It Is Only a Matter of Implementation

Keynote Address by Barry Bloom
HSPH 75th Anniversary Symposium held April 27-29, 1997

This symposium celebrating
the Harvard School of Public Health, its considerable achievments and
traditions, offers a wonderful opportunity for each of us to contemplate
the future of public health. In so doing, I find myself rather optimistic–but
an optimist in the sense defined by the nuclear physicist, Leo Szilard,
as "one who believes the future is uncertain." Clearly there are uncertainties
associated with infectious diseases, emerging drug resistance, changes
in microbial pathogenesis and even the threat of biological terrorism.
But the uncertainties inhering in the broader realm of public health encompass
a great deal more than infectious diseases. There are uncertainties in
the very definition of health, in standards and appropriate levels of
health. There is enormous uncertainty about health care policy and financing
everywhere in the world . And there is uncertainty about the relevance
and survival of academic medical and public health institutions. On this
occasion, I would like principally to focus my presentation on yet another
uncertainty, one not listed elsewhere on the program of this extraordinary Symposium–education in public health. My favorite definition of education
is "what you remember when you forget what you’ve learned." As someone
who is enormously respectful of the public health community and utterly
dependent on its help in shaping my own scientific agenda and priorities,
I hope it will not appear presumptious for me to comment on public health
education, and on the enduring ‘imprint’ made on some of its graduates,
which I have experienced as an outsider. My intent, I must warn you in
advance, is to be provocative, and to challenge some of the shibboleths
and precepts that I believe have been imprinted in public health education. 

Let me describe the context in which my views have been
formulated, which will constitute the thread that I hope will connect
much of what I have to say. The monumental study, Global Burden of
Disease and Injury
, compiled by Christopher Murray of the Harvard
School of Public Health and Alan Lopez at WHO (Harvard Univ. Press, 1996),
defined a metric of the burden of disease and disability, from all causes,
in all regions of the world. This metric, disability adjusted life years
(DALYS), takes into acount not only disease-related mortality, but also
years of healthy life lost to debilitating illness. The largest single
burden of disease in the world–whether measured by DALYS or mortality–remains
communicable diseases, including maternal and perinatal morbidity and
mortality. More people die of infectious diseases than of heart disease
or neoplastic disease or intentional and unintentional injuries. A second
major point this historic study makes clear is that the burden of disease
and disability does not fall equally on people in all parts of the world.
The vast majority of the burden of disease and disability (88%) falls
on people in developing countries and upon the poorest people in every
society. 

Among infectious diseases, the largest cause of death in
the world from any pathogen is tuberculosis. That is the disease my research
work has been focused on for the past decade. The truth is that that tuberculosis
has always been a major problem, largely ignored until recently, when
it reemerged in the developed world. In the first tract on epidemiology
in English, published in 1662 by one John Grant, citizen of London, entitled
"Natural and Political Observations Mentioned in a Following Index
and Made upon the Bills of Mortality,"
documenting the causes of death
in 1632 in the City of Westminster (that later became London), the second
leading cause of death, after neonatal and childhood mortality, was consumption.
Of the 9,536 burials recorded, tuberculosis was the attributable cause
of death in 19%. In passing it is interesting to note that grief was also
a major cause of death, which I take to reflect a high level of mental
illness persisting into our current time; and perhaps surprising to some,
murder was more prevalent then, certainly (0.7%), than it is even in Boston
now. 
 
"It is only a matter of
implementation

The title of the talk was chosen to reflect my concern
about a perspective often justified in the field of public health by people
who are committed to getting things done, to changing the world, making
it a better place in as short a term as possible. It is very easy to believe
that public health is only a matter of implementation. "If we only had
the funding, we could accomplish X, Y, and Z in our lifetimes"–or as
WHO has enunciated it, we can have "health for all by the year 2000." 

This perspective, in my own field, is by no means new.
The first tool for implementation in tuberculosis was the laying-on-of-hands
in the twelfth century by the kings of England and France to treat the
King’s evil, scrofula or tuberculosis of the lymph nodes. In a little-known
retrospective epidemiological comparison of the efficacy of laying-on-of-hands
by the kings of England and France carried out in the seventeenth century,
it emerged that while the intervention was carried out more assiduously
by the kings of England than of France, like all interventions in tuberculosis,
after a few years it was found to be inadequate to deal with the problem.
That is a great tradition in the field of tuberculosis. As everyone knows,
Robert Koch discovered the tubercle bacillus in 1882. While few are aware
of it, in 1890 Robert Koch also reported the cure for tuberculosis–an
ill-characterized brown oil, for which he received a directorship at a
new government institute and his government received a monopoly on the
cure. So much for the claim that international property rights issues
represent a radically new problem for scientific research! In 1921, Calmette
and Guerin made the vaccine for tuberculosis; and in 1948 Waxman
and Schatz discovered streptomycin, the drug for tuberculosis.
This year, the director-general of the World Health Organization declared
directly observed therapy with short course chemotherapy (DOTS) to be
"the most important medical discovery of the decade." In fact, in a press
release on March 24 of this year to mark the date
of the discovery by Koch of the tubercle bacillus, the director of WHO’s
Global Programme on Tuberculosis issued this statement, "This week, for
the first time in the six-thousand-year history of tuberculosis, we have
the tools, strategies and medicines to defeat the epidemic in all parts
of the world. And we know the precise path we must take to accomplish
this." There is no one that I have met in the field of tuberculosis that
has confidence that that statement is true. 

The question raised here is how important is the implementation
of a program that saves lives? How important is that with respect to resource
allocations for other efforts to save lives? How important is it to implement
programs and mobilize funds, even if they compromise the integrity and
credibility of the one institution in the world that has been trusted
by every country in the field of health? These are questions the answers
to which hinge on one’s judgment on how important implementation using
existing tools is in any circumstance. 

Cost is the limiting factor
to health intervention
 

Any student of international health and public health has
been imprinted with the belief that it is cost that limits the application
of existing health interventions. And, of course, that fact is usually
true. But there are circumstances in which costs change, and priorities
change, when public demand changes. In 1989, after fifteen years of effort
of many people to persuade the government of the United States to mount
a major push to eliminate tuberculosis as a public health problem, and
at a time when the World Health Organization, in June of 1989, had only
a single professional in its Tuberculosis Unit, the standard rationale
for why it was not possible to do anything substantial in TB was that
the cost of implementation, specifically of the three drugs required for
6-9 months, was prohibitive. Prior to 1990, isoniazid, rifampicin, and
pyrazinamide required for a cure of a single case cost about $125. How
could one contemplate spending $125 per case when in many countries of
the world per capita spending on health was less than $2? The present
circumstance is that the Global Programme on Tuberculosis at WHO is doing
a highly effective job working with countries to achieve an increase in
patients under treatment and to improve compliance and cure rates. This
is an extraordinary achievement. Because WHO created that program and
made the commitment to an effective global TB control program, the price
of the same drugs dropped from $125 to $18 per case currently. One doesn’t
always succeed, but one cannot give up on good interventions solely because
it is assumed that costs cannot be dealt with. 

One of the greatest lessons in this regard comes from the
case of ivermectin, an antihelminthic drug that, in a single administration,
is effective in preventing onchocerciasis or river blindness. Again, the
thought was that the cost of drugs had been the limiting factor for controlling
the disease. Ivermectin is a profitable veterinary product that is now
given for human use by Merck and Co. entirely free. One would have expected
a vast clamoring for access to the drug. The result was quite the contrary.
In the second year of the Mectizan Program to make the drug available
free to the 18 million people in Africa at risk for onchocerciasis, only
240,000 people received the treatment. And yet the drug cost nothing.
So what we have learned is that the cost of the drug was really not the
limiting factor. The lack of health care infrastructure and the assurance
that the drug could be safely and well used were ultimately limiting.
Perhaps as much as for giving it away free, Merck is to be credited for
investing over a long period of time in the Mectizan Program to provide
the infrastructure to distribute, apply, and monitor the use of the drug.
In 1996, 19.1 million people were receiving ivermectin for free, and onchocerciasis
in now one of those diseases targeted by WHO for elimination as a public
health problem. This has been truly a remarkable success story in public
health. 

