  |
|
|
|
|
|||
| Journal of the New Zealand Medical Association,
06-August-2004, Vol 117 No 1199
|
|||
|
‘All about research’—looking back at the
1987 Cervical Cancer Inquiry
Barbara Heslop
Every year on August 5, members of the Auckland
Women’s Health Council gather in the grounds of National Women’s
Hospital to commemorate the anniversary of the release of the Cartwright Report
and to remember the women who died as a result of the ‘unfortunate
experiment’.
The Council’s newsletter pages http://homepages.ihug.co.nz/~awhc/newslett.htm
have this to say (February 2004):
‘In
more recent years we have also remembered others – in 1999 the premature
babies who were part of the chest tapping physiotherapy at the hospital, and in
2000 the women of Gisborne. Last year, a wreath of yellow daffodils was placed
around the statue to acknowledge the Gisborne women whose lives were lost or
damaged as a result of a cervical screening programme—which did not do
what it was set up to do...
‘Following the ceremony in
front of the statue, the party walked around the back of the hospital to a
pohutukawa tree marked by a plaque, which was laid in 1993 in memory of Dr Bill
McIndoe, cytologist and colposcopist at the hospital from 1963–1983; and
Dr Malcolm McLean, pathologist at the hospital from 1961–1988. The tree
and plaque were placed beside a path in the hospital grounds near what used to
be the Colposcopy Cinic where Dr McIndoe worked and was overlooked by Dr
McLean's Pathology Laboratory...
‘...the Inquiry itself and
the subsequent Report marked the end of an era of medical paternalism and
arrogance which was allowed to reign unchecked.’
My knowledge of the Auckland Women’s Health Council
derives from its webpages. Apart from the fact that I live at the other end of
the country, my medical academic background gives me a somewhat different
perspective of the events commemorated by the Auckland Women’s Health
Council.
The Cartwright report, of course, recorded the findings of
the Cervical Cancer Inquiry held in 1987. Specifically this inquiry related to
the circumstances surrounding an unorthodox approach to treating cervical
dysplasia and carcinoma at National Women's Hospital (NWH) in Auckland by Dr G H
(Herb) Green. A professional paper (Obstet.Gynecol.1984; 64:451-458) published
after Green’s retirement by NWH staff members (pathologist Malcolm [Jock]
McLean, colposcopist and cytologist Bill McIndoe, and others), discussed the
outcome of Green’s management of his patients. This paper was brought to
the notice of Sandra Coney and Phillida Bunkle, who in 1987 published an article
in Metro magazine entitled
An ‘Unfortunate Experiment’ at
National Women’s, which eventually led to the official inquiry
chaired by Judge (later Dame) Silvia Cartwright in 1987. The official report of
the Inquiry, issued in 1988, is the report to which I refer below.
A couple of years ago, I found myself discussing the
Cervical Cancer Inquiry with a group of 3rd
year medical students in Dunedin. At the time when the Inquiry was held, most of
these students would have been 5 or 6 years old. Between 1999 and 2002, I had
returned to the university (teaching pathology to 2nd and 3rd year medical
students) as a retired staff member helping out temporarily during a staffing
crisis.
The third year of the medical course in Dunedin has for the
last few years included a session that I first encountered in the student
programme as ‘Integrative Day – Cartwright’. As a graduate
from a different era, the ‘Patient Doctor and Society’ part of the
course, in which this session figured, was new to me. So ‘what was the
Cartwright session about?’ I asked my student group (because at that stage
they would have known little about cervical carcinoma). ‘It was all about
research,’ was the reply.
I thought that I knew a little about medical research. Apart
from directing my own transplantation immunology research group for several
years, I had been a member of a couple of the first assessing committees when
peer-review assessment was instituted by the Medical Research Council (MRC) in
the early 1970s, and I had later (for several years) chaired the National
Scientific Committee of the Cancer Society of NZ, which at the time funded most
of the country's cancer research. I also knew a bit about histopathology, one of
the ‘bones of contention’ at the Cervical Cancer Inquiry—in
fact, I had done nothing else for a period of 8 years in New Zealand and
London.
Despite the extensive nature of the investigation, it had
always seemed to me that parts of the
research side of the picture were
missing. I doubt whether filling the relevant scientific gaps would necessarily
have made much difference to the recommendations of the Inquiry. But the missing
information might have explained the apparent lack of intellectual
sophistication that not only allowed the ‘unfortunate experiment’ to
get started in the first place, but also prevented it from being terminated much
earlier than it was. Conceivably, it might have tempered some of the opprobrium
to which Herb Green—seemingly a bewildered old man at the time of the
inquiry—was subjected. But by the same token, it would also have asked why
the pathologist and colposcopist took so many years to make a point that they
were probably very well placed to make much earlier.
