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267  VIth International Fermentation
            Symposium 1980
           London - Ontario
     First of all, may I take just a moment to express my pleasure at
visiting the University of Western Ontario on its lovely campus here.
When I taught at the University of Wisconsin, whenever I did have
occasion to drive east, I would always choose the scenic route via the
lake Michigan Ferry, Detroit and London, and visit some of my old
friends here:  I hope Dr. Robinow is in the audience today.

     I am not going to be making any startling announcements of
further breakthroughs; you will have heard a number of those during the
course of these particular sessions.  Instead, my remarks are rather
what you would expect to hear at the closing end of the session, when
you are a little too tired to absorb still one more concrete datum,
and welcome a chance to relax and wind down.  Unfortunately, the 
airplane schedules didn't cooperate that, and so I am a little bit out 
of place at this front end of the program.

     The program committee challenged me to aggregate some of my own
thoughts on the strategies of further development in recombinant DNA
technology.  A session is being held right now in Toronto that is 
dedicated to futures; and I want to be sure that I am in the right 
symposium in the orientation of my remarks. My focus will be some rather
manifest elements in the logic of the existing science and technology.
This is moving so rapidly that we are contemplating a time horizon
with a median of perhaps five, or at most ten years, for further 
developments.  There will be some vexing exceptions; it isn't always 
possible to anticipate in advance just how hard a given problem is going
to be: but a number of things can be foreseen with some confidence, as
being the agenda of the next symposium of this kind within the next
few years.  There will be exceptions -- twenty years ago, many of us
believed we would soon advance from the cloning of a frog from somatic
cell into the egg, to the cloning of a mammal.  That has so far proved
not to be feasible.  Perhaps fundamental biological distinctions
between frogs and mammals, of which we are still not fully aware, 
impede those kinds of developments.  Similar pitfalls may affect 
extrapolation of DNA technology. However, if we look at the recent past,
if anything, the pace of events in the last five years has exceeded most
people's prognostications, even my own.  One loses one's breath trying
to keep up with the pace, not only in scientific, but in technological
developments in this field.

     May I take a few things as given for this discussion, without
depreciating the enormous ingenuity and diligence, insight and 
imagination that are involved in the development of the techniques?  
They are also very great fun, and I don't want to deprive anybody of the
opportunity to engage in those details, even though I am going to 
leapfrog over all of them just now.  My stipulation is that our 
appreciation of the structure of DNA and of a few of the enzymes, (I 
think we have far from exhausted them), that are involved in the
replication, in recombination, in repair, in splicing and so forth,
and in the regulatory factors that control those, permits us to plan 
the manipulation of DNA as if it presents only difficult but superable
technical problems.  It is very difficult for me to visualize an 
objective in DNA designs for which we cannot outline a plausible 
research program.

     Our strategic challenge almost unique in the history of
technology is less how than what!
    
     Many techniques other than DNA-splicing and implantation into an
appropriate vector are crucial for useful applications.  They include
the systematic fractionation of DNA, particularly from eukaryotes with
large genomes, the isolation of particular components, with the best
ways of expanding them; modifying those sequences in ways that open up
new lines of experimentation with respect to the products that one is
going to see; the confrontation of products in a variety of metabolic
pathways with one another, techniques.  For sequencing both in 
analytical and in a synthetic sense the desired intermediate and end
products.  However, I repeat, those are today fairly manifest technical
problems for which answers are being found every day.  We can put
it down that we have really a very thorough repertoire of procedures,
either in hand or very shortly in hand to do whatever is socially and
technically and economically feasible and desirable in those spheres.

     As we work our way through these problems, and for example, find 
ways in which we can assure fairly consistent expression of a sequence,
even at very low levels; we can of course then use the most 
sensitive, or selective procedures to isolate the rare progeny we   
seek.  We are already much further along today than we were two or  
years ago in this methodological infrastructure.

     How then we manage the development of this technology?  Our
orientation should not be confined to products themselves, but also
how these can be introduced, marketed, integrated into our science and
technology and our economy.  These issues deserve at least a small
percentage of the time that is now occupied with the technological 
feasibility of specific ventures.  Please recall too that DNA splicing
is just one of a host of techniques for doing genetic experimentation,
which began in a systematic way about 115 years ago with Mendel.
Hybridization is still the bedrock of genetic analysis in all organisms:
recombining DNA in the way that nature had evolved will still
play a very large part in all that we do in this field in a very wide
variety of organisms.  Still other technologies have to be thought
about: the development of chimeric or mosaic embryos, organisms which
contain not admixtures of DNA within a single nucleus but the allophenic
mice that Beatrice Mintz is making, where the embryos are constituted
from zygotes of a variety of origins.  This opens up another modality
of "genetic engineering", if you like, it begins to breach the boundary
between the somatic and the germ line in a given animal, permits the
introduction of genetic innovations into a germ line that would not
otherwise be feasible.  This can go on over a wide variety of other
ontogenetic technologies.