In the Global Burden of Disease and Injury and the
related Ad hoc Committee Report on Investing in Health Research and
Development
(WHO, Geneva, 1996), Christopher Murray developed an interesting
strategy to analyze health resource allocations and priority setting.
If the burden of any particular disease is schematized as the area of
a box, one can analyze what proportion of existing disease can be averted
by presently existing tools; how much could be averted if the presently
existing tools were more efficiently delivered, termed "allocative efficiency";
and how much of the disease could be dealt with existing tools in a non-cost-effective
way. What remains, then, is how much of the burden of a particular disease
one simply does not have adequate tools to address. This would define,
at a first approximation, the need for a research agenda. It is a sophisticated
conception, but I believe has significant pitfalls and is subject to misconstruction. 

One of those pitfalls is illustrated by imagining oneself
at WHO or NIH in the 1950s, debating the priorities for allocation of
scarce health resources to confront the urgent global problem of poliomyelitis.
One expert steps forward and pronounces, "I have the tool, strategies
and the path we must take. It is iron lungs–and I can take care of all
the kids in the world with life-threatening polio, if I had only enough
money to get them out there." At that same meeting, perhaps, there would
be some wild red-eyed fellow in a white coat arguing, "I have a vision
that, perhaps for pennies, we could make a vaccine, if only we invest
in some research." If that debate were held today, I would not be terribly
optimistic about the outcome.  Another problem
limiting our thinking by allocative efficiency arguments, going strictly
by the numbers, or by cost-effectiveness, is how to address the small
number of diseases targeted for elimination. They would be totally ignored.
Six of those diseases represent a triumph in a quiet way of the World
Health Organization. No one else but WHO has payed an awful lot of attention
to these diseases. But, leprosy, onchocerciasis, lymphatic filariasis,
Chagas disease and dracunculiasis (Guinea worm) have been officially targeted
for elimination as public health problems–not for total extinction
from the world or eradication, which have been promised but not
delivered in the past. And they are being eliminated. On the basis of
allocative efficiency, as the burden of these diseases declines, the cost-effectiveness,
of course, becomes less, and priority for eliminating these diseases would
disappear in any sort of cost-effectiveness analysis. One must balance
the opportunity of relatively short-term investments to eliminate diseases
that have burdened humanity from time immemorial with cost-effectiveness
criteria promoted by the current generation of sophisticated economists. 

It is
only a matter of prevention

One great tradition and perhaps major comparative advantage
of schools of public health has been their focus on disease prevention
rather than treatment. The world of medicine is changing, and I believe
it will be necessary in this rapidly evolving context to consider expanding
the scope from the base of disease prevention to broader aspects of health,
including treatment. The power of prevention and its fundamental role
in public health is obvious. One has only to look at the precipitous decline
of childhood infectious diseases such as measles, rubella, pertussis,
diphtheria, mumps, polio, and H. flu meningitis within a very few
years after the introduction of childhood vaccines in this country and
around the world. The impact and cost-effectiveness of many prevention
tools is truly extraordinary, and regrettably, I fear, taken too much
for granted. As Murray and Lopez have projected, the world in the year
2020 will be a very different place. While the preponderance of the burden
of disease is currently infectious and perinatal disease, the new emerging
epidemic will be of chronic debilitating diseases. It is projected that
ischemic heart disease, unipolar depression, road traffic accidents, and
cardiovascular disease will be the major global health problems in the
year 2020. These are not necessarily the simplest of diseases to prevent,
like polio or measles, for which classical biomedical interventions are
possible. The educational programs of schools of public health, I believe,
will have to adapt to a different environment, and strike a new balance
between chronic versus infectious diseases. They will be forced to reexamine
their emphasis on prevention relative to treatment, and evolve to maintain
and enhance their relevance.

Let me illustrate the dilemma by citing a fascinating paper
from Milton Weinstein’s group at the School of Public Health, published
earlier this year (Hunink, M. et al, JAMA 227:535, 1997). The study evaluated
the impact of two types of intervention, preventive and therapeutic, on
mortality rates in cardiovascular disease, specifically coronary artery
disease. Between 1980 and 1990 there was a reduction in deaths of 34%
in the populations studied. The question addressed was what was responsible
for that striking reduction in death from coronary artery disease. Surprisingly,
they found that only 25% of the reduction in deaths could be attributed
to primary prevention. The vast majority of deaths averted derived from
the application of curative medicine. As biomedical research and technology
produce new tools, some expensive, hopefully others not, that keep people
alive and signficantly improve their quality of life, I believe this finding
may anticipate others in the future. In this context, the distinction
between prevention and treatment will become more ambiguous and an ideological
attachment to only a narrow definition of prevention may limit the scope
and relevance of the field of public health. 

Two kinds of research 

The president of the Royal Society, Lord Porter, liked
to say that "there are two kinds of research, applied research and not
yet applied research." Twenty years ago, there was a major debate in medicine,
led by Thomas McKeown, who wrote of a book entitled The Role of Medicine:
Mirror, Mirage or Nemesis
, that argued that increases in life expectancy
in this century, perhaps 35 years at the time he wrote, could not be attributed
to any known medical interventions. The vast majority of that extended
life expectancy, he speculated, had to be due to changes in nutrition
and the environment. It was his judgment that biomedical research had
contributed virtually nothing. That view still endures. In a press release
on tuberculosis from the World Health Organization, their director of
tuberculosis research made the following statement: "Money is wasted on
[research] projects that will be neither practical nor effective. For
example, there is widespread misallocation of resources as well as underfunding.
Donors have continued to fund narrowly defined biomedical research that
will simply be too costly to be practical." Narrowly defined biomedical
research! As someone who has engaged in biomedical research for 30 years,
I don’t know what that is, because I don’t know what broadly defined biomedical
research is. I think I have some sense what good research is, although
my own view can often be admittedly shortsighted. I find it shocking that
such a position is promulgated under the logo of the World Health Organization,
one of whose missions is to bring the best in science and medicine to
people around the world. 

Let me pursue McKeown’s thesis from the perspective of
tuberculosis. First, I must note that mortality statistics in the United
States did not become nationally compiled until 1900. From the point of
view of national mortality statistics since 1900, he would appear to be
right, even for tuberculosis. There has been a steady decline in mortality
since 1900. But if one examines the New York City Department of Health
statistics on tuberculosis, which began their extraordinary and meticulous
health records in 1800, it is interesting to note that mortality from
tuberculosis was an almost straight line at a level of 400 deaths per
100,000 population from 1800 until about 1885, when the curve started
its decline. Is it coincidental that this decline, associated as you well
know with the beginning of the public health movement in this country,
corresponds with the discovery of the tubercle bacillus in 1882 by Robert
Koch, and the more general acceptance of the germ theory of disease? Or
is the decline in TB at this time the result of some mysterious change
in the environment or nutrition that spontaneously occurred and which
no one has yet been able to identify? 