I have taken the opportunity to look at the New Zealand
medical research scene in the 1950s–1970s because, although these were
very exciting years for biologists, at the same time a lot of medical research,
and especially clinical research, was relatively unsophisticated and
unstructured. A substantial re-appraisal of research methodology followed the
introduction of formal peer-review by the Medical Research Council in the early
1970s. Scientific assessment became a very different procedure from some of the
so-called review processes that had operated previously. Knowledge of the basic
biological processes that underlie disease was very limited in the 1950s and
1960s, relative to the huge expansion that was to come, and this was reflected
in much of the research that was carried out at that time. So the session that
my students had reported as being ‘all about research’ concerned an
event that I had always seen as thin on the scientific side. I was more inclined
to interpret it as being ‘all about peer review’, and to an even
larger extent—embarrassingly—it was ‘all about some of the
ignorance and intellectual naivety of a previous age’.
Terminology—In
talking about cervical lesions, I'll use the simpler terminology of today's
undergraduate pathology classes—ie, dysplasia for all the relevant
non-invasive lesions of the cervix, and carcinoma (or cancer) for the invasive
lesions. Since the hallmark of malignancy (cancer) is invasive growth, unless I
am quoting others, I'll avoid using that contradictory term carcinoma
in situ—CIS (‘a cancer
lacking the hallmark of cancer’), and call it severe dysplasia instead.
Today’s model of neoplastic (tumour) growth has been
around since the mid 1980s. It views all the relevant cervical lesions as
resulting from a series of genetic mutations, whose occurrence lacks any
consistent pattern—hence the clinical variability. The mutations affect a
wide assortment of genes, which in their normal (unmutated) state mostly control
cell growth. Invasion supervenes when a set of mutations (the ‘metastatic
cascade’) provides the altered cells with the biological ‘know
how’ to travel beyond their normal confines. The early mutations, whose
occurrence is reflected in the cytological features of dysplasia, increase the
probability of further mutations, including the potentially lethal
‘metastatic cascade’. Dysplasia can, nevertheless, persist for many
years without supervention of the ‘metastatic cascade’.
The above conceptual framework of neoplasia (see
Scientific American July 2003, for a
brief account) does much to explain the variable and unpredictable relation
between dysplasia and invasive cancer. The model was in its very early days at
the time when Herb Green retired. I mention it here because those people
re-reading the report of the Inquiry may find it easier to think along these
lines than to get too enmeshed in the different (and often confusing and
contradictory) terminologies prevailing at the time of the Inquiry.
Medical research between 1950 and the mid-1970sI’ll start by considering the
background against which this all occurred. I qualified in medicine in 1948
– three years after Herb Green, and in the same year as Malcolm (Jock)
McLean. Bill McIndoe graduated shortly after this. We were all students of Sir
Charles Hercus, for whom the promotion of research in the Otago Medical School
was a mission. The extent to which he succeeded was summarised by Prof John
Ludbrook, an Otago graduate working in Australia, in his article written on the
occasion of the Medical School centenary in 1975 (N Z Med J.
1975;81(533):133–4). Not surprisingly in this environment, all members of
staff and all aspiring academics were encouraged to become involved in research.
This was fine—if you had any idea how to
go about it. Most of us did not.
Research training: then and
now—Today's intending medical researchers are usually enrolled for
a research degree, and have mentors and official supervisors. The problems to be
investigated and the students' approach to them will be approved before they
start, and monitored along the way. Research trainees will learn how to test a
scientific hypothesis, how to present their findings, and how to defend their
conclusions in the face of possible criticism. Only a little of this sort of
training was available at undergraduate level in our day, and only in the
medical sciences. Not surprisingly, most students of our vintage graduated with
major scientific deficiencies. How well we made good the deficiencies probably
depended on how quickly we identified them. There was often an element of luck
in this—it depended on our chosen fields, what we read, who were our
seniors and mentors, and to some extent on chance encounters.
Human biology on the eve of
the golden age—By today’s standards, the general public in
the 1940s and 1950s was almost unbelievably ignorant of human biology. Virtually
no biological sciences were taught in secondary schools; what there was,
consisted mostly of botany taught in a few girls’ schools. Polite
conversation was delicately non-specific about biological topics, and this vague
gentility served to perpetuate the underlying ignorance. Thus, the Auckland
newspapers during the war referred to ‘social diseases’ for what we
would now call ‘sexually transmitted diseases’. Needless to say,
there was no sex education in schools at any level. At university in Dunedin in
the 1940s, the annual lecture to 5th year medical students on contraception was
crowded with students from other faculties. Among many of the general public,
bowel diseases and cancer were scarcely mentionable.
Against this social background, those who were familiar with
anatomy, physiology. and pathology spoke a different language from those who
were not. This partly accounts for some of the medical paternalism and
condescension of the time, although it hardly excuses its grosser
manifestations. Of all people, the distinguished biologist JBS Haldane
(described by Nobel laureate Peter Medawar as ‘In some respects ... the
cleverest man I ever knew’) was not told by his London surgeon about the
spread of his cancer—an omission that had significant effects on his
subsequent plans. His sister, writer Naomi Mitchison, duly complained to the
British Medical Journal about this (see
JBS. The Life and Work of JBS Haldane
by Ronald Clark; Oxford University Press, 1984).