     The one development that I would neither advocate nor foresee in
any practical way is the direct application of gene modification to
human beings.  There has been an enormous amount of nonsense about
that, both at the level of technical feasibility and also of moral, 
political and practical and common sense feasibility.  One has to stop
and think what one would have to do to validate a procedure that one
would wish to advocate for the rectification of genetic disease in an
already existing individual suffering from a genetic defect.  I think
one sees immediately the impossibility of the situation.  How would
you ever set up a clinical trial that would enable you to demonstrate
that injecting DNA or any other such material into, say, a child with
sickle cell disease or cystic fibrosis or phenylketonuria was an 
efficacious and safe procedure, particularly in the face of competing
techniques that have a higher degree of predictability and assurance
and reliability - and I refer here particularly to pre-natal diagnosis
and preemptive abortion?  I think the moral imperative to prevent
the birth of defective children by our insight into the inevitability
of genetic disease in certain confrontations, in our ability to 
monitor those pregnancies with more and more specific and reliable 
methods for knowing just what the outcome of a particular gestation is
going to be, is an ethical categorical that overrides the possibility
of the clinical trials for the rectification of disease, once 
established.

     On the other hand we are going to learn a great deal about 
diagnostic human genetics, the understanding of the way in which gene 
alterations result developmentally and physiologically into a line of
defect, and how these can be mitigated by therapeutic measures as well
as by the preemptive ones that I have just indicated.  Diagnosis will
be the main role DNA of DNA technology applied to humans.

     Even more than the products we surely will make, the applications
to industrial microbiology, insight into the genome, particularly in
human beings but also that of economically important plants and 
animals will far outstrip what the products themselves are going to do.
For example, in the general domain of human medicine, there is no
disease that is not modified by the genetic composition of the host.
At one extreme, we have those single gene syndromes, of which 
phenylketonuria or sickle cell disease are prototypic, which are almost
directly determined by the genetic composition of the individual,
although even there, with some insight, we can learn something about 
environmental amelioration that will prevent the full development of
that syndrome.  So there is no disease that is purely genetic even in
those particular circumstances.  More important public health problems
are heart disease, cancer, psychiatric disease, and range of autoimmune
and related syndromes.  And for each of these we know that there
are important genetic factors that will influence the likelihood of
development of the disease, but know very little about specific genes
involved, although that knowledge is increasing rapidly.  I would 
submit that the extension of the techniques that have been introduced,
for example by Y. W. Kan for prenatal diagnosis of sickle cell disease,
the isolation of the DNA segment that is responsible for the 
determination of the structure of hemoglobin, that those techniques are 
already and very rapidly will be generalized to the total mapping of the
human genome and the ability to recognize correlations, not between
grandparents and their children or between siblings and one another,
which is an extremely feeble method of genetic analysis,but correlations
between the presence of a specific nucleotide sequence in a
chromosome and the emergence of disease with some probability in the 
individual carrying it.  That can then be used as a most effective
hammer and wedge to work out the biochemical basis of these syndromes
and the development of further therapeutic measures.  Even without the
benefit of DNA technology we have already made very great strides in
that direction in our elucidation of the mechanisms of deposits of
cholesterol in the arteries of atherosclerosis with the studies of the
metabolism of cholesterol, the identification of the carrier proteins.
There is a large school of people involved in this, particularly in the
work of Brown and Goldstein, looking at rare anomalies in cholesterol
deposition and how to pry loose basic mechanisms of cholesterol 
transport by the lipid protein systems of the blood;  their dissection 
and analysis have given us our most important lead on the actual 
pathogenetic mechanisms involved in that disease.  At that point we 
leave the genetics of rare diseases; we have used genetic insight as a 
method of biochemical and physiological  analysis, and I think one can 
expect very great promise from this approach in that context and as well
in the other major public health problems.

     Now on a somewhat mixed area of insight and products, I would 
put that the most telling challenge that we face in this field is the
systematic survey of the approximately 100,000 different proteins of
which the human organism is constituted again using the kinds of 
technology which are available to us at the present time.  We know of 
that set a few dozen that have been characterized well, that is to the
extent that we have got the amino acid sequences and the crystal
structures and so on, and we have a reasonable awareness of perhaps
100 to which names can be attached; we can talk about a specific
entity that constitutes an enzyme or a structural protein or similar
functional constituent, perhaps a couple of hundred might be put in
that category if we include some of the polypeptides.  So you can see
we have barely scratched the surface, because in order to approach
that kind of dissection we have generally had to relate a structure
and a function simultaneously; if we are talking about an entity which
is present to the extent of less that 1 per 1000 of the total protein
composition of a cell, you have to know what you are looking for in
order to be able to isolate it; you are not going to get at it by
gross chromatographic separation, you simply do not have enough
material available using our present techniques.  The cloning of the
corresponding messengers is in principle a pretty straightforward task
for developing this library or cataloging of the essential constituents
in relation to the particular organisms that they come from, and a 
variation of functional states can be examined at the level of the 
messengers, and I think this becomes probably our most important new 
tool in the examination of human physiology and biochemistry starting 
from that genetic perspective.

     Of those 100,000 proteins, we already know only a modest 
sprinkling, perhaps half a dozen, well enough to know that they have a 
therapeutic application.  These are some of the biologicals that have
been produced for some time, insulin; growth hormone; interferon is
emerging in this context.  We use a very dirty material, because we
have no better, for prophylaxis for hepatitis, so we call it mixed
human gamma globulin.  We use a slightly cleaner stuff, which may be 
1 per 1000 pure and call it RhoGamma R and use it as a prophylaxis for
Rh disease.  And then we have the hemophilia proteins and there are a
few more.  And there I have almost exhausted the human biologicals
which are available today as therapeutic entities, because we are
trapped in a vicious cycle of not knowing about them because we didn't
have them, not being able to validate the therapeutic efficacy until
they are available at some point.  And then in many cases, as for
example, human growth hormones, we are facing almost insuperable
difficulty in getting enough material from human sources in order to
really try them out effectively for therapeutic purposes, so there is
a great deal about the biology and the therapeutics that has simply
not been accessible to us in that way.

     We will hear more headlines in future like the interferon story; I
think it has become quite evident that that is an exciting wrinkle;
but there really is no firm reason to believe that it is the panacea 
that one would like to observe; there is nothing in the history of the
development of the subject to give one confidence that it was likely
to be or to have been the major answer to the problem of the control
of cancer.  It is a member of considerable class of substances of
which we are only slightly more than vaguely aware, that regulate the
growth and function of cells in the immune system and macrophage system
and whether it, or any one of a number of several hundred alternatives,
is going to end up being the final candidate for the most efficacious
application remains to be seen.  So the door has been opened up a
crack and has given us a prototype of a very large family of
potential alternatives, and we have now a way to break the vicious
cycle of finding enough of these substances and producing them in 
sufficient quantity to try them out, to be able to make our deliberate
choices as to which candidates for more extensive trials.

     Biologicals, generally, have always posed some rather difficult 
problems of certification, validation, reliability, purity and safety.
In many cases, we use what we have because they were the best that
seems to be available, although I question whether we couldn't have
gone further in areas like vaccines, which are terribly dirty materials
even today, although they are far better than they were 5 and 10
years ago.  There is no reason in the world why those should not be
produced as chemically and biologically homogeneous materials and with
some prospect both of greater efficiency in vaccination and with some
possibility avoiding some of the serious side effects certainly, we
should be able to avoid the more trivial ones of response to 
contaminating proteins and so on.  Similar considerations apply to the
gamma globulins that we use today; pooled human blood as a source of 
material without specific fractionation for chemical entity - I think we
will look back 10 or 15 years from now and wonder how we could have
been as barbarous as we have been now in using materials of that kind,
but one can say we didn't have many alternatives.  But those are the
alternatives, of course, that are most evidently opened up now to DNA
technology because those are products that we know have a therapeutic
application - there is no problem about discovering a market for them,
we simply have to go out and learn how to produce these.

     I would just like to put in a note of hope that we have a 
technology that is not only economic and efficient and rational, s
but gives us the opportunity to examine these issues of validity and 
certification and identity and purity to a degree that we have not had 
before.  And certainly part of any program for the production of a human
protein using a microbial fermentative process ought to have built into
it the demonstration of how you know that the stuff you make tomorrow
is the same you made yesterday, in your trials with it, in respect to
its homogeneity.  And then the delightful point is that producing it
through such a rational approach, we really do have the fundamental
tools to answer that question.  It is going to be in fact easier to 
demonstrate the chemical homogeneity of the protein product.  I think
we are going to find that there will be mutated insulins and mutated
interferons that might or might not be consequential when introduced
chronically into human subjects, that would pose great difficulty 
unless you knew what you were looking for in identifying them in parts 
per hundred contamination, and would not be difficult at all to 
demonstrate that at the level of genetic composition of the organisms
producing them.  But it is my hope that if these issues are opened up
early, that the appropriate and entirely feasible methodology will be
built in from the very start and prevent the kind of aberration that
could result in a backlash against the entire field.

     If we go to other lines of application of these technologies (and
here I will be treading on ground that is much more familiar to many 
of you than it is to me), I think we run into some problems about the
way that our economy is structured, that may provide very great en-
couragement to some of the wonderful things I have just been talking 
about in medicine, but do not provide quite the same degree of support
in other important areas.  I am rather discouraged in particular by
agriculture innovation, because the development of new crops does make
it an area for perhaps more direct government, that is socialized, in-
intervention in order to meet social needs, but I think it is a matter
that we should all be concerned about.  Similarly, we already have had
proposals, and I think they are just the beginning, about the way in
which restructured organisms could be absolutely, indispensable in
environmental clean-up, and there again the problem of how to get
return on investing in development of such a business in the private
sector.  This is a serious obstacle to eliciting the same kind of in-
ingenuity and industry and diligence and capital investment and so forth
that we do have on the productive industrial side.  So I think these 
are some of the structural problems that we should be thinking about
and how to make the most use of these technologies.

     Resource conversion is in a somewhat intermediate state in that
respect; it is hard to see how you are going to make a business out of
efficient garbage disposal except by heavy taxes on present effluents;
although of course our sewage plants already reflect a certain 
ingenuity in using what nature has to offer us by way of microbial 
intervention.  There will be a few commodity chemicals that will emerge
as new products not being made, not merely improvements over existing 
procedures, but I guess I remain somewhat skeptical whether fermentation
systems are really going to be as important in biomass conversion,
in producing fundamental feedstocks and so on, as they are in
the production of specialty materials of very intricate structure, 
whether the organic chemists and the application of physical and 
chemical methods of conversion and the handling efficiency and the rates
of conversion that one can get at higher temperatures, the use of 
specialized reagents and so on, isn't going to overtake what we have put
in this field.  That is something that is susceptible to alternative
argument.  One would like to see more fundamental analyses of process
cost and process flow, not only in of what is done now, but what are
the horizons, what are the margins, what are the limitations for con-
version processes along these lines?  I think we need those as 
strategic markers in order to indicate what feasible technology there is
going to be in particular areas.

     I also think that industrial microbiologists ought to be looking
over their shoulders about competition from other organisms to conduct
some of the conversions that are certainly much easier to program and
much easier to initiate using microbes.  Again, if I think about the 
process handling that is involved in the production of a specialty
protein, I wonder if I wouldn't rather grow a few plants in my garden
in order to produce a kilogram of some protein modification that might
be represented in the seeds, than to establish a sterile fermentation
tank to yield exactly that result.  This is not the large-scale 
manipulation of crops, the development of a dwarf rice or whatever; but
it is asking if we can go as far as we have gone, and then one step
further, into the modification of the plant genome, wouldn't we solve
a lot of production problems with microbes?  My preference would be
something you could graft onto a tree in order to produce specialty
outputs.  the same generalization might apply to a class of organisms
that has been grossly underestimated, except in some primitive, 
indigenous cultures; and these are invertebrates like termites, 
earthworms and so forth which have enormous capability for biomass 
conversion and which have the capacity for mechanical handling of those
materials that may exceed what we can do economically with a ball mill 
and so on.

     One of the fundamental challenges that faces us now altogether is
the very pace of innovation; the field is growing so explosively that
the pace of new scientific and technical insight exceeds by far the
rate at which new processes can be brought to market, and by still a
further order of magnitude, the pace at which it is possible to get
through the regulatory controls that those materials that are involved
in human medicine will certainly have to face.  And that may be one of
the most important strategic decisions that this community has to
address.  Anything that you start now will take five years before you
can bring it to term - what are the chances that it is going to be 
obsolescent by the time you are even half-way there?  And I think in
many areas the changes are very high.  I think the only possible
answer to this is a rather intergrated approach to the development of
the field that is not just devoted to creamskimming of specific 
scientific opportunities, but which is very thoughtful about the 
integration of the academic and scientific and technical aspects of 
these developments. To do that properly, in my view, is going to require
development of new systems for the interaction of the academic and the
industrial and the government world, which must be pursued within the
framework of the strategic issues I have just begun to discuss.
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