debate
raged for several years (Scott 1988a).
I tried to keep clear of any active involvement in the debate. I had
no interest, involvement, or stake in the outcome, and no expertise
in veterinary health matters. I intended to be dispassionate and
objective in reporting my findings, and I was confident that I could
maintain the necessary neutrality.
My research began with the readily available public documents on the
laboratory, such as government and parliamentary reports, but then I
needed to go beyond these public accounts of decision-making and talk
to the individuals involved. My first encounter was with an "insider"
opponent who provided me with a variety of background materials and
information about which documents to request from the authorities. So
to some extent, I "entered" the debate via the opponents of the
laboratory.
My next major encounter was with CSIRO. This is the organization
responsible for administering and operating the laboratory, and its
most powerful and prestigious advocate. When I met with members of
the CSIRO Executive to discuss obtaining access to CSIRO files, their
attitude was extremely defensive and cautious. They agreed to give me
access provided I cleared anything I wrote on the subject with them.
This approval opened up vast quantities of material and facilitated
access to the files of other government bodies.
While both sides supplied me with information, the laboratory
proponents did so reluctantly, perceiving my interest as a threat to
their already damaged reputation, and whilst appearing cooperative,
they were anxious to maintain control over my work. The laboratory
opponents, on the other hand, were not uniform in their views - some
saw my work as exposing the politics of CSIRO, some saw it as
vindicating their opposition, others hoped it would settle the issue
- but all thought it was important to reveal and record what had
happened.
My detailed documentation of the decision-making process and the
background to the controversy was not meant to support one side or
the other, to nominate winners or losers, but to reveal the social
processes shaping the knowledge claims. The disputants themselves,
however, were not so sociologically enlightened. They adopted a
traditional positivist stance. For them it was a conflict with a
right and a wrong side, with winners and losers. And my work was
incorporated into the debate.
The opponents of the laboratory were primarily farmers and their
organizations, but they also included members of the public and some
scientists, who were critical of what they perceived as an
unnecessary, costly, and high-risk enterprise. They had been labeled
by the laboratory proponents (who were primarily veterinary
scientists, CSIRO, and government bureaucrats), as irrational,
unscientific, emotional, biased, and politically and economically
motivated in their actions. This depiction placed the opponents at a
considerable disadvantage in the context of the proponents' claim to
objective scientific authority. My analysis corrected this imbalance
by showing the non-scientific, value-laden, and politically-motivated
basis for the proponents' decision-making. Because this was seen as
undermining the proponents, I, like Collins and Pinch, was perceived
by both sides as favoring the opponents.
The opponents of the laboratory described my work as scholarly and
well-documented. The proponents claimed that it was a partisan
presentation, that I had started from a conclusion and then sought
evidence to support it, and that I wore blinkers. One of them called
one of my papers a "mischievous beat-up" and made reference to "dung
beetles digging in the droppings of time". When I submitted work in
progress to CSIRO it was closely scrutinized and my interpretations
and conclusions were constantly challenged. On the other hand, the
laboratory opponents requested copies of my papers, circulated them,
and invited me to address farmers' groups.
One of the effects of my research was to make available information
that was not widely known or had been forgotten. Many participants
did not know the background to the establishment of the laboratory,
and even those involved in the decision-making did not always have a
complete picture of events. The spreading of information and even the
knowledge that someone was actively researching the controversy
altered the debate. In other words, my very presence changed what I
was investigating.
Was I a bad researcher who was captured by the laboratory opponents
and seduced by their attention, or was this the inevitable outcome of
my research?
The question of whether fluoride
should be added to public water supplies to reduce tooth decay has
been one of the most vociferously debated issues concerning science
and public policy over the past forty years. It involves scientific
issues, such as the assessment of the effectiveness of fluoride in
reducing tooth decay and the status of claims of health risks, such
as skeletal fluorosis, allergic and intolerance reactions, and
genetic effects including cancer. It also involves ethical and
political issues, including the compulsion implicit in adding a
chemical to the water supply to treat the individual, and the
question of who should make decisions about fluoridation. The issue
has long been highly polarized, scientifically and politically.