Quite apart from doctors’ attitudes to
‘telling’ or ‘not telling’ (which varied among my
contemporaries), withholding bad news was often viewed as kindness. Margaret
Forster’s Good Wives? (Vintage,
2002) describes the measures taken in his own household in the 1960s to keep
Aneurin Bevan, architect of the British National Health Service, from finding
out that he was dying of cancer. Arrogance and paternalism? Sometimes, but these
accusations need to be considered in the context of their day.
Experimentation and the
golden age of biology—The 30 or so years after the war saw the dawn
of the current golden age of biology, with DNA as its incomparable opening
fanfare in 1953. On the medical scene, antibiotics and better anaesthesia opened
the door to procedures that had previously seemed impossible. Thus, the postwar
years were a time of unprecedented medical experimentation. A vivid account of
the medical research climate then and now, and of the spectacular advances that
were achieved at great cost, can be found in the obituary of Francis D. Moore,
one of America’s major players—perhaps
the major player—in the surgical
dramas of those times (New Yorker, May
5 2003). The obituary goes on to describe the complete change in his attitude in
the 1970s. To some extent, this attitudinal change reflected a worldwide
zeitgeist—triggered by revulsion
at the human experimentation carried out in Hitler’s Germany, and revealed
at the end of the war.
But the scrutiny was not restricted to clinical
experimentation—it came to extend to virtually all aspects of medical
practice. I mention the Francis Moore obituary here, because the same climate
change (albeit a little later in arriving) took place in New Zealand.
New Zealanders as research
‘loners’—A significant, and probably increasing,
proportion of today’s clinical research is done by large multidisciplinary
teams and multinational collaborative programmes. The situation in New Zealand
in the 1950s–1970s, and especially in clinical research, was the exact
opposite. Whether they wanted to or not, medical researchers often found
themselves working alone. Today’s communications (eg, fax, email,
internet) did not exist. Geographic isolation and the cost of overseas travel
added to the isolation. Medical scientists were slightly better off than
clinicians. They usually worked in university departments, and their juniors
were likely to be research students. The corresponding juniors in hospitals were
mainly studying for specialist college qualifications and were often not
particularly interested in research. For those who have to work alone, informed
argument and criticism become luxuries, when in reality they are necessities.
Collections as clinical researchClinicians looking for research
projects during the years 1950–1970 could find it hard to get started, and
they often ended up working on their own. One option was to study as many
examples as possible of a given disease or procedure. In the first instance,
this might entail accessing the hospital records and ‘taking out’
all the relevant cases.
Later on, with growing clinical experience, and perhaps with
a published analysis of the records, it might be possible to attain some local
standing as an expert. It was easy enough to keep adding to the collection as
cases became available, and to examine different aspects of the relevant topic,
including the effects of different treatments. These studies were unlikely to
have been designed as experiments, but were more in the nature of ‘wait
and see what crops up and then write it up’. A new treatment in those days
would have been seen as an extension of the therapeutic armamentarium rather
than as an experiment.
The publications arising from a clinical collection were, of
course, retrospective analyses. They had the shortcomings that go with this
approach—especially the variability of the data and the difficulty of
making comparisons. These faults were not always appreciated in the 1950s and
1960s, when some substantial research reputations were built up in this way.
Publications arising from large collections of cases usually conferred some
local cachet on the author, and an international specialist journal carried more
clout than a New Zealand journal.
Indeed, getting published in an overseas journal was
sometimes equated with having ‘an international reputation’. Once
the writer had attained this status, referrals were likely to increase, and with
any luck his (in those years it was seldom her) collection would snowball. By
this stage, his opinion was seldom challenged. The main difference between the
collector and his non-collecting colleagues lay in the propensity of the
collector to collate his results for publication.
As far as I am concerned,
Herb Green’s research was an ongoing collection of clinical cases.
In asking his colleagues in 1966 to refer patients, he clearly had to tell them
why, so he presented the relevant staff meeting with an overview of what he
proposed to do. Managing these patients was always going to entail an element of
‘playing it by ear’—so it is quite conceivable that there
never was a detailed experimental plan of action, of the kind that we would
expect today. The proposal ostensibly related to an alternative treatment plan,
and was probably seen at the time as no more than an extension to Green’s
therapeutic repertoire. For many doctors, trying out a new treatment that they
had read about, or offering a new skill that they had acquired while on study
leave overseas, was simply part of keeping up with things. Nevertheless, the
observations accumulated by a clinical collector were almost certainly destined
to be collated and published as a retrospective analysis, which would
ultimately, at least in a teaching hospital, find its way into the departmental
annual report as research. Doctors undertaking similar procedures without
publishing their findings were unlikely to get mentioned in research reports.
Ostensibly, they did not do research. We would look at things differently today,
but that was how it was in the 1960s.
There is nothing wrong with amassing a collection of cases.