Let us consider the position of the WHO TB programme, and
ask whether there is, indeeed, any longer a need for biomedical research,
narrow or broadly defined, in tuberculosis? Perhaps they wish to argue
that new tools are no longer needed, because the present strategy is so
effective at curing cases. Tuberculosis is a disease that has an epidemic
cycle of 100-300 years. With the best tools currently available, Directly
Observed Therapy (DOTS) for six months with three or four drugs under
supervision, it is going to take a very long time and a lot of money to
reach all the people in the world who need it. Let me point out that there
is currently not a single rapid, inexpensive diagnostic test that can
be employed in the field to detect TB cases or ascertain drug resistance.
In a world in which one-third of the global population is infected with
the tubercle bacillus, if there were a drug or vaccine that acted to kill
the persisting bacilli in latent or dormant infection and prevent reactivated
disease, the 100- year epidemic cycle could be reduced to a 10-year cycle.
If we had an effective vaccine to prevent infection or disease, we would
certainly stem the epidemic. I do not wish to belittle DOTS–it is clearly
the best tool available today for addressing the problem of tuberculosis.
My point is that even when one has adequate tools, there is likely to
be a continuing need for research. 

There is no better example of that maxim than the experience
of a closely related disease, leprosy, where the WHO Leprosy Unit exhibits
a totally different mentality about research. Because of indications of
a major rise in bacterial resistance to monotherapy with dapsone, in the
1970s WHO recommended multidrug therapy with three drugs. In 1973 there
were approximately 12 million registered patients with leprosy. In 1983
there were 5.4 million registered cases, and about one-half of all those
who had formerly been on lifetime treatment could be discharged from treatment
as cured. There are now fewer than 1 million registered cases. The recommended
regimen was six months treatment for paucibacillary (tuberculoid) cases
and two years treatment for lepromatous or multibacillary cases, and the
treatment clearly worked. But the WHO Leprosy Unit and the Tropical Diseases
Research Programme did not announce that they no longer needed research,
or call a press conference. They continued to experiment and do research.
Two weeks ago, they broke the code of their latest trial which was designed
to learn how short a treatment could be given with a new combination of
drugs. Using two new drugs plus rifampicin, they learned that in patients
with single-lesion disease, a single administration of drugs was as effective
as six months’ treatment. The implications in terms of compliance and
cost are, within the context of that disease, staggering. Lifetime treatment
was reduced to six months treatment and is now reduced for many to one
day’s treatment. The message here is that even with a treatment that was
effective, there was a need for more research and an opportunity for significant
improvement. 

On "narrow biomedical
research"
 

Recombinant DNA technology, and much of the revolution
in modern biology, that I hope will bring health benefits to every person
on the planet, derives from a laboratory experiment that Joshua Lederberg
carried out in the 1940s. Lederberg was not seeking to do anything useful
or practical, but rather to understand sex in bacteria, or more specifically
the nature of recombination in bacteria. The original experiments of Kohler
and Milstein that produced the first monoclonal antibodies were similarly
designed to ask a basic question. They found that fusion of a myeloma
tumor cell with a differentiated primary somatic cell type, B lymphocytes,
generated an immortalized cell that continued to express antibodies. This
experiment was particularly remarkable, since cell fusions with other
types of cells had extinguished expression of differentiated functions.
The studies of Bernard Moss and Enzo Paoletti aimed to understand the
molecular basis of the pathogenesis of smallpox, which by that time had
truly been extinguished from the face of the earth. By molecular genetic
manipulations of the vaccinia virus, they created more-attenuated strains
and the concept of multivaccine vectors that could be used to deliver
antigens protective against multiple infections. It is almost certain
that one of the first AIDS vaccine trials to enter efficacy trials will
use a recombinant vaccinia virus. More recently, the failure of gene therapy
in some experimental studies was found to result from the production of
antibodies to the gene product. As discouraging as that may be from the
gene therapy viewpoint, it has given rise to the newest type of vaccines,
naked DNA vaccines, that are inexpensive and, at least in experimental
animals, remarkably effective at inducing a wide variety of host immune
responses to individual antigens encoded by the DNA. These are simply
a few examples, well known to all of us, that some of the most important
practical applications derived from pursuit of fundamental scientific
questions. 

If one were to project where biomedical science is likely
to make contributions to health in the future, the one certainty is uncertainty.
Nevertheless, while your list may be more accurate than mine, I would
expect that the human genome project, in addition to providing an invaluable
roadmap to every gene and the organization of the genome, will have the
potential to reveal every genetic predisposition within an individual
for disease susceptibility and resistance. Neuroscience, in uncovering
the fundamental mysteries of mind and cognition, will address what is
projected to be the second largest burden of disease in the 21st
century, depression and mental illness, and hopefully result in new treatments
and preventives. Combinatorial chemistry permits synthesis of a half million
new compounds per week in a single laboratory, more than any pharmaceutical
company previously could generate before it merges with an even larger
conglomerate or undergoes a leveraged buyout. This new approach is accelerating
both drug screening and rational drug design. Developmental biology and
oncogenes will hopefully allow understanding of neoplastic disease, and
lead to better cancer treatments and preventives. Communication technology
and the analysis of large linked data bases will allow studies of interventions
that affect a great many people, which could accelerate the validation
of new interventions and their incorporation into public health. My general
point here is simply that there has to be scope in public health to accommodate
and foster appropriate respect for the entire range of contributors to
public health–researchers, physicians and health care providers across
the health spectrum. As Robert Oppenheimer once said, "It is a profound
and necessary truth that deep things in science are not found because
they are useful. They are found because it was possible to find them." 

The topology of
health
 

There is another imprint of their education that many
of my colleagues trained at schools of public health carry within the
deep recesses of their cerebral cortices, which frequently becomes patent
among those who represent international donors and overseas development
agencies and oversee international health programs. What they learned
is that for a program to be good, it must be "horizontal," i.e. delivered
within primary health care, and that any program that is "vertical" must
be a dreadful thing, distorting of primary health care systems and infrastructure.
This has become, in my judgment, a kind of mindless mantra in public health
ideology. Let me point out that the global eradication of smallpox, oral
rehydration for diarrheal disease, the entire expanded program for immunization
against childhood infectious diseases, the onchocerciasis control program,
and the hookworm eradication program of the Rockefeller Foundation in
the US, which found that putting shoes on kids was better than any medical
intervention, were all originally vertical programs. The equally important
point, however, is that once they were shown to work–and perhaps only
then–it became possible to integrate them into primary health care strategies.
I would simply urge that this question be looked at in a longer-term context,
and that the topological ideology not be slavishly worshiped to the detriment
of pragmatic and constructive alternatives. 

Topology deals with surfaces, and there are more pressing
core issues that I believe have not been adequately addressed by schools
of public health. The one that I am most concerned about here is the issue
of equity–health equity within countries and between countries. I am
gratified that equity figures in many of the presentations at this Symposium.
Let me again refer to an example from the world of tuberculosis. A classic
study of Karen Brudney and Jay Dobkin at Columbia Presbyterian Medical
Center in New York analyzed 224 consecutive patients with tuberculosis
at the Harlem Hospital in New York in 1988 (Amer. Rev. Resp. Dis.
144:745-49, 1991). They found that the case completion rate was 11% (we
don’t really know what the case cure rate was because there was no two-year
follow up). There is probably no developing country in the world that
had a less effective control program than that in New York City in the
late 1980s. If one looks more deeply at the patient population, as they
did, perhaps one finds some of the explanations. Eighty-two percent of
the patients were unemployed, 53% were alcoholic, 45% were homeless, 40%
had AIDS or AIDS-related syndromes. This is health inequity in the richest
country in the world. 