One of the reasons I undertook my study was my long exposure to the
issues through a colleague who is one of the prominent scientist
critics of fluoridation. But, unlike the anti-fluoridationists, I
have never been passionately concerned about whether water supplies
are actually fluoridated. I regularly drank large amounts of
fluoridated water before becoming acquainted with the controversy,
and continue to do so. My interest was and is in the politics of
science as revealed through the controversy.
One of my first tasks was to study earlier sociological treatments of
the fluoridation controversy. There have been many dozens of these,
and almost all of them use a traditional positivist approach:
fluoridation is assumed to be scientifically correct, and there is
little or no discussion of the scientific evidence. Scientific
evidence raised by critics of fluoridation is almost entirely
unmentioned in these studies. The social scientists have seen their
task as one of determining the reasons for the opposition to
fluoridation. A range of hypotheses have been studied: the
demographic characteristics of opponents have been studied (opponents
were found, in some studies, to be disproportionately low in
education, politically conservative, and older); the opposition has
been explained by concepts such as irrationality, alienation and
confusion (Martin 1989).
A number of the social researchers reveal not only their strong
commitment to fluoridation but also the relation of this commitment
to their studies. The United States Public Health Service, a leading
force behind fluoridation since 1950, invited Aaron Spector to study
the issue, and this led to the major project by Crain, Katz and
Rosenthal (1969, v). These authors assume that fluoridation is "progressive" and "rational" and agonize over the political
difficulty that many citizens oppose it (1969, 227-228).
Many social scientists studying fluoridation have seen their research
as a source of insight and advice for the proponents. For example,
Kegeles (1961), in a commentary on social science research on
fluoridation, concluded that "While future research will undoubtedly
continue to emphasize understanding rather than action, there seems
reason to be optimistic that help for the [pro-fluoridation]
practitioner will be one of the eventual by-products." Gamson (1965)
wrote on "How to lose a fluoridation referendum", giving counsel to
proponents on what they should not do.
Twenty years later, the quest for social science understanding useful
to proponents continues. Hastreiter (1983) tried to combine several
different social science perspectives: "Only by using a broad
spectrum of behavioral social science analyses can the complex
process of fluoridation conflict be conceptualized and ameliorated."
(490). There is not a clear boundary between social science research
and what can be called "campaigning literature". Isman's (1981)
"Fluoridation: strategies for success" is a good example. Isman draws
on both social science studies and practical experience in drawing up
recommendations for successful fluoridation campaigns.
As noted earlier, some would argue that there is no contradiction
involved in partisan social research if it is assumed that one side
in the controversy is supported by scientific truth. Indeed,
participation in the controversy on this particular side may be
considered a moral imperative. Gamson (1961, 54) concludes that "Those who believe that truth needs no advocate need only witness a
few of the more heated fluoridation controversies." Hastreiter (1983,
486) states that "as a lesson in sociopolitical interaction, the
failure to achieve universal water fluoridation is a demonstration of
humanity's tenuous ability to apply the knowledge of proved,
cost-effective disease prevention to everyone's benefit." Such
quotations abound in the field [4].
Unlike most of these previous researchers, I undertook my study with
the intention of using the tools of relativist analysis. Obtaining
and studying both the scientific and sociological literature on
fluoridation through standard sources, literature searches and so on,
presented no apparent methodological problems. It was when
interacting with fluoridation partisans that the stance of symmetry
became increasingly difficult.