People with a special interest in a given condition will tend to do this, and
will often be extremely well-informed and highly experienced practitioners.
Indeed, even retrospective observational research (the clinical descriptions of
SARS, for instance) can still be very useful. But for the most part, by the
1960s and 1970s, large-scale retrospective analyses had had their day
as research projects. There were better
ways of collecting and presenting data. By the early 1970s, it would have been
almost impossible to submit an ongoing collection as a research proposal using
the format introduced by the MRC (Medical Research Council—currently the
Health Research Council).
Some scientific questions about Herb Green's researchI now consider some of the
scientific aspects of Herb Green’s research. The Cervical Cancer Inquiry
took place in 1987 and related to clinical and histological investigations,
which had had their origin a generation earlier. My familiarity with both
research generations prompted me to ask four questions relating not only to the
science of the period, but also to the understanding of some of the science,
which I suspect to have been rather less than was assumed at the Inquiry.
Proving a
hypothesis?—I am almost certain that Herb Green did not know that
that a scientific hypothesis has to be falsifiable. After reading the report of
the Inquiry, and also Sandra Coney’s book
(The Unfortunate Experiment;
Penguin,1988) which provides some additional transcripts from the
Inquiry), I concluded that only a small minority of the
New Zealand players in this drama (the
epidemiologists) clearly indicated that they knew this. The references in the
Inquiry to proving a hypothesis left me feeling very uneasy about the level of
understanding of many of the other participants.
The word
‘hypothesis’ is often used
by all of us to mean no more than ‘a sort of idea’. Strict
scientific usage requires that a hypothesis be
testable and
falsifiable. Indeed, in
contradistinction to what is widely assumed, a scientific hypothesis
cannot be proved. At best, one can
obtain evidence that is consistent with it. This information is sufficiently
basic to figure in today’s secondary school biology syllabus (and it
certainly did not figure in secondary school science in the 1930s and 1940s).
Thus, Herb Green's aim of proving that cervical dysplasia does not lead to
invasive cancer should have entailed
falsifying this contention. This should
not have taken very long—whatever time it took to record the first case of
invasive cancer.
I have read and re-read the relevant pages of the report of
the Inquiry trying to ascertain whether Herb Green knew this. All the evidence
leads me to conclude that he did not. This sort of misconception can be sorted
out quite easily in an informal student class, or at a departmental seminar, but
it can cause enormous difficulty in the context of a formal inquiry, when not
only is it central to the whole investigation, but when it is not officially
identified as a problem.
Thus, while Prof David Skegg
(Report of the Inquiry, pp32–33)
commented on the inconsistencies in Green’s approach, had his
investigation been set up with the aim of disproving a hypothesis, I suggest
that Green himself never knew that he was supposed to be falsifying anything.
Rather, I think that he intended to accumulate a large series of cases in which
dysplasia had persisted for years without malignant transformation, and in due
course to record his observations retrospectively.
If I am correct, Herb Green would probably not have
appreciated the points made by David Skegg at the Inquiry about falsification.
Furthermore, he (and ? his chief Prof Bonham) could have been bamboozled by the
discussion of whether the word
‘invariably’ had been used
in relation to the proposal that he submitted to the medical staff in 1966. A
few years later, such a misconception might have become apparent during the
course of MRC scientific assessment.
Pre-cancerous conditions (of which cervical dysplasia is one
of many) increase the likelihood of developing a specified type of cancer. The
concept is statistical—it is a matter of probabilities. As Kolstad
indicates (Report of the Inquiry, p23),
the evidence that supports classifying a condition as pre-cancerous, is
circumstantial. We do not usually expect to observe the actual transformation of
the original lesion into a cancer.
Herb Green aimed to ‘prove’ his hypothesis by
carefully observing that dysplasia did not lead to cancer—and that was how
it was presented to the medical staff in 1966. Unfortunately, the proposed
methodology was equally appropriate for showing that dysplasia did lead to
cancer. Paradoxically, and I am sure unintentionally, he ended up demonstrating
(via the paper by McIndoe et al in 1984;
Report of the Inquiry, Appendix 7) more
convincingly than had been done before, the transition of dysplasia to cancer. I
do not for a moment think that any group of New Zealand doctors would ever have
condoned a clinical management plan that entailed watching cancers develop.
Those attending the 1966 meeting at NWH simply did not see the proposal for what
it was.
If Herb Green was under a misapprehension about scientific
hypotheses, I doubt whether too many of his NWH clinical colleagues were any
better informed. None of the medical staff seemed to see that the whole approach
to Green’s hypothesis was ‘back to front’, as it were. A
misconception like this, if it occurred, is no more than a commentary on the
general state of scientific sophistication of those people at that time. Most of
the clinical medical staff would, after all, have had little reason to ponder
over the formal approach to a scientific hypothesis. This involves a mind-set
rather different from that of routine clinical practice, and certainly different
from that usually prevailing at staff meetings with multiple agenda items.
To those inclined to say ‘they should have seen it for
what it was!’, I agree that it would have saved all sorts of trouble.
