AS WE HEAD INTO THE 21ST CENTURY, IS THERE STILL VALUE IN TOTAL SYNTHESIS OF NATURAL PRODUCTS AS A RESEARCH ENDEAVOR?
Clayton H. Heathcock
Department of Chemistry, University of California
Berkeley, CA 94720-1111 USA
This year (1994) marks the 50th anniversary of the publication of the total synthesis of quinine (1) by Woodward and Doering . This accomplishment was the first of a series of increasingly ambitious total syntheses by Woodward and his students and ushered in what has been called the "Woodwardian Era" of organic chemistry. The outstanding synthetic successes that were realized during the 1940s and 1950s, first by Woodward and then by a number of other talented organic chemists, gave birth to a whole new sub-field of chemistry - "Natural Products Total Synthesis".
The ground rules of the game of Natural Products Total Synthesis were simple. In the beginning of the Woodwardian Era, the very existence of an unsynthesized natural product was sufficient justification for its synthesis and a successful total synthesis was viewed as a final, decisive step in the establishment of the structure of a natural product. However, for this rationale to be valid, it was important that the synthesis be well-planned and that the chemist only employ reliable, well-understood reactions - ones that were not likely to give unexpected results and thereby diminish the value of the synthesis as a proof or confirmation of structure.
The advent of x-ray crystallography, one-dimensional NMR spectrometry, and, perhaps most importantly, two-dimensional NMR spectrometry, has changed this situation. In today's world it is a rare synthesis that contributes to our knowledge of the structure of a natural product. As the value of total synthesis as a tool for structure proof waned, practitioners of the Art sought and found a new raison d'être, namely that the practice of total synthesis can often yield unexpected results. The case was made effectively in 1963 by Woodward himself in discussing the earlier demise of classical structure elucidation by chemical degradation in a footnote to his classic paper on the synthesis of strychnine :
"Of course, men make much use of excuses for activities which lead to discovery, and the lure of unknown structures has in the past yielded a huge dividend of unsought fact, which has been of major importance in building organic chemistry as a science. Should a surrogate now be needed, we do not hesitate to advocate the case for synthesis."
A corollary of this philosophy was that chemists could be more daring in their choice of synthetic tools. In other words, if the structure of the target is absolutely secure, and the total synthesis will not provide further information on this point, the synthetic chemist can take chances with unknown reactions and unproven strategies. The focus of a total synthesis is shifted to the chemistry used in the synthesis, and the specific target serves to enforce a certain discipline on the chemist. That is, for the synthesis to be successful, the exact structure of the target must be synthesized, even if this structure is not easily amenable to state-of-the-art strategies and tactics.
As the field of Natural Products Total Synthesis burgeoned, the related discipline of "Synthetic Methods Development" was born. In this field of research, chemists sought to invent new procedures for accomplishing various synthetic chores, such as introduction and modification of various functional groups, construction of carbon-carbon bonds in sundry ways, control of relative or absolute configuration when new stereocenters are created, etc. Although some of the new synthetic methods that have emanated from these activities have found commercial applications, to a large extent, the field of Synthetic Methods Development has served mainly to support practitioners of Natural Products Total Synthesis.
In the past decade or so, we have witnessed a number of highly impressive total synthesis accomplishments. Notable among these are the epochal conquests of vitamin B12 by Woodward and Eschenmoser  and palytoxin by Kishi . These signal achievements, and many others, have caused many observers, at least in the United States, to question the value of continued research in the area of synthesis, both total synthesis and methods development. In a previous article, I have commented on the situation as follows :
"If important fields such as medicine, biochemistry, and materials science are to continue to progress, it is essential that we be able to synthesize literally any structure that the imagination can conceive. The goal of research in organic synthesis is to reach a level of sophistication where this ability can be taken for granted. Yet, there is abroad an insidious notion that organic chemists have already become so adept at synthesis that further academic exercises such as that described here are no longer necessary, that there is no longer any need for research in multi-step synthesis. I believe that, in part, this difficulty stems from a confusion of the adjectives effective ["adequate to accomplish a purpose"]  and efficient ["performing or functioning in the best possible and least wasteful manner"] . In fact, although chemists have over the last half-century become rather adept at constructing small amounts of very complicated molecules, we generally cannot prepare most desired organic compounds in an efficient, practical, and truly cost-effective manner. We can synthesize almost any given molecule and demonstrate that we have done it. However, this is due more to the development of high-powered separation and analytical tools (hplc, capillary glpc, tlc, FT nuclear magnetic resonance spectrometry) than to some discontinuous change that has come about in our ability to solve synthesis problems. That is, because we can carry out separations and establish structure with minute amounts of material, it is possible to do synthesis on an order-of-magnitude smaller scale. Thus, we can carry out multistep syntheses in a much shorter period of time than was possible ten or twenty years ago, since more time can be devoted to developing new chemistry and less to the time-consuming `bringing up material.' This maturity should be considered a normal step in the development of a productive science, not a sign that all of the problems have been solved and that the field no longer merits investigation. Problems of synthesis still abound, as is well known by anyone who practices the art. Our textbooks are filled with hundreds of synthetic methods, all of which have limitations that will never be discovered unless the methods are tested in the arena of challenging multifunctional synthesis. Although our approaches to problems have matured, we need even more mature strategies of synthesis. There is no reason that organic chemists should not be able to surpass Nature's virtuosity in the synthesis of complex organic structures. In fact, we are still very far from this goal in most cases."