The inclination of most people presented with such data
would be to infer that that problem is most likely attributable to the
lack of access to health care. If there were only greater access, this
type of inequity would disappear. Alas, there are some extraordinary data
that would suggest that lack of access to health care is not likely to
be the whole story. The classic study of death rates in Chicago in the
1960s as a function of personal income (Kitigawa E.M. and Hauser, P.M.,
Differential Mortality in the United States: A Study in Socioeconomic
Epidemiology
. Harvard Univ. Press, 1973) indicated, not surprisingly,
that mortality rates in the highest income sector in the population was
very much lower than in the lowest income sector of the population. However,
at virtually the same time, the famous Black study was being conducted
on death rates as a function of professional status in the United Kingdom
(Townsend P., Davidson, N., amd Whitehead, M., Inequalities in Health:The
Black Report and the Health Divide.
Penguin Books. London, 1990),
and it yielded almost identical results. Professionals there had the lowest
death rates and unskilled laborers the highest. But in Britain, every
one of those individuals had access, in fact, to the National Health Service.
Understanding and resolving equity disparities in health, then, is not
a simple matter. The causes may be structural or biological, cultural,
political, economic, lack of access, or knowledge of how to "work the
system." My caution is that these need to be meaningfully delineated,
if equity and health are to be improved. Public health schools should
be wonderful places to do that, and ought to take the lead. In the course
of that pursuit, it may emerge that some of the factors that are most
important to improving health may be ones that the health sciences and
health professions have little power to affect, and that the identification
of others in which we do have a major role to play will present important
opportunities. In the pursuit of equity we must also maintain a sense
of integrity, and a perspective of what academic public health can, and
cannot, do. 

It is
only a matter of prevention

One great tradition and perhaps major comparative advantage
of schools of public health has been their focus on disease prevention
rather than treatment. The world of medicine is changing, and I believe
it will be necessary in this rapidly evolving context to consider expanding
the scope from the base of disease prevention to broader aspects of health,
including treatment. The power of prevention and its fundamental role
in public health is obvious. One has only to look at the precipitous decline
of childhood infectious diseases such as measles, rubella, pertussis,
diphtheria, mumps, polio, and H. flu meningitis within a very few
years after the introduction of childhood vaccines in this country and
around the world. The impact and cost-effectiveness of many prevention
tools is truly extraordinary, and regrettably, I fear, taken too much
for granted. As Murray and Lopez have projected, the world in the year
2020 will be a very different place. While the preponderance of the burden
of disease is currently infectious and perinatal disease, the new emerging
epidemic will be of chronic debilitating diseases. It is projected that
ischemic heart disease, unipolar depression, road traffic accidents, and
cardiovascular disease will be the major global health problems in the
year 2020. These are not necessarily the simplest of diseases to prevent,
like polio or measles, for which classical biomedical interventions are
possible. The educational programs of schools of public health, I believe,
will have to adapt to a different environment, and strike a new balance
between chronic versus infectious diseases. They will be forced to reexamine
their emphasis on prevention relative to treatment, and evolve to maintain
and enhance their relevance.

Let me illustrate the dilemma by citing a fascinating paper
from Milton Weinstein’s group at the School of Public Health, published
earlier this year (Hunink, M. et al, JAMA 227:535, 1997). The study evaluated
the impact of two types of intervention, preventive and therapeutic, on
mortality rates in cardiovascular disease, specifically coronary artery
disease. Between 1980 and 1990 there was a reduction in deaths of 34%
in the populations studied. The question addressed was what was responsible
for that striking reduction in death from coronary artery disease. Surprisingly,
they found that only 25% of the reduction in deaths could be attributed
to primary prevention. The vast majority of deaths averted derived from
the application of curative medicine. As biomedical research and technology
produce new tools, some expensive, hopefully others not, that keep people
alive and signficantly improve their quality of life, I believe this finding
may anticipate others in the future. In this context, the distinction
between prevention and treatment will become more ambiguous and an ideological
attachment to only a narrow definition of prevention may limit the scope
and relevance of the field of public health. 

Two kinds of research 

The president of the Royal Society, Lord Porter, liked
to say that "there are two kinds of research, applied research and not
yet applied research." Twenty years ago, there was a major debate in medicine,
led by Thomas McKeown, who wrote of a book entitled The Role of Medicine:
Mirror, Mirage or Nemesis
, that argued that increases in life expectancy
in this century, perhaps 35 years at the time he wrote, could not be attributed
to any known medical interventions. The vast majority of that extended
life expectancy, he speculated, had to be due to changes in nutrition
and the environment. It was his judgment that biomedical research had
contributed virtually nothing. That view still endures. In a press release
on tuberculosis from the World Health Organization, their director of
tuberculosis research made the following statement: "Money is wasted on
[research] projects that will be neither practical nor effective. For
example, there is widespread misallocation of resources as well as underfunding.
Donors have continued to fund narrowly defined biomedical research that
will simply be too costly to be practical." Narrowly defined biomedical
research! As someone who has engaged in biomedical research for 30 years,
I don’t know what that is, because I don’t know what broadly defined biomedical
research is. I think I have some sense what good research is, although
my own view can often be admittedly shortsighted. I find it shocking that
such a position is promulgated under the logo of the World Health Organization,
one of whose missions is to bring the best in science and medicine to
people around the world. 

Let me pursue McKeown’s thesis from the perspective of
tuberculosis. First, I must note that mortality statistics in the United
States did not become nationally compiled until 1900. From the point of
view of national mortality statistics since 1900, he would appear to be
right, even for tuberculosis. There has been a steady decline in mortality
since 1900. But if one examines the New York City Department of Health
statistics on tuberculosis, which began their extraordinary and meticulous
health records in 1800, it is interesting to note that mortality from
tuberculosis was an almost straight line at a level of 400 deaths per
100,000 population from 1800 until about 1885, when the curve started
its decline. Is it coincidental that this decline, associated as you well
know with the beginning of the public health movement in this country,
corresponds with the discovery of the tubercle bacillus in 1882 by Robert
Koch, and the more general acceptance of the germ theory of disease? Or
is the decline in TB at this time the result of some mysterious change
in the environment or nutrition that spontaneously occurred and which
no one has yet been able to identify? 

Let us consider the position of the WHO TB programme, and
ask whether there is, indeeed, any longer a need for biomedical research,
narrow or broadly defined, in tuberculosis? Perhaps they wish to argue
that new tools are no longer needed, because the present strategy is so
effective at curing cases. Tuberculosis is a disease that has an epidemic
cycle of 100-300 years. With the best tools currently available, Directly
Observed Therapy (DOTS) for six months with three or four drugs under
supervision, it is going to take a very long time and a lot of money to
reach all the people in the world who need it. Let me point out that there
is currently not a single rapid, inexpensive diagnostic test that can
be employed in the field to detect TB cases or ascertain drug resistance.
In a world in which one-third of the global population is infected with
the tubercle bacillus, if there were a drug or vaccine that acted to kill
the persisting bacilli in latent or dormant infection and prevent reactivated
disease, the 100- year epidemic cycle could be reduced to a 10-year cycle.
If we had an effective vaccine to prevent infection or disease, we would
certainly stem the epidemic. I do not wish to belittle DOTS–it is clearly
the best tool available today for addressing the problem of tuberculosis.
My point is that even when one has adequate tools, there is likely to
be a continuing need for research. 