My social interaction with partisans in the controversy began with
letters to people outside Australia who had been involved in the
debate. Out of letters to 51 individuals in 11 countries over several
years, I received replies to 36. There was not much difference
between the response rates for known proponents and opponents of
fluoridation. But some of the opponents were much more energetic
correspondents than any of the proponents, plying me with numerous
articles, names of people to contact, references and comments. No
pro-fluoridationist did the same. This differential response was
bound to affect my writing: I was aware of materials, such as
personal correspondence, most of which had been supplied by
anti-fluoridationists.
As part of my study, I interviewed 11 leading proponents and 6
leading opponents of fluoridation in Australia, most of whom were
scientists, dentists, or doctors. Only a few of these knew of me and
my work before the interviews. Most of them were forthright and
helpful. But it soon became clear that my minor role in the
controversy had preceded me.
Professor Elsdon Storey at the University of Melbourne told me, after
an hour or so of our interview, that he knew what I was going to
conclude in my study: he had seen a report of a talk of mine on
suppression of dissent, in which I referred to cases of suppression
of scientist opponents of fluoridation. He demanded that anything I
wrote which mentioned him be shown to him in entirety before being
seen by anyone else.
I subsequently received a letter from another senior academic
proponent of fluoridation, Professor Jack Martin [5],
also requesting that he not be quoted in any way without first
approving the entire article. I inferred that he had talked to Storey
after my interviews with them both. After I had prepared a draft
paper called "Coherency of viewpoints among fluoridation partisans" (later published as Martin 1988a), I sent copies to all interviewees
for their comments. I designed the text so that I did not refer
directly to the contents of the interviews with Storey and Martin,
only noting the existence of the interviews and referring to a
published letter by Storey. I received comments from 5 of the 6
opponents interviewed, including some quite critical ones. The only
proponent responses were from Storey, who said he did not want to be
associated with my article in any way, and Martin, who requested that
he not be mentioned in the article, not even in the list of
interviewees (a request which I declined).
Clearly, this was a very one-sided response to my work. It was not
unexpected, since my symmetrical analysis of the controversy meant
that the anti-fluoridationists were given much more credence than is
usually the case in the standard scientific or sociological
literature. The effect was to isolate me from further insights into
pro-fluoridation thinking (except through the literature), while
keeping channels open to anti-fluoridation thinking.
Later, I organized my material into a book and tried to obtain
critical comments on the manuscript from both proponents and
opponents. The three opponents I approached each readily provided
significant comments on the draft, but obtaining comments from
proponents was a more difficult task. I received comments from only 4
of the 12 international proponents of fluoridation I approached.
These responses were invaluable: without them, it would have been far
harder to obtain a good picture of the proponent case, and even
easier to be drawn into the camp of the opponents.
When my papers appeared in Metascience, Social Studies of
Science and Sociological Quarterly, the fluoridation
opponents circulated copies of them. The work was useful to their
cause. In one case, a leading British opponent made my papers the
subject of a couple of his newsletters (although to some extent for
the purposes of criticism).
The fluoridation controversy is so highly polarized that any analysis
that is not strongly pro-fluoridation is seen as anti-fluoridation.
In this context, many proponents apparently saw me as an opponent as
soon as they saw the type of symmetrical analysis I was undertaking.
Therefore, in one sense there was not a lot of effort required to "capture" me to the anti-fluoridation cause. Nevertheless, a number
of anti-fluoridationists were quite critical of some of my
statements. The most common criticism from both sides was that I
hadn't given enough credence to the overwhelming body of science that
supported their case. The trouble was that the two sides differed so
completely about how the science was to be interpreted!
My experiences cannot be attributed specifically to adopting a
relativist framework. Similar problems beset positivists who give
less than complete support to the orthodox scientific position.
Mazur's (1973, 1981) classic paper "Disputes between experts" analyzed the rhetoric of both proponents and opponents of
fluoridation, as well as partisans in the controversy over low-level
ionizing radiation. Mazur's article has been highly cited in the
general social science literature, but it has seldom been mentioned
by pro-fluoridation social analysts.