Thus, when confronted with the task of chairing a Panel Discussion on some aspect of organic synthesis for this NATO Workshop, I chose as a topic the rhetorical question that is the title of this chapter. As panelists for the discussion, I selected five distinguished participants in the Workshop: Paul A. Bartlett (Berkeley), Derek H. R. Barton (Texas A&M University), Ronald Breslow (Columbia University), Albert Eschenmoser (ETH), and Stephen Hanessian (University of Montreal).
At the outset, and to serve as a sub-topical guide for the discussion, several questions were posed to the panelists and audience. A spirited discussion, involving panelists and members of the audience alike, occurred over a period of about three hours on a rainy Thursday afternoon. In the following pages, I attempt to capture the essence of the major points that were touched upon during this lively exchange. Comments are organized along topical lines and not necessarily in the order in which they were made in the discussion. Although the following condensation was made from a tape recording of the actual discussion, statements have been heavily edited and condensed for the purpose of this chapter.
2. Does total synthesis still have value as a method of structure determination?
In the Introduction, it was stated that ". . . it is a rare synthesis that contributes to our knowledge of the structure of a natural product." However, there are still many cases in which synthesis is the best way to gain structural information, particularly when stereochemistry is an issue. For example, the synthesis of the "C-40 archaebacterial diol" (2) in 1985 did establish both the relative and absolute configurations of this novel natural product, which does not crystallize and is so conformationally mobile that spectroscopic methods cannot readily provide stereochemical information .
Another good example is found in Schreiber's recent synthesis of the immunosuppressant discodermolide, which established the absolute configuration of the natural product to be 3 .
This total synthesis also led to a "dividend of unsought fact." By using essentially the same synthetic protocols, Schreiber's group was able to prepare both the natural and the unnatural enantiomers of discodermolide. Amazingly, it was found that both enantiomers inhibit cell proliferation, but at different concentrations and by different mechanisms! It is probably fair to say that this remarkable fact would have never been known had not chemists gone to the trouble to carry out a 36-step synthesis of discodermolide and its enantiomer.
3. Is total synthesis an appropriate vehicle for educating students?
This point was not specifically listed as a sub-topic of the discussion because I had assumed that it would be obvious to all that one undisputed value of total synthesis research is that it is an effective means of educating young scientists. In my opening comments and later, I said:
"Now it seems to me that there is no debating the fact that multistep synthesis is a good training vehicle for students, those who are going to go into medicinal chemistry, for example.
"I have trained many graduate students and postdocs who have worked on total synthesis projects, and most of them have gone to work in the pharmaceutical industry. They are highly sought after. The people in industry really value this kind of training, for several reasons. First, multistep synthesis, persisting in order to find an effective path to a specific target molecule, develops experimental skill because you aren't allowed to make many mistakes. That is, you have to get your material through the 10 or 15 or 20 steps without losing it. Second, you are exposed to a wide diversity of chemistry. Finally, I think that solving a problem of this sort builds character because the student regularly faces barriers and must find ways through or around them."
Panelist Eschenmoser commented along similar lines:
"In my experience and in the experience of many young synthetic chemists who have spent Ph.D. time with total synthesis, this kind of research is among the best in giving a young chemist a very broad survey of what is the most important quality organic chemists can bring to natural or molecular science, namely their way of understanding reactivity. The process of preparing a structurally-complex target molecule by chemical synthesis confronts the young practitioner with so many different and difficult reactivity situations that the education that results from the experience is probably the major payoff of the work."
The question was put in a slightly different form for the panel by Dr. W. Rutsch, of CIBA-GEIGY:
"Do you think it is fair and right to do natural product synthesis to educate young chemists? Is this a good tool to train them? Do you think that after such training these students are properly equipped to solve the problems that will face them in industry? After all, we in industry and you at the university are not isolated entities. We are affected by public opinion. The chemical industry at the moment has a very bad reputation in the public opinion. I don't know about universities. The question should be: What does natural product synthesis contribute to the public opinion about chemistry? Or, in other words, can we justify spending taxpayer's money doing elegant natural product synthesis? Might there be other important problems of society that should be solved before we go into natural product synthesis?"
To this question of "relevance," I replied as follows:
"These students go to Merck or Pfizer or Lilly or Abbott or one of the many other companies and make a big salary and pay lots of taxes. In just a few years they pay back in taxes all of the money that other taxpayers have paid to educate them. Furthermore, for the rest of their lives they continue to pay taxes on their salaries, which are higher than they would be if they had not been so educated. Therefore, I think that total synthesis is both a good tool for education and a good deal for the public. We turn out scientists who are highly qualified and who do good things for society."
Panelist Bartlett responded to the relevance issue with the following comments:
" It's worth elaborating a little bit on this issue of practical application of the research that we do in academe. I am often asked why we don't direct some of our enzyme inhibitor design approaches towards more medicinally relevant enzymes rather than study such common enzymes as thermolysin and carboxypeptidase. After all, we don't really need a better inhibitor of our digestive enzymes. For example, why did I not work on the angiotensin-converting enzyme, which is a zinc peptidase just like the ones I have described in my lecture? My response is that I have made a conscious decision to avoid enzymes with which I would be competing with professionals. The goal of industrial research is to come up with practical compounds that can be turned into drugs to earn money for the company. The product of industrial research is profit.
"But profit is not the goal, or should it be the product, of academic research. Our products are ideas and well-trained students, who can go to industry and solve relevant problems. If we really want to understand how a protein binds a small molecule, and how to design the best inhibitor of an enzyme, thermolysin is just as useful as the angiotensin-converting enzyme.
"Furthermore, commercial drug discovery carries with it a lot of constraints, things such as patent coverage, pharmacokinetics, oral bioavailability, human safety, etc. It doesn't seem to me that it is appropriate for one or two graduate students in my research group to try to compete with 20 chemists at Merck and 15 chemists at Bristol Myers in trying to develop a real drug candidate."
Panelist Breslow introduced another element into the discussion of education:
"Yesterday a student asked me how we can encourage and train people to be creative. Of course, that is an absolutely critical element of education and we simply must do it. I think most American universities require their students to do research proposals. At Columbia we even require research proposals outside the student's research area. But everybody, especially the students at this Workshop, should be listening to the seminars given not just to see if they understand them, but also with the question of what you could do in the area of the seminar. After you hear a seminar, you should think about whether you could do something better, or at least use that material in your own work. If you do this and if you attend a lot of seminars that are not just in your own special area, for example, in various parts of biology, you will acquire the breadth that you need. But it has to be a creative breadth, not just an amassing of facts."
The discussion of total synthesis and education was carried in yet another direction by panelist Eschenmoser:
"During my generation total synthesis was heavily executed and large numbers of chemistry students were involved in it, profiting from that quality in education. However, it is to be admitted that we educators missed one important point - we didn't teach our students how to recognize a research problem. We gave them the target, that was the problem. Therefore, I think educators must pay more attention to teaching their students how to identify significant problems."
Professor V. Snieckus, of the University of Waterloo, posed the following question for the panel:
"How do we go about training students who have the perspective on the one hand and are solidly trained in their specialty on the other hand? On any given day a synthetic organic chemist is thinking so hard about the next step that he usually does not have the time or the possibility to look at the other side of the fence. How do we encourage students to recognize problems that are more general, and still be very good as synthetic organic chemists?"
Panelist Breslow responded to this question as follows:
"That is a very important issue. I think there is no question that the student or postdoc of tomorrow must be a person of many talents. If we just teach chemistry, and only chemistry, if we expose our students only to that discipline, we are doing them a disservice. There has to be at least some exposure, some appreciation, some sensitization to things other than chemistry. I am not saying that chemistry graduate students who are doing a synthesis or doing something that is entirely organic should also be expert pharmacologists or molecular biologists. However, in any University there are other departments and other courses than organic chemistry. Even if each student takes only one or two other courses, such as introductory biochemistry, that could be very useful. Many departments have introduced Special Topics courses. For example, in my department at Columbia, we have introduced a special course entitled `Topics in Medicinal Chemistry.' We bring in colleagues from industry to give lectures about different subjects. So I think we can't close our eyes and say we are organic chemists and we do what we do and just forget about the rest of the world. I think it is important that we expose our students to as much as possible."
4. What are some of the great unanswered questions in organic chemstry, and can total synthesis play a role in finding answers to these questions?
Panelist Barton began the discussion of this topic with the following comments about practical challenges that still face us in synthesis:