There is no better example of that maxim than the experience
of a closely related disease, leprosy, where the WHO Leprosy Unit exhibits
a totally different mentality about research. Because of indications of
a major rise in bacterial resistance to monotherapy with dapsone, in the
1970s WHO recommended multidrug therapy with three drugs. In 1973 there
were approximately 12 million registered patients with leprosy. In 1983
there were 5.4 million registered cases, and about one-half of all those
who had formerly been on lifetime treatment could be discharged from treatment
as cured. There are now fewer than 1 million registered cases. The recommended
regimen was six months treatment for paucibacillary (tuberculoid) cases
and two years treatment for lepromatous or multibacillary cases, and the
treatment clearly worked. But the WHO Leprosy Unit and the Tropical Diseases
Research Programme did not announce that they no longer needed research,
or call a press conference. They continued to experiment and do research.
Two weeks ago, they broke the code of their latest trial which was designed
to learn how short a treatment could be given with a new combination of
drugs. Using two new drugs plus rifampicin, they learned that in patients
with single-lesion disease, a single administration of drugs was as effective
as six months’ treatment. The implications in terms of compliance and
cost are, within the context of that disease, staggering. Lifetime treatment
was reduced to six months treatment and is now reduced for many to one
day’s treatment. The message here is that even with a treatment that was
effective, there was a need for more research and an opportunity for significant
improvement. 

On "narrow biomedical
research"
 

Recombinant DNA technology, and much of the revolution
in modern biology, that I hope will bring health benefits to every person
on the planet, derives from a laboratory experiment that Joshua Lederberg
carried out in the 1940s. Lederberg was not seeking to do anything useful
or practical, but rather to understand sex in bacteria, or more specifically
the nature of recombination in bacteria. The original experiments of Kohler
and Milstein that produced the first monoclonal antibodies were similarly
designed to ask a basic question. They found that fusion of a myeloma
tumor cell with a differentiated primary somatic cell type, B lymphocytes,
generated an immortalized cell that continued to express antibodies. This
experiment was particularly remarkable, since cell fusions with other
types of cells had extinguished expression of differentiated functions.
The studies of Bernard Moss and Enzo Paoletti aimed to understand the
molecular basis of the pathogenesis of smallpox, which by that time had
truly been extinguished from the face of the earth. By molecular genetic
manipulations of the vaccinia virus, they created more-attenuated strains
and the concept of multivaccine vectors that could be used to deliver
antigens protective against multiple infections. It is almost certain
that one of the first AIDS vaccine trials to enter efficacy trials will
use a recombinant vaccinia virus. More recently, the failure of gene therapy
in some experimental studies was found to result from the production of
antibodies to the gene product. As discouraging as that may be from the
gene therapy viewpoint, it has given rise to the newest type of vaccines,
naked DNA vaccines, that are inexpensive and, at least in experimental
animals, remarkably effective at inducing a wide variety of host immune
responses to individual antigens encoded by the DNA. These are simply
a few examples, well known to all of us, that some of the most important
practical applications derived from pursuit of fundamental scientific
questions. 

If one were to project where biomedical science is likely
to make contributions to health in the future, the one certainty is uncertainty.
Nevertheless, while your list may be more accurate than mine, I would
expect that the human genome project, in addition to providing an invaluable
roadmap to every gene and the organization of the genome, will have the
potential to reveal every genetic predisposition within an individual
for disease susceptibility and resistance. Neuroscience, in uncovering
the fundamental mysteries of mind and cognition, will address what is
projected to be the second largest burden of disease in the 21st
century, depression and mental illness, and hopefully result in new treatments
and preventives. Combinatorial chemistry permits synthesis of a half million
new compounds per week in a single laboratory, more than any pharmaceutical
company previously could generate before it merges with an even larger
conglomerate or undergoes a leveraged buyout. This new approach is accelerating
both drug screening and rational drug design. Developmental biology and
oncogenes will hopefully allow understanding of neoplastic disease, and
lead to better cancer treatments and preventives. Communication technology
and the analysis of large linked data bases will allow studies of interventions
that affect a great many people, which could accelerate the validation
of new interventions and their incorporation into public health. My general
point here is simply that there has to be scope in public health to accommodate
and foster appropriate respect for the entire range of contributors to
public health–researchers, physicians and health care providers across
the health spectrum. As Robert Oppenheimer once said, "It is a profound
and necessary truth that deep things in science are not found because
they are useful. They are found because it was possible to find them." 

The topology of
health
 

There is another imprint of their education that many
of my colleagues trained at schools of public health carry within the
deep recesses of their cerebral cortices, which frequently becomes patent
among those who represent international donors and overseas development
agencies and oversee international health programs. What they learned
is that for a program to be good, it must be "horizontal," i.e. delivered
within primary health care, and that any program that is "vertical" must
be a dreadful thing, distorting of primary health care systems and infrastructure.
This has become, in my judgment, a kind of mindless mantra in public health
ideology. Let me point out that the global eradication of smallpox, oral
rehydration for diarrheal disease, the entire expanded program for immunization
against childhood infectious diseases, the onchocerciasis control program,
and the hookworm eradication program of the Rockefeller Foundation in
the US, which found that putting shoes on kids was better than any medical
intervention, were all originally vertical programs. The equally important
point, however, is that once they were shown to work–and perhaps only
then–it became possible to integrate them into primary health care strategies.
I would simply urge that this question be looked at in a longer-term context,
and that the topological ideology not be slavishly worshiped to the detriment
of pragmatic and constructive alternatives. 

Topology deals with surfaces, and there are more pressing
core issues that I believe have not been adequately addressed by schools
of public health. The one that I am most concerned about here is the issue
of equity–health equity within countries and between countries. I am
gratified that equity figures in many of the presentations at this Symposium.
Let me again refer to an example from the world of tuberculosis. A classic
study of Karen Brudney and Jay Dobkin at Columbia Presbyterian Medical
Center in New York analyzed 224 consecutive patients with tuberculosis
at the Harlem Hospital in New York in 1988 (Amer. Rev. Resp. Dis.
144:745-49, 1991). They found that the case completion rate was 11% (we
don’t really know what the case cure rate was because there was no two-year
follow up). There is probably no developing country in the world that
had a less effective control program than that in New York City in the
late 1980s. If one looks more deeply at the patient population, as they
did, perhaps one finds some of the explanations. Eighty-two percent of
the patients were unemployed, 53% were alcoholic, 45% were homeless, 40%
had AIDS or AIDS-related syndromes. This is health inequity in the richest
country in the world. 

The inclination of most people presented with such data
would be to infer that that problem is most likely attributable to the
lack of access to health care. If there were only greater access, this
type of inequity would disappear. Alas, there are some extraordinary data
that would suggest that lack of access to health care is not likely to
be the whole story. The classic study of death rates in Chicago in the
1960s as a function of personal income (Kitigawa E.M. and Hauser, P.M.,
Differential Mortality in the United States: A Study in Socioeconomic
Epidemiology
. Harvard Univ. Press, 1973) indicated, not surprisingly,
that mortality rates in the highest income sector in the population was
very much lower than in the lowest income sector of the population. However,
at virtually the same time, the famous Black study was being conducted
on death rates as a function of professional status in the United Kingdom
(Townsend P., Davidson, N., amd Whitehead, M., Inequalities in Health:The
Black Report and the Health Divide.
Penguin Books. London, 1990),
and it yielded almost identical results. Professionals there had the lowest
death rates and unskilled laborers the highest. But in Britain, every
one of those individuals had access, in fact, to the National Health Service.
Understanding and resolving equity disparities in health, then, is not
a simple matter. The causes may be structural or biological, cultural,
political, economic, lack of access, or knowledge of how to "work the
system." My caution is that these need to be meaningfully delineated,
if equity and health are to be improved. Public health schools should
be wonderful places to do that, and ought to take the lead. In the course
of that pursuit, it may emerge that some of the factors that are most
important to improving health may be ones that the health sciences and
health professions have little power to affect, and that the identification
of others in which we do have a major role to play will present important
opportunities. In the pursuit of equity we must also maintain a sense
of integrity, and a perspective of what academic public health can, and
cannot, do. 

It is
only a matter of prevention

One great tradition and perhaps major comparative advantage
of schools of public health has been their focus on disease prevention
rather than treatment. The world of medicine is changing, and I believe
it will be necessary in this rapidly evolving context to consider expanding
the scope from the base of disease prevention to broader aspects of health,
including treatment. The power of prevention and its fundamental role
in public health is obvious. One has only to look at the precipitous decline
of childhood infectious diseases such as measles, rubella, pertussis,
diphtheria, mumps, polio, and H. flu meningitis within a very few
years after the introduction of childhood vaccines in this country and
around the world. The impact and cost-effectiveness of many prevention
tools is truly extraordinary, and regrettably, I fear, taken too much
for granted. As Murray and Lopez have projected, the world in the year
2020 will be a very different place. While the preponderance of the burden
of disease is currently infectious and perinatal disease, the new emerging
epidemic will be of chronic debilitating diseases. It is projected that
ischemic heart disease, unipolar depression, road traffic accidents, and
cardiovascular disease will be the major global health problems in the
year 2020. These are not necessarily the simplest of diseases to prevent,
like polio or measles, for which classical biomedical interventions are
possible. The educational programs of schools of public health, I believe,
will have to adapt to a different environment, and strike a new balance
between chronic versus infectious diseases. They will be forced to reexamine
their emphasis on prevention relative to treatment, and evolve to maintain
and enhance their relevance.

Let me illustrate the dilemma by citing a fascinating paper
from Milton Weinstein’s group at the School of Public Health, published
earlier this year (Hunink, M. et al, JAMA 227:535, 1997). The study evaluated
the impact of two types of intervention, preventive and therapeutic, on
mortality rates in cardiovascular disease, specifically coronary artery
disease. Between 1980 and 1990 there was a reduction in deaths of 34%
in the populations studied. The question addressed was what was responsible
for that striking reduction in death from coronary artery disease. Surprisingly,
they found that only 25% of the reduction in deaths could be attributed
to primary prevention. The vast majority of deaths averted derived from
the application of curative medicine. As biomedical research and technology
produce new tools, some expensive, hopefully others not, that keep people
alive and signficantly improve their quality of life, I believe this finding
may anticipate others in the future. In this context, the distinction
between prevention and treatment will become more ambiguous and an ideological
attachment to only a narrow definition of prevention may limit the scope
and relevance of the field of public health. 

Two kinds of research 

The president of the Royal Society, Lord Porter, liked
to say that "there are two kinds of research, applied research and not
yet applied research." Twenty years ago, there was a major debate in medicine,
led by Thomas McKeown, who wrote of a book entitled The Role of Medicine:
Mirror, Mirage or Nemesis
, that argued that increases in life expectancy
in this century, perhaps 35 years at the time he wrote, could not be attributed
to any known medical interventions. The vast majority of that extended
life expectancy, he speculated, had to be due to changes in nutrition
and the environment. It was his judgment that biomedical research had
contributed virtually nothing. That view still endures. In a press release
on tuberculosis from the World Health Organization, their director of
tuberculosis research made the following statement: "Money is wasted on
[research] projects that will be neither practical nor effective. For
example, there is widespread misallocation of resources as well as underfunding.
Donors have continued to fund narrowly defined biomedical research that
will simply be too costly to be practical." Narrowly defined biomedical
research! As someone who has engaged in biomedical research for 30 years,
I don’t know what that is, because I don’t know what broadly defined biomedical
research is. I think I have some sense what good research is, although
my own view can often be admittedly shortsighted. I find it shocking that
such a position is promulgated under the logo of the World Health Organization,
one of whose missions is to bring the best in science and medicine to
people around the world. 

Let me pursue McKeown’s thesis from the perspective of
tuberculosis. First, I must note that mortality statistics in the United
States did not become nationally compiled until 1900. From the point of
view of national mortality statistics since 1900, he would appear to be
right, even for tuberculosis. There has been a steady decline in mortality
since 1900. But if one examines the New York City Department of Health
statistics on tuberculosis, which began their extraordinary and meticulous
health records in 1800, it is interesting to note that mortality from
tuberculosis was an almost straight line at a level of 400 deaths per
100,000 population from 1800 until about 1885, when the curve started
its decline. Is it coincidental that this decline, associated as you well
know with the beginning of the public health movement in this country,
corresponds with the discovery of the tubercle bacillus in 1882 by Robert
Koch, and the more general acceptance of the germ theory of disease? Or
is the decline in TB at this time the result of some mysterious change
in the environment or nutrition that spontaneously occurred and which
no one has yet been able to identify? 

Let us consider the position of the WHO TB programme, and
ask whether there is, indeeed, any longer a need for biomedical research,
narrow or broadly defined, in tuberculosis? Perhaps they wish to argue
that new tools are no longer needed, because the present strategy is so
effective at curing cases. Tuberculosis is a disease that has an epidemic
cycle of 100-300 years. With the best tools currently available, Directly
Observed Therapy (DOTS) for six months with three or four drugs under
supervision, it is going to take a very long time and a lot of money to
reach all the people in the world who need it. Let me point out that there
is currently not a single rapid, inexpensive diagnostic test that can
be employed in the field to detect TB cases or ascertain drug resistance.
In a world in which one-third of the global population is infected with
the tubercle bacillus, if there were a drug or vaccine that acted to kill
the persisting bacilli in latent or dormant infection and prevent reactivated
disease, the 100- year epidemic cycle could be reduced to a 10-year cycle.
If we had an effective vaccine to prevent infection or disease, we would
certainly stem the epidemic. I do not wish to belittle DOTS–it is clearly
the best tool available today for addressing the problem of tuberculosis.
My point is that even when one has adequate tools, there is likely to
be a continuing need for research. 

There is no better example of that maxim than the experience
of a closely related disease, leprosy, where the WHO Leprosy Unit exhibits
a totally different mentality about research. Because of indications of
a major rise in bacterial resistance to monotherapy with dapsone, in the
1970s WHO recommended multidrug therapy with three drugs. In 1973 there
were approximately 12 million registered patients with leprosy. In 1983
there were 5.4 million registered cases, and about one-half of all those
who had formerly been on lifetime treatment could be discharged from treatment
as cured. There are now fewer than 1 million registered cases. The recommended
regimen was six months treatment for paucibacillary (tuberculoid) cases
and two years treatment for lepromatous or multibacillary cases, and the
treatment clearly worked. But the WHO Leprosy Unit and the Tropical Diseases
Research Programme did not announce that they no longer needed research,
or call a press conference. They continued to experiment and do research.
Two weeks ago, they broke the code of their latest trial which was designed
to learn how short a treatment could be given with a new combination of
drugs. Using two new drugs plus rifampicin, they learned that in patients
with single-lesion disease, a single administration of drugs was as effective
as six months’ treatment. The implications in terms of compliance and
cost are, within the context of that disease, staggering. Lifetime treatment
was reduced to six months treatment and is now reduced for many to one
day’s treatment. The message here is that even with a treatment that was
effective, there was a need for more research and an opportunity for significant
improvement. 

On "narrow biomedical
research"
 

Recombinant DNA technology, and much of the revolution
in modern biology, that I hope will bring health benefits to every person
on the planet, derives from a laboratory experiment that Joshua Lederberg
carried out in the 1940s. Lederberg was not seeking to do anything useful
or practical, but rather to understand sex in bacteria, or more specifically
the nature of recombination in bacteria. The original experiments of Kohler
and Milstein that produced the first monoclonal antibodies were similarly
designed to ask a basic question. They found that fusion of a myeloma
tumor cell with a differentiated primary somatic cell type, B lymphocytes,
generated an immortalized cell that continued to express antibodies. This
experiment was particularly remarkable, since cell fusions with other
types of cells had extinguished expression of differentiated functions.
The studies of Bernard Moss and Enzo Paoletti aimed to understand the
molecular basis of the pathogenesis of smallpox, which by that time had
truly been extinguished from the face of the earth. By molecular genetic
manipulations of the vaccinia virus, they created more-attenuated strains
and the concept of multivaccine vectors that could be used to deliver
antigens protective against multiple infections. It is almost certain
that one of the first AIDS vaccine trials to enter efficacy trials will
use a recombinant vaccinia virus. More recently, the failure of gene therapy
in some experimental studies was found to result from the production of
antibodies to the gene product. As discouraging as that may be from the
gene therapy viewpoint, it has given rise to the newest type of vaccines,
naked DNA vaccines, that are inexpensive and, at least in experimental
animals, remarkably effective at inducing a wide variety of host immune
responses to individual antigens encoded by the DNA. These are simply
a few examples, well known to all of us, that some of the most important
practical applications derived from pursuit of fundamental scientific
questions. 

If one were to project where biomedical science is likely
to make contributions to health in the future, the one certainty is uncertainty.
Nevertheless, while your list may be more accurate than mine, I would
expect that the human genome project, in addition to providing an invaluable
roadmap to every gene and the organization of the genome, will have the
potential to reveal every genetic predisposition within an individual
for disease susceptibility and resistance. Neuroscience, in uncovering
the fundamental mysteries of mind and cognition, will address what is
projected to be the second largest burden of disease in the 21st
century, depression and mental illness, and hopefully result in new treatments
and preventives. Combinatorial chemistry permits synthesis of a half million
new compounds per week in a single laboratory, more than any pharmaceutical
company previously could generate before it merges with an even larger
conglomerate or undergoes a leveraged buyout. This new approach is accelerating
both drug screening and rational drug design. Developmental biology and
oncogenes will hopefully allow understanding of neoplastic disease, and
lead to better cancer treatments and preventives. Communication technology
and the analysis of large linked data bases will allow studies of interventions
that affect a great many people, which could accelerate the validation
of new interventions and their incorporation into public health. My general
point here is simply that there has to be scope in public health to accommodate
and foster appropriate respect for the entire range of contributors to
public health–researchers, physicians and health care providers across
the health spectrum. As Robert Oppenheimer once said, "It is a profound
and necessary truth that deep things in science are not found because
they are useful. They are found because it was possible to find them." 

The topology of
health
 

There is another imprint of their education that many
of my colleagues trained at schools of public health carry within the
deep recesses of their cerebral cortices, which frequently becomes patent
among those who represent international donors and overseas development
agencies and oversee international health programs. What they learned
is that for a program to be good, it must be "horizontal," i.e. delivered
within primary health care, and that any program that is "vertical" must
be a dreadful thing, distorting of primary health care systems and infrastructure.
This has become, in my judgment, a kind of mindless mantra in public health
ideology. Let me point out that the global eradication of smallpox, oral
rehydration for diarrheal disease, the entire expanded program for immunization
against childhood infectious diseases, the onchocerciasis control program,
and the hookworm eradication program of the Rockefeller Foundation in
the US, which found that putting shoes on kids was better than any medical
intervention, were all originally vertical programs. The equally important
point, however, is that once they were shown to work–and perhaps only
then–it became possible to integrate them into primary health care strategies.
I would simply urge that this question be looked at in a longer-term context,
and that the topological ideology not be slavishly worshiped to the detriment
of pragmatic and constructive alternatives. 

Topology deals with surfaces, and there are more pressing
core issues that I believe have not been adequately addressed by schools
of public health. The one that I am most concerned about here is the issue
of equity–health equity within countries and between countries. I am
gratified that equity figures in many of the presentations at this Symposium.
Let me again refer to an example from the world of tuberculosis. A classic
study of Karen Brudney and Jay Dobkin at Columbia Presbyterian Medical
Center in New York analyzed 224 consecutive patients with tuberculosis
at the Harlem Hospital in New York in 1988 (Amer. Rev. Resp. Dis.
144:745-49, 1991). They found that the case completion rate was 11% (we
don’t really know what the case cure rate was because there was no two-year
follow up). There is probably no developing country in the world that
had a less effective control program than that in New York City in the
late 1980s. If one looks more deeply at the patient population, as they
did, perhaps one finds some of the explanations. Eighty-two percent of
the patients were unemployed, 53% were alcoholic, 45% were homeless, 40%
had AIDS or AIDS-related syndromes. This is health inequity in the richest
country in the world. 

The inclination of most people presented with such data
would be to infer that that problem is most likely attributable to the
lack of access to health care. If there were only greater access, this
type of inequity would disappear. Alas, there are some extraordinary data
that would suggest that lack of access to health care is not likely to
be the whole story. The classic study of death rates in Chicago in the
1960s as a function of personal income (Kitigawa E.M. and Hauser, P.M.,
Differential Mortality in the United States: A Study in Socioeconomic
Epidemiology
. Harvard Univ. Press, 1973) indicated, not surprisingly,
that mortality rates in the highest income sector in the population was
very much lower than in the lowest income sector of the population. However,
at virtually the same time, the famous Black study was being conducted
on death rates as a function of professional status in the United Kingdom
(Townsend P., Davidson, N., amd Whitehead, M., Inequalities in Health:The
Black Report and the Health Divide.
Penguin Books. London, 1990),
and it yielded almost identical results. Professionals there had the lowest
death rates and unskilled laborers the highest. But in Britain, every
one of those individuals had access, in fact, to the National Health Service.
Understanding and resolving equity disparities in health, then, is not
a simple matter. The causes may be structural or biological, cultural,
political, economic, lack of access, or knowledge of how to "work the
system." My caution is that these need to be meaningfully delineated,
if equity and health are to be improved. Public health schools should
be wonderful places to do that, and ought to take the lead. In the course
of that pursuit, it may emerge that some of the factors that are most
important to improving health may be ones that the health sciences and
health professions have little power to affect, and that the identification
of others in which we do have a major role to play will present important
opportunities. In the pursuit of equity we must also maintain a sense
of integrity, and a perspective of what academic public health can, and
cannot, do. 

An issue of global
health equity
 

Investing in Health Research and Development revealed that the
greatest burden of disease occurs in developing countries in terms of
lost years of healthy life, but only 3.6% of the health research in the
industrialized world is directed to problems specifically affecting the
people in developing countries. That is an unconscionable inequity in
itself. One of the great and colorful politicians of the state of Massachusetts,
Tip O’Neill, used to say, "All politics is local." Too many of our colleagues
in science and public health, and probably in every other field of endeavor,
believe that their business, too, is all local. If there were a single
new concept that I could wish to be imprinted on every public health school
graduate, it would be that "all health is global." In a recent report
of the Institute of Medicine’s Board on International Health, America’s
Vital Interest in Global Health
, which I had the pleasure of co-chairing
with Dean Fineberg, global health was defined as "health problems, issues,
and concerns that transcend national boundaries, and may best be addressed
by cooperative action." One would think that in the richest country in
the world there would be great support for global health, particularly
in light of America’s great tradition of humanitarian concerns. Apparently
that has not been sufficient. In a ranking of the top 20 OECD countries
in terms of their percentage of gross domestic product (GDP) spent on
overseas development assistance, the United States scored at the bottom
of the list. In absolute terms, the United States, the world’s largest
economy by far, ranked fourth –not the strongest argument for the great
humanitarian tradition of this country. Yet, in America’s Vital Interest
in Global Health,
Dean Fineberg and I learned that there is, in fact,
a considerable interest by the American public, consistently reflected
in opinion polls and surveys, in helping the poorest and most disadvantaged
people of the world. But that vision appears not to be reflected in the
actions of our politicians. The chairman of the Senate Foreign Relations
Committee has been quoted as saying that foreign assistance is like "pouring
money down a rat hole."

Consequently, the IOM report explored another approach, namely identifying
reasons of enlightened self-interest that support the argument that the
United States should take a more active role in global health. Three types
of arguments were adduced: Protecting our people, enhancing our economy,
and advancing our international interests. With respect to protecting
people, the need for global surveillance to protect against emerging infections
and drug resistance is perhaps most obvious, and would benefit people
in all countries of the world. A second advantage of global health activities
to protect our people is to gain scientific knowledge that cannot be obtained
domestically as easily or cost-effectively. For example, NIH-sponsored
acellular pertussis vaccine trials were done in Europe, where the whole-cell
vaccine was not given in some of their immunization programs, providing
a unique opportunity not available here. This is real value-for-money.
The knowledge gained on the effectiveness and safety of acellular pertussis
vaccines is a public good that will benefit children all over the world.

A second recent example: The apparent success, albeit imperfect, of combination
drug therapy for HIV-infected individuals in the industrialized world
has made clear to all that because of the cost, this advance will have
little impact on the 90% of people infected with HIV who live in developing
countries. The impact of drugs in the industrialized countries has helped
to focus attention on the need to develop a new intervention that would
be applicable to developing countries, specifically AIDS vaccines. The
prevailing expectation for an AIDS vaccine for many years has been to
engender sterilizing immunity, thus effectively preventing people from
becoming infected. A closer examination of existing vaccines, however,
indicates that few, if any, achieve protection by totally preventing infection.
Rather they prevent disease. Many immunologists are coming to the view
that protection against HIV infection is not going to be easily possible,
or perhaps even an appropriate trial endpoint. Nevertheless, there is
a hope, deriving particularly from studies of live attenuated SIV vaccines
in monkeys and long-term human survivors, that it may be possible to engender
protection against disease, without preventing infection. Monkeys immunized
with certain mutated SIV strains that persist at low levels are not protected
from infection with virulent strains, but do not develop disease. It is
my view that while it will be possible to test vaccines of this concept
for safety in the industrialized world, because of the availability of
the combination drug therapy, any patient in a vaccine trial in the industrialized
world who, despite counselling against risk behavior, gets infected with
HIV and exhibits a viremia, will ethically have to be offered combination
chemotherapy. If that therapy proves to be effective in suppressing the
virus, we will never know whether the chemotherapy or the immunization
was responsible for the protection achieved against disease. Consequently,
one must infer that it will be very difficult to do long-term, large-scale
HIV vaccine efficacy trials in the industrialized world. The countries
that have the greatest need for a vaccine are many of those that do not
have the ability to acquire the expensive drugs–namely, the developing
countries. Our knowledge of protection against disease may only be tested
in developing countries, which, if trials are not done well, will inevitably
raise ethical concerns. This is the second example where knowledge of
enormous value to addressing the needs of populations of the richest and
poorest countries of the world can only be acquired by scientific cooperation
and collaboration between the technologically advanced countries and the
countries with the greatest burden of disease. 

I mentioned the fact that through global health investments
we can sometime achieve remarkable knowledge and value-for-money in research.
The paradigm of Chile provides another example of value-for-money from
the study of health around the world that I would love to see elucidated.
Chile had a per capita income of $5,019 in 1990, identical to the per
capital income of the United States in 1900 (using inflation-adjusted
figures). The life expectancy in the United States in 1900 was 49 years.
In Chile, in 1992, it was 74 years. How can Chile obtain that many healthy
years of life from that level of per capita income? Perhaps there is as
much knowledge to be gained in studying the social and economic aspects
of health from a global and international perspective as in scientific
studies. 

On the future of public
health
 

I would like to end with four reflections. One of the occupational
hazards in the field of public health is the knowledge, imprinted on each
of us during our education, that we do good work. We know that we are
engaged in good causes, and consequently too often indulge tendencies
towards self-congratulation, self-righteousness, and perhaps complacency.
That self-satisfaction in the biomedical community resulted, about a decade
ago, in a dramatic reduction of support for research. At one point the
president of the United States actually impounded funds allocated by the
Congress for research, although these were later released by the Supreme
Court. That situation has changed. There has been an active participation
of all the biomedical societies, individually and in coalitions in, as
you well know, a very difficult economic time of trying to reduce the
federal deficit. In a series of polls, Research! America found that 8l%
of the population felt that the federal government should support basic
science research, even if it brings no immediate benefits. It also revealed
that 77% of the people polled would willingly pay one dollar a week additionally
to support biomedical research. There are no comparable data of which
I am aware in the field of public health. One of the things that I believe
is not adequately imprinted by schools of public health in their educational
program is the crucial need for advocacy. There is no more heroic person
on this planet that a New York City public health worker, or a public
health TB case worker going into crack dens to provide DOT, or people
providing vaccines to children in the most remote regions of the world.
Yet, there is frighteningly little understanding or appreciation of public
health in the public consciousness. Everyone at this symposium goes at
some time to Washington or to your own capital city. How often does any
of you arrange to talk to your elected representatives or their staffs,
to tell them what you do and how important it is, and ask for their support?
The lack of appreciation of the importance of public health is not the
fault of your societies. Every one of us has to make our case for federal
and local support for what we do–and we have not done it well. 

With the emphasis of public health schools on enhancing
the technical and scientific skills of their students, and on improving
the cost-effectiveness of the health system, there is a great potential
risk that our students–and we ouselves–may lose the sense of wonder
about what we are privileged to do, and the unique perspective that make
us functionally useful to society. I love the comment by Margaret Cately-Carlson,
president of the Population Council, made at the World Summit for Children
in 1992: "The GNP tells you everything about a country that is not important.
It does not inform about the beauty of the countryside, the joy and value
of its music and art–or the health of its children." Schools of public
health must above all nurture that sense of wonder and awe. 

The best argument I can provide to justify a research
component in public health thinking derives from the World Bank’s World
Development Report, 1993: Investing in Health.
There appears a figure
that plots life expectancy of many countries versus per capita income,
normalized to 1991 dollars, for four periods of time: 1900, 1930, 1960,
and 1990. These curves, I believe, reveal two profound truths. The first
is that for people who are very poor and have very low per capita incomes,
minuscule increases in per capital income lead to striking rises in life
expectancy. Minimal efforts to relieve poverty, particularly of the poorest
people in the world, have a profound influence on their life expectancy.
The second inference is that no matter how rich one was in 1900, or how
much disposable income one had, there were simply 25 years of life available
in 1990, that one could simply not buy in 1900. I would argue that it
is knowledge about public health in the broadest sense, acquired between
1900 and 1990, that was responsible for that 25-year increase in life
expectancy. Such knowledge cannot be bought only with money. It requires
enormous commitment, effort, and imagination. Generating that knowledge
also requires great institutions. The Harvard School of Public Health
is a great institution. All of you here have contributed, and will, I
hope, continue to contribute to this great institution. Clark Kerr, who
created the University of California and made it great, providing extraordinary
opportunities for students of all backgrounds and incomes in the State
of California, once wrote that "In Western civilization since the 14th
century, with the exception of the Protestant and Catholic Churches, only
eight institutions have survived in recognizable form–the Parliaments
of Iceland and the Isle of Whyte–and six great universities." I would
like to believe that half a millennium from now that list of universities
will increase, and that there will be a few schools of public health on
it–including the Harvard School of Public Health.