Nevertheless, over 20 years later, comparable scientific shortcomings appeared
to be widespread at the Cervical Cancer Inquiry. (Otherwise, why did nobody
seize upon the points raised by David Skegg, and ask whether the NWH approach
was an appropriate way of dealing with a scientific hypothesis?)
The medical staff, and particularly Herb Green, have been
accused of all sorts of arrogance in rejecting criticism. Whatever part the
personalities of all the participants in the Inquiry did, or did not, play, the
lack of scientific sophistication—in my opinion the central
problem—had its genesis in ignorance rather than arrogance.
There is a certain piquancy in noting that Karl Popper, the
distinguished philosopher who established that a scientific hypothesis should be
falsifiable, was working in Christchurch at the time when most of us were
students. Physiologist Prof J C Eccles (a future Nobel laureate) invited him to
Dunedin to speak in his department.
Making predictions from
hypotheses—Also apropos of scientific hypotheses, I wondered
whether anybody at NWH in the 1960s and 1970s realised that a scientific
hypothesis should generate predictions?
Herb Green had hypothesised that severe dysplasia was a different disease entity
from invasive cancer.
If this were so, it could have been predicted not only that:
Therefore, I wondered whether Herb
Green's hypothesis might not have been approached from the ‘other end of
the disease spectrum’ by attempting to falsify prediction (b) above?
Herb Green is said to have regularly disparaged the
specialist opinion of histopathologist Jock McLean. Most pathologists subjected
to this sort of thing would have been hopping mad. But viewed from afar, it is
pertinent to ask whether Herb Green might have done this simply because he
belonged to that group of aggressive players who rather enjoy ‘trading
intellectual punches’? Might it have been possible to beat an aggressive
Herb Green at his own game? I think so.
The falsification of the prediction that cancer could occur
on its own without severe dysplasia would have dealt a mortal blow to
Green’s hypothesis. A purely histopathological investigation into which no
clinical input was required, need not have involved Herb Green at all, so the
exercise could have been free of verbal punch-ups. As long as the hospital had
retained its hysterectomy specimens (and most hospitals would have done so in
those days), it should not have taken too long to answer the question:
How frequently is unequivocal invasive cancer
accompanied by severe dysplasia in the adjacent cervical epithelium?
The two pathological lesions were already known to be
associated—indeed, Jock McLean himself referred to NWH material showing
the association (Report of the Inquiry,
p76). More information was needed from the NWH cases on
how often dysplasia accompanied
cervical cancer. The existing literature already hinted at a figure not too far
from 100% (references cited in the 2nd edition of R A Willis’s
Pathology of Tumours (Butterworth,
1953—the virtual bible on neoplasia in its day). The demonstration that
invasive cancer did not occur in the absence of severe dysplasia of the adjacent
epithelium could have provided compelling evidence that the two lesions were
related.
Such an investigation should not have been too difficult to
carry out. With any luck, most of the relevant information would have been
available on existing slides without calling for the preparation of more
sections. Even at the slow rate of one specimen examined in detail each day, it
would not have taken long to accumulate results from, say, 50 consecutive cases
of cervical cancer. The findings would almost certainly have been publishable in
a peer-reviewed international pathology journal. With suitable high-quality
photomicrographs to illustrate the basis of the diagnoses, the conclusions would
have been open to scrutiny by all, and could have supplied a reference point
against which future discussions of this contentious project were considered.
Once the information had been published, it would have been irrelevant whether
Herb Green believed the results.
So why was it not done? I don't know, but my guess is that
(like Herb Green) Bill McIndoe and Jock McLean had not given much serious
thought to scientific hypotheses. It was a missed opportunity, but it could
hardly be called anybody's fault.
A Eureka
experience?—My next question concerns the origin of the hypothesis
which Herb Green set out to prove, and to which he adhered so tenaciously. I was
looking for the sort of information that in later years would have appeared in
the Justification section of a standard research grant application—a
detailed account of the evidence that led him to believe that some of the
histological changes interpreted by most pathologists as being sinister were, in
fact, innocuous. Epithelial dysplasia elsewhere in the body (mouth, skin, colon,
for instance) has for a long time been regarded as pre-cancerous, although in
some situations, many years can elapse before a cancer develops. Indeed, it may
never do so. Green had, of course, already had a patient with a high-grade smear
who had refused treatment, and who had nevertheless survived for many years in
good health. He was no doubt acquainted with the slow progression rate of some
other dysplastic lesions. A comparable behaviour pattern of cervical dysplastic
lesions might offer a potential rationale for avoiding hysterectomies.
Green’s postulate that cervical dysplasia was
relatively innocuous was, of course, ultimately going to require an answer to
the question: ‘If it is not a
pre-cancerous lesion, what is it?’ I suggest that Green had a
pretty good idea of what the lesion was, but that his interpretation was wrong.