Edward Groth III (1973) studied fluoridation in the early 1970s as an
issue of public policy. He examined the scientific evidence and
arguments on both sides in considerable detail. Groth was not
interested in supporting or opposing fluoridation, but his intended "neutral" position was not seen this way by partisans. Opponents
eagerly supplied him with information; proponents tried to discredit
him personally and portray him as an anti-fluoridationist. Groth
avoided being a "captive of controversy" only by getting out of the
area (Groth 1988).
Groth did not use a relativist conceptual framework, but his adoption
of a "neutral", critical-of-all-claims stance served as a de facto
relativism. Many of Groth's experiences were forerunners of my own.
The stance of relativist symmetry seems to provide no special
mechanism for avoiding de facto partisanship.
The vitamin C and cancer
controversy centers on the attempt by Linus Pauling (Nobel laureate
and well-known anti-war activist and advocate of vitamin C as both
preventative and therapy for the common cold) and Ewan Cameron (a
Scottish surgeon) to theoretically elaborate and demonstrate their
claim that vitamin C megadose can control or palliate cancer. It is a
well polarized controversy that has spilled over into the popular
press. Pauling and Cameron apart, the interested parties include the "cancer establishment", various influential medical and scientific
journals, the medical profession as a whole, nutritionists,
megavitamin therapists, the holistic health movement, the health food
industry, the pharmaceutical industry, and the many tens of thousands
of cancer patients who, largely as a result of Pauling's and
Cameron's well-publicized claims, currently take large daily doses of
vitamin C. The dispute has become particularly intense over the
claims and counterclaims surrounding the two negative clinical trials
of vitamin C carried out by leading American oncologists at the Mayo
Clinic in 1979 and 1985 [6].
The literature on medical controversies is dominated by the standard
positivist assumption that even the most protracted and rancorous
conflicts may be resolved by the application of the scientific method
to medicine in the form of the rigorously designed and properly
applied controlled clinical trial (Lasagna, 1980; Doyle 1983). In the
case of disputes involving alternative or marginal therapies,
analysts generally have uncritically adopted the orthodox "scientific" medical position. They focus almost exclusively on the
"unscientific", "irrational" or "unproven" claims of the
alternatives, and perceive their analytical task in terms of
explaining the popular "mistaken" or "credulous" adherence to such
scientifically unproven or unjustifiable therapies. The most partisan
of these analysts are committed to the exposure of "quacks" and
"charlatans", and their studies have been incorporated into the
anti-quackery crusades of orthodox organizations such as the American
Medical Association and the American Cancer Society (for example,
Young 1967, 1972; Holland 1982) [7].
There is little in the literature on contemporary medical disputes,
particularly those involving alternative therapies, that is
consistent with a relativist epistemology. The more sociologically
informed analyses by Petersen and Markle (1979a,b; Markle and
Petersen, 1980) of the laetrile controversy avoided espousing the
orthodox cause. They claimed a "causal, impartial and symmetrical"
approach (1979b, 159). But their analyses still lent themselves to
the standard view that the facts about disease and its treatment may
be objectively determined, and that it is their interpretation from
divergent social, political and ideological frameworks that accounts
for the polarized positions of the disputants and the lack of
scientific resolution of the dispute. Their persistent demarcation of
facts from values, their emphasis on the overtly expansionist
"political" tactics of the laetrile proponents as opposed to the
delimiting "scientific" tactics of their orthodox opponents, the care
with which they dissociated their "equal time" treatment of both
sides from any suggestion that "both sides have similar legitimacy"
(1979b, 159), led to their de facto capture by orthodoxy. Petersen's
and Markle's accounts of the laetrile proponents became a resource
for the American Cancer Society's (ACS) "Unproven Methods" list
(1987), and for such a notable "quackbuster" as William Jarvis in the
ACS-endorsed "professional education publication", "Helping Your
Patients Deal With Questionable Cancer Treatments" (1986, 8) [8].
As with Brian's analysis of the fluoridation debate, my own attempts
at a neutral relativist analysis of the vitamin C and cancer
controversy must be interpreted in the context of the dearth of
relativist accounts of contemporary disputes over medical therapies.
In this context, a symmetrical analysis that does not
epistemologically privilege orthodox knowledge claims, but deals
evenhandedly with the claims of orthodox oncologists and marginal
therapists, is flying in the face of all tradition. As I soon found,
it invites the suspicion and hostility of orthodoxy and the equally
problematic embraces of the unorthodox. My thorough grounding in
recent sociology of scientific knowledge had not equipped me to deal
with the unintended consequences of my careful application of the
interpretative tools of relativist analysis.
I am a trained historian of science with a medical background. I
became interested in controversy analysis primarily because I wanted
a contemporary string to my bow. In 1981, I cast around for a topic
and settled on the vitamin C controversy. I had read Pauling's (1970)
well-known Vitamin C and the Common Cold, but I was not even
aware that there was a vitamin C and cancer controversy until I did
some preliminary reading in preparation for a research grant
application. I got the grant and began my study. I did not at that
stage take vitamin C, although I now do - when I remember to!
I soon narrowed my study down to the cancer debate, which I found the
most sociologically interesting and manageable. I decided on a social
constructivist comparison of the medical evaluations of vitamin C
with those of 5-fluorouracil, a conventional but contentious
cytotoxic drug, and with the putative wonder drug for cancer,
interferon, that was then at the height of its hype. I presented a
first paper on this comparison at our annual professional conference
in Melbourne. The difference between researching issues on which the
dust of history has safely settled and topical disputes was brought
home to me when I was contacted by a reporter for a leading
Australian newspaper. He interviewed me, obtained a copy of my paper,
and published an article on my research (Anon. 1983). I was then
deluged with letters from members of the public (some of whom asked
my advice about their medication), and various alternative
practitioners and megavitamin entrepreneurs, all of whom interpreted
me as supporting a pro-vitamin C position. I was also invited to
write an article for an Australian alternative health journal, which
I declined, as I did not want to jeopardize what I considered to be
my neutral position. The only orthodox professional response I
received was from a Sydney academic oncologist who had not seen the
newspaper article, but who had been given a copy of my paper by one
of his patients. This same oncologist tried, without success, to
interest some of his colleagues in my analysis and to set up a
clinical trial of vitamin C.
I next sent copies of my paper to Linus Pauling and also to the
leading oncologists at the Mayo Clinic who had carried out what was
at that stage the only orthodox trial of vitamin C as a cancer
treatment. This trial had given negative results which were disputed
by Pauling and Ewan Cameron, who was collaborating with Pauling on
the clinical assessment of vitamin C for terminal cancer patients. I
had very cordial replies from both Pauling and Cameron (who was by
then Medical Director of the Linus Pauling Institute at Palo Alto).
Pauling congratulated me on my "fine" paper and offered a few
criticisms of matters of detail and interpretation. He also requested
that I keep him informed of its publication progress, as the Linus
Pauling Institute might want to purchase some reprints for
distribution. Cameron congratulated me for my "very good
understanding" of the machinations of the cancer establishment and
claimed, rather disturbingly, that his interpretation so completely
coincided with mine, that he might have written my paper himself.
My Mayo Clinic correspondents were less encouraging. One of them
professed to find my study "intriguing" and thought that it had
broadened his "keen awareness relative to the impact of socioeconomic
factors on cancer therapies". The other was Charles Moertel,
nationally famous (or infamous if you prefer) for his recent
demolition of laetrile as a cancer treatment as well as of vitamin C.
Moertel pulled no punches in attempting to exercise his cognitive and
social authority over this upstart from Australia. While he thought
that the first part of my analysis was written with admirable style
and considerable objectivity, he claimed that the second part of my
paper (where I dealt with orthodox cancer research and treatment) had
degenerated into a diatribe against the scientific conduct of medical
practice and an endorsement of quacks and charlatans. According to
Moertel, I had misstated and distorted facts and had quoted him out
of context for the purposes of emphasizing my own personal
philosophy. In other words, while he enjoyed reading my relativist
analysis of the socio-economic shaping of the case for vitamin
C, he condemned and rejected my analogous analysis of orthodox
American cancer practices. Moertel claimed that my ringing defence of
Linus Pauling was biased and he demanded correction of this. He
concluded by stressing that he did not authorize my quotation of any
part of his letter. As I was not prepared to rewrite my paper
according to his prescription, I interpreted this letter as
effectively blocking my access to this leading participant in the
controversy.
Up to this point I had relied on published papers and accounts for my
analysis, but in 1984, as a result of my representations, Pauling and
Cameron gave me access to their personal correspondence. I used part
of my research grant to travel to the Linus Pauling Institute, and,
for several months, with only minimal supervision, I ransacked their
extensive files. These contained a wealth of source material,
including not only hundreds of their letters to one another, but also
their correspondence with their leading professional opponents in the
dispute, with editors, research and funding bodies, and their
manuscripts and referee's reports. I was given an office at the
Institute for my personal use, and unrestricted access to a
photocopier. As well, Pauling and Cameron made themselves available
for a number of lengthy separate interviews on this and subsequent
occasions.
By contrast, my attempts to gain access to their orthodox opponents
met with only limited success. The editor of the New England
Journal of Medicine, which published both negative trials of
vitamin C but which had consistently refused to publish Pauling's and
Cameron's papers, refused my request for an interview on the grounds
that he was "too busy". The Director of the National Cancer
Institute, who had engaged in an extensive correspondence with
Pauling over the funding of vitamin C research and the interpretation
of the Mayo Clinic trials, was also too busy for interview. He
arranged for a stand-in who had had only limited involvement in the
controversy, and who gave me one hour of his time and very guarded
information and opinion. My request for access to relevant NCI
documents was restricted to those that I already knew of through my
study of the Pauling files and could specifically request. In short,
I was forced to rely primarily on the Pauling-Cameron files, and on
published material.
This has resulted in a systematic bias in the documentation of the
controversy, although this bias is not necessarily to the advantage
of the vitamin C advocates. Perhaps its most significant implication
is that it lays open to the closest scrutiny the expressed actions,
beliefs and motivations of the supporters of vitamin C, while leaving
those of their opponents undeclared except in so far as they are
willing to represent them to the other side or in published accounts
of their work. The main danger of this situation is that the claims
of those most closely scrutinized may be perceived to be "biased" by
the revelation of the supposedly "non-scientific" factors that have
fed into their assumptions, procedures and presentation of their
work, while those of their opponents remain relatively unscrutinized
and, perhaps, may be presumed freer of such contaminating
influences.
In spite of my best efforts to steer a prudent path through the
minefield of contemporary controversy analysis, I have become an
involuntary participant in the dispute. I have not been able to
dissociate myself from being viewed by the vitamin C advocates as an
ally in their just struggle. Everything I write seems to confirm them
in this opinion.
In 1986 the British journal New Scientist published my account
of the recently concluded and problematic second Mayo Clinic trial of
vitamin C. Pauling had been unable to secure publication of his
criticisms of this trial in the mainstream medical or scientific
literature, so my account was an important vehicle for their
dissemination. As well, my New Scientist article was picked up
and summarized by the American publication Medical Self-Care,
and so made available to the alternative network (Freer 1986). After
this, I found it possible to secure previously inaccessible and
restricted documents and letters via alternative moles at the
National Cancer Institute, the Office of Technology Assessment, and
even the Mayo Clinic.
When I recently returned to the Pauling Institute to update my
material, I found myself and my work entering into Cameron's
applications for NCI grants and his ongoing publication negotiations
with the editor of the New England Journal of Medicine. Pauling cites my work in his public lectures on the Mayo Clinic "fraud", and refers his correspondents to it and to me. My 1988 paper
in Social Studies of Science was viewed as a "scholarly" and
"objective" account by Pauling and Cameron. Although they have not
always agreed with my interpretation of events, I am regarded at the
Linus Pauling Institute as the "official unbiased historian" of the
dispute.
On the other hand, my attempts to elicit some response to my work
from orthodox American oncologists and nutritionists have met with
very little success. Nor, in spite of my representations of their
relevance to the major forthcoming report on the evaluation of
unconventional cancer treatments, was I able to interest the U.S.
Office of Technology Assessment (OTA) in my published analyses of the
vitamin C and cancer controversy. Vitamin C is featured in the OTA
revised draft report as the unconventional treatment to have
undergone the most complete orthodox testing. The detailed discussion
of the Mayo Clinic trials is based on the OTA-commissioned report of
Dr. Jack Yetiv, the author of a book summarizing recent scientific
findings on popular nutritional practices (Yetiv 1986) and a
contributing editor to Nutrition Forum, the leading popular
journal devoted to the exposure of nutritional quackery. In his book,
Yetiv's approach to the vitamin C controversy was the standard
positivist one: that vitamin C has been tested in the two "carefully
performed scientific studies" carried out by the Mayo Clinic, and
that "current evidence clearly suggests that vitamin C has no role in
the treatment of cancer" (1986, 183-4). This same partisan approach
is evident in the section on vitamin C in the OTA draft report, which
gives no coverage to the Pauling-Cameron criticisms of the Mayo
Clinic trials, nor to my own work. As a result of my representations,
I was invited by the OTA to review this draft. My submission opposes
Yetiv's interpretation, and disputes, on sociological grounds, the
lack of symmetry in the OTA draft report.
My position of neutral, symmetrical analysis has led finally to my
active intervention in the dispute. I can only conclude, like Pam and
Brian, that I too have been "captured".
First, sociological studies of
contemporary controversies must be viewed as potential resources in
social struggles over scientific or technical knowledge claims. Our
experiences suggest that, more often than controversy analysts care
to acknowledge, the analyst becomes a participant in what Latour and
Woolgar have very aptly described as the "fierce fight to construct
reality" (Latour and Woolgar, 1979). The analyst is at the front
lines of the battle. It is so easy to be caught in the cross fire
that many prefer to don positivist camouflage and seek shelter in the
best-fortified trench, rather than venture out into the no-man's-land
(which is even more a no-woman's-land) of sustained symmetry. The
combatants have a good deal at stake in the sociologist's
interpretation and presentation of news from the war zone. Their
perceptions of what the analyst is up to, or rather, of what the
analyst should be up to, inevitably enter into the
reconstruction of the story. Both sides to a dispute have opposing
and unshakeable convictions as to who are the heroes and the villains
involved, and where truth and justice lie. If they do not welcome the
analyst's attempt to deal symmetrically with the claims of their
opponents, they may withdraw their cooperation or actively hinder the
study. Alternatively, one side may react more sympathetically to the
analysis, and attempt to win the analyst to their cause.
This leads us to our second conclusion: an epistemologically
symmetrical analysis of a controversy is almost always more useful to
the side with less scientific credibility or cognitive authority. In
other words, epistemological symmetry often leads to social asymmetry
or non-neutrality. The side with fewer scientifically and/or socially
credentialed resources is more likely to attempt to enroll the
researcher, whereas the better credentialed side views an
epistemologically symmetrical analysis as threatening to their
cognitive and social authority, and they are more likely to react to
the analyst with hostility or suspicion. Each case we have discussed
has followed this pattern. We do not consider our experiences to be
unique. Without buying into the boundary dispute between discourse
analysts and Bath relativists, we think that this is precisely what
happened to Collins and Pinch in their study of parapsychology.
Parapsychologists, who lacked the sources of cognitive and social
power available to orthodox scientists, interpreted the symmetrical
analysis of Collins and Pinch as support for their cause and deployed
it in their struggle against the orthodox scientists.
There is no reason to expect that discourse analysts are exempt from
this process. As argued by Doran (1989), the discourse analysts are
subject to the same problems of reflexivity and recursion as the
strong program analysts they criticize. Discourse analysts certainly
have not shown how they might avoid being captives of
controversy.
Our third conclusion is that the intervention by the analyst perturbs
the dispute. Among other problems, this may make it more difficult
for the analyst or other researchers to obtain access to participants
and documents. It is possible, we suggest, for the analyst's "unwitting" intervention significantly to change the course of the
controversy.
So, methodological imperatives to the contrary, the controversy
analyst, wittingly or not, may become a partisan participant in the
debate. The view, raised to a principle in relativist approaches to
controversy analysis, that social researchers must be neutral or
apolitical observers, requires radical reassessment. The political
role of the researcher must also be addressed in any full-blooded
controversy analysis. Our position is that symmetrical analysis is an
illusion: the methodological claim of neutral social analysis is a
myth that can be no more sustained in actual practice than can the
scientist's belief in a universal and efficacious scientific method.
We think that an analytic insistence on the political role of the
analyst cuts through the Gordian knot of the sterile reflexivity
debate.
The irony of our analysis is that the guise of neutrality is one of
the best ways to be an effective partisan. The positivist controversy
analyst, employing a "sociology of error", is an effective supporter
of scientific orthodoxy through stigmatizing its critics; the
relativist analyst, through ostensible symmetry, is an effective
supporter of the critics of orthodoxy by giving them unusual
credence. An active partisan who undertakes either form of analysis
has less credibility than an apparently independent and neutral
person. This is precisely why partisans on one side point to the
analyst, as independent authority, as support for their cause, while
those on the other side try to paint the analyst as not being
independent.
Our analysis fits nicely into the framework of the "weak program of
the sociology of scientific knowledge" as presented by Chubin and
Restivo (1983). The weak program does not distinguish between the
controversy and the analyst: the social scientist is automatically
part of the controversy. The implication is that the analyst is more
than a detached observer: the analyst should be critically involved,
in the role of citizen.
Although the weak program provides a theoretical solution to the
problem of the disjunction between participants and analysts of
controversies, it provides no practical solution to the dilemmas
posed by the prospect of being a captive of controversy. The analyst
may employ a positivist analysis, a strong program analysis, a weak
program analysis, or whatever. But that is simply the analyst's
self-description. The (other) controversy partisans are likely to
ignore motivations and methods and try to enroll, discredit, or
otherwise deal with the analyst as their interests dictate. The
implications of this for the study of controversies remain to be
fully assessed.
1 Some excellent surveys are Engelhardt and Caplan (1987) and Nelkin (1979).
2 Key works in relativist controversy analysis include Collins (1981; 1985), Pickering (1984) and Pinch (1986).
3 For a full account of the history of the laboratory see Scott (1986), or for a shorter version Scott (1988b).
4 For a more detailed discussion see Martin (forthcoming), where the relation between social science work critical of fluoridation and participation in the debate is also discussed.
5 No relation to Brian Martin.
6 For a detailed analysis of the vitamin C and cancer dispute see Richards (1988 and forthcoming).
7 The most notable exception to such positivist orthodox partisanship is Harris Coulter's (1973) scholarly account of the historical conflict between homeopathy and the American Medical Association. Coulter mounted a stinging attack on orthodox drug therapy and claimed that homeopathy was more "scientific" than the former.
8 In their most recent account of the laetrile controversy, Markle and Petersen (1987) are less cautious in their dissection of the role of orthodoxy in the conflict. It remains to be seen how this more critical account is viewed by orthodoxy.
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