He knew that histological sections of the foetal cervix often showed lesions
very similar to adult cervical dysplasia and cancer. Thus, he argued that
dysplasia in the adult might represent
persistence of a foetal structure. And
because the foetal lesion clearly did not lead to cervical cancer in childhood
or adolescence, he deduced that the adult lesion was therefore less dangerous
than conventional gynaecological wisdom deemed it to be. This interpretation
accords with several pieces of evidence from the inquiry:
Paragraph 1 on p34 of the Report quotes Herb Green as
saying,
‘Around about 1963 I
thought of the possibility that abnormal cytology in women later developing CIS
(= carcinoma in situ or severe
dysplasia) or cancer may have been present at birth: this was because many
pathologists and clinicians whom I consulted, diagnosed dysplasia or CIS in
autopsy specimens of cervixes of stillborn infants’
It was an unusual idea, which should have provoked all sorts
of discussion about the validity of the interpretation. It called for a
contribution from histopathologists who had had experience with foetal and
neonatal tissues, and possibly also from a developmental biologist.
Unfortunately, New Zealand had not too many of these people at the time. Thus, I
was curious about the identity of the ‘many pathologists and
clinicians’ said to have made the diagnosis. Not many autopsies are
normally carried out on stillborn babies. Nor are many histopathologists very
interested in examining the foetal cervix. Anyway, whatever Herb Green had seen
in the tissue sections no doubt prompted him in 1963 to start looking for the
corresponding ‘abnormal cells’ in vaginal smears from newborns. No
abnormal cells were found in the smears. The intellectual isolation of the day
meant that (as far as I can tell) nobody asked the important question
‘Why not?’ It might have
led to a more critical appraisal of the tissue sections.
If the neonatal smears were uninformative, the evidence from
the tissue sections remained important. At least two patients in the 1966 series
(Report of the Inquiry, p33) were told
about it:
Patient
code 4F1: ‘He (Dr Green) told me that there was 9 out of 10 women
have cancer and he said that in my case, if I went to my normal GP they would
panic.... They would be rushing me into hospital.... and he says in cases like
that, it does lie dormant.... ‘
Patient code
4S: ‘Every person is normally born with cancer, but it is the type
of cancer that is dormant....He said sometimes it just flares up every now and
then.....’
Although patients’ recollections are prone to
inaccuracy, I doubt if two people could independently have come up with the same
very unusual story that ‘we all have cancer but it lies dormant’,
had they not actually heard something very like it.
As late as 1979, Herb Green noted (in N Z Med J.
1979;89(629):89–91):
‘Some observations (unpublished) by the present
author on the histological features of the cervical epithelium of infants dying
at or around term have shown appearances which some pathologists (without
knowing the source of the material) have been prepared to describe as at least
dysplastic if not neoplastic’.
Oddly, and tantalisingly, Herb Green did not publish any
representative photomicrographs. Inexplicably in the circumstances, nor did
anybody else at NWH seem to make a point by referring to photomicrographs. Yet
they were at the time easily obtainable. So we are left guessing what Herb Green
had seen in the foetal cervix. I suggest that he almost certainly saw the early
phases of squamous metaplasia— a
benign but actively developing lesion, occurring at a time when the foetal
cervix was already engaged in the normal growth spurt that occurs before birth.
The process is described in some detail in Yao S Fu’s
Pathology of the Uterine Cervix, Vagina and
Vulva 2nd edition (Saunders, 2002). Metaplasia involves the conversion of
one type of epithelium into another and is fairly common in the cervix from late
foetal life to the 8th decade. While Herb Green was no doubt very familiar with
its adult manifestation, in which the
mature squamous cells are easy to recognise, the immature cells in the early
stages of the foetal lesion are a more difficult diagnostic problem. Indeed, as
Yao Fu points out (Figs 2-22 and 2-23) the appearances
superficially resemble the lesions seen
in adult cervical dysplasia, or even invasive cancer, for which they can be
mistaken.
Thus, I suggest that Herb Green’s ‘dormant
cancer’ idea stemmed from his failure to realise that metaplasia in the
foetus was a different lesion from adult cervical dysplasia. From his 1979
comment (above), it appears that he was not alone in thinking this. Yao
Fu’s photomicrographs, incidentally, probably explain why Green failed to
identify ‘abnormal’ cells in vaginal smears from neonates –
the relevant cells were deeply situated, and would not have been detached during
the preparation of the smears.
It is easy enough to be disdainful of this whole idea today,
especially with the advantage of being able to view things within the conceptual
framework of the current model of neoplastic growth (which has dysplasia a few
mutations away from cancer). This was not possible in the 1960s, when
Green’s ideas would have looked considerably less ‘way out’
than they do today. Nothing highlights the downside of intellectual isolation
more tellingly than this story. Indeed, his hypothesis should have brought the
devil’s advocates out of their laboratories.
Instead, apart from some unidentified pathologists, who did
not know the source of the material (referred to in his 1979 publication), the
only record of any communication seems to have been with a couple of patients.
Anybody who has worked in isolation will know how easy it is to become devoted
to a misconception, especially if it has involved something of a Eureka
experience—one of those ‘highs’ that reward researchers for
having what at the time seems to be a great idea.
Notwithstanding the intellectual isolation in which Herb
Green worked, it remains a mystery to me why none of his colleagues were
acquainted with the ‘dormant cancer’ idea.
Was it because he was better informed than his colleagues on
cervical histopathology, so did not bother to discuss it with them?
Maybe there is a grain of truth in all these
possible explanations.
Scientific peer review:
then and now—The inquiry raised the subject of inadequate peer
review on several occasions but was vague not only about the
process, but more importantly about who
should be doing the reviewing and when. The expectation that Herb Green’s
clinical colleagues had the know-how to evaluate some
scientific aspects of his contentious
investigation was, I think, unrealistic. Scientific assessment underwent a
radical change in New Zealand during the early 1970s. For all practical
purposes, New Zealand adopted international practice. Something very different
had obtained before this.
The apparent lack of understanding of the process of
scientific peer review, and what it entailed over the relevant period, was a gap
in the Inquiry as far as I was concerned.
To provide a standard against which to consider the
so-called assessment carried out in 1966, it is useful to outline the process
set up by the Medical Research Council in the early 1970s. This represented the
country’s first attempt at
systematic scientific review. Research
proposals were submitted in a standard format that basically asked what was
being done, why it was being done, how it was to be done, what staff were
involved, whether their qualifications were appropriate, what benefits were
likely to accrue from the study, how long it was likely to take, what it was
going to cost, and so on. Furthermore, a proposal was typically supported by
up-to-date references from the relevant literature.
All the MRC committee members were experienced researchers.
A research proposal was first considered by two committee members who provided
preliminary written reports. In the general discussion that followed, all the
other committee members commented individually, and the opinions of national
and/or international referees were made available. A numerical score, using the
designated MRC scale, was finally assigned privately by each member. Neither the
applicant for a grant, nor any of his/her associates, was ever present in the
room while the proposal was being discussed.
Within the limits of what is possible in a small country,
the members of the four committees were selected for their knowledge of a given
field. Thus, a molecular biologist would not usually be a member of the clinical
committee, and vice versa. Reviewing a grant application could be time-consuming
if it called for ‘nitpicking’ checking of data or journal
references, or if it entailed writing a balanced report on a contentious
application. Formal assessment of this type is simply not the business of the
usual medical staff meeting.
Research funding organisations such as Cancer Society,
National Heart Foundation, Neurological Foundation, Arthritis Foundation, and so
on, subsequently adopted the MRC format. Most of the funding for university and
hospital biomedical research has (for many years) come from the above
sources—so for the last 25–30 years, it has been almost impossible
to gain a significant research grant without submitting an application along
these lines.
In a recent (2003) personal communication, Jim Hodge
(formerly Director of the MRC) who instituted this assessment process,
commented:
‘In retrospect, I think the
most important thing that I did during my time with the MRC was to persuade (?
force) the council to adopt a proper peer review system. The members had naively
assumed that appointing a professional as Chief Executive Officer would solve
all their problems of assessment of research quality; and it took some time and
effort to persuade them otherwise.’
It was a hugely important move and changed New Zealand
medical research irrevocably for the better.
Scientific peer review
pre-1970s—Prior to the institution of individual project grants,
the MRC used to provide block grants to academic departments, the disbursement
of which was the responsibility of the departmental head. Such peer review as
there was at the time, took place at departmental seminars or institutional
research meetings, at national and international meetings, and finally when the
work was published.
For an individual researcher, the extent of the peer review
was apt to be variable, and depended on the culture of the department or
institution. Medical sciences departments were more likely than clinical
departments to hold regular research meetings, and junior scientists were
usually more likely than junior clinicians to argue with their seniors.
When individual project grant applications replaced most of
the departmental block grants in the early 1970s, preparing a formal application
turned out to be a much more demanding task than contributing a section of the
departmental annual report, which had until then constituted the main
communication with the MRC for those of us who were not departmental heads. The
informed national and international criticism to which most of us were now to be
individually subjected (via our grant applications) no doubt sharpened our
intellectual faculties more effectively than almost any other relatively simple
administrative change could have done.
Herb Green and the Medical
Research Council?—It seems almost certain that Herb Green’s
research was never submitted for assessment by the MRC. Amassing a collection of
cases costs nothing, so there is no need to apply for financial support. The
former Director of the MRC (Jim Hodge) and Deputy Director (Colin Geary) have
both confirmed that Green never held an individual project grant from the MRC
(personal communications 2003). His work had started in the days when funding
was via departmental block grants, and Green did figure as an associated
investigator, and later as a principal investigator, in some of the annual
reports to the MRC provided by Prof Bonham.
All departmental research activity was apt to find its way
into the annual reports, irrespective of whether it had used MRC funds. Although
Herb Green’s research was said to have been ongoing, his name appeared in
some annual reports but not in others. Indeed, in the personal communications
(2003) referred to above, neither Jim Hodge nor Colin Geary is certain why the
Inquiry (p64) reported that Herb Green’s research was assessed by the MRC
in 1982. Since he did not hold a grant, the MRC would have had no reason to
assess his work.
Our theories may be wrong
but our data must be right—Some of the data relating to the
Cervical Cancer Inquiry leave me feeling uneasy—at least from this
distance. For at least some of the time period covered by the investigation, it
appears that for a number of patients, two different histological diagnoses
(McLean, Green) had been made on the basis of the same cervical lesion. The
in-house investigation undertaken at NWH in 1975 had its origin in a conflict
about these histological diagnoses. So who made the definitive diagnosis? When?
Which diagnosis is in the hospital records? When did it get there? And which one
appeared in those hospital records that were examined in 1975 by the in-house
investigating committee (Drs Macfarlane, Faris and Seddon)?
Since the inquiry recorded that the in-house committee of
investigation had no terms of reference, what did its members know about the
histological disagreement and the memos relating to it? Did the differences of
pathological opinion involve only dithering on the basement membrane—ie,
the decision on whether there was micro-invasion. (This is a comparable problem
to the harder ‘run out’ decisions by the
3rd umpire in cricket. It concerns difficult
borderline situations open to differences of opinion.) Or did it involve major
diagnostic disagreements?
The absence of photomicrographs in a couple of situations
that seemed to be calling out for them is strange. For histopathologists, they
exemplify the aphorism that one picture is worth 1000 words. One photomicrograph
with an arrow pointing to the lesion of interest, and accompanied by the
caption: ‘The arrow marks the lesion interpreted by A as ... and by B as
...’ would have been more effective than a dossier of memos.
Photomicrographs were easy enough to obtain in the 1960s and 1970s, so why did
nobody bother?
Maybe it is possible to resolve the data about which I feel
uneasy into a set of clear unequivocal results. But that calls for better access
to the data than I have.
For my former student group—the salient pointsMy students are supposed to leave
class armed with the salient points of the topic under discussion. So the
scientific pieces that were missing from their ‘all about research’
session go something like this:
Some more treesComing back to the tree at National
Women's Hospital: Trees are lovely things—we should plant more of them.
I'd plant one to remind an institution that suffered as a result of the inquiry,
that it has hosted some of the country's top biomedical scientists.
Indeed, I’d add another tree to thank all the
staff—yesterday’s and today’s—for caring for thousands
of patients over the years. Hospitals are safer places when they retain some
esprit de corps, and when the staff can
feel that their work is appreciated.
And please, a tree to remind everybody that Jim Hodge
instituted the sort of peer-review assessment that halted inferior
investigations before they got off the ground—a system that all the larger
research funding organisations in the country duly copied a few years later. I
am keen on this tree because many people in this country give generously to
medical research. I would hate them to think that we are not deadly serious
about what we do with their money. Also apropos of scientific peer-review
assessment, another tree would acknowledge the overseas experts who review this
country's grant applications. They work behind the scenes and give of their time
and expertise for nothing.
Somewhere in this grove I’d like to record two
comments on research. Specifically, and in relation to medicine, clinical
research is undertaken simply because the current diagnosis and/or treatment are
not good enough. In a more general sense, we should carve the message into stone
that it was research—finding out—that brought our ancestors out of
caves.
A final questionWe teach our pathology students
that in biology, as elsewhere, ‘there is no such thing as a free
lunch’. Thus, an account of a vitally important process like inflammation
always comes with the questions: What harm does it do, and what does it cost?
Turning to the Cervical Cancer Inquiry, undoubtedly it righted some wrongs. But
what harm did it do, and what did it cost? Perhaps 16 years is long enough after
the event for somebody (who knows more that I do about the current O&G
scene) to scan the balance sheet dispassionately.
Author information:
Barbara Heslop, Emeritus Professor, Dunedin School of Medicine, University of
Otago, Dunedin
Acknowledgment: This
account of medical research in the third quarter of the last century owes much
to discussion and correspondence with my contemporaries. As might be expected,
their research experience has varied. Some have been academics, and this group
includes distinguished international endocrinologist Mont Liggins. Many others
have belonged to a group that I’ll call inadvertent
researchers—clinicians who introduced new treatments in their day, only to
find a later generation classing their way of doing things as research. I hope
that they will agree that this was how it was.
Correspondence:
Emeritus Professor Barbara Heslop, 1 Hart St, Belleknowes, Dunedin; email: b.heslop@xtra.co.nz
Reference:
The Report of the Committee
of Inquiry into Allegations Concerning the Treatment of Cervical Cancer at
National Women’s Hospital. Report. Auckland; 1988. Available online: URL:
http://www.womens-health.org.nz/cartwright/cartwright.htm
Accessed August 2004.
|
|
|
| | Current
issue | Search journal |
Archived issues | Classifieds
| Hotline (free ads) Subscribe | Contribute | Advertise | Contact Us | Copyright | Other Journals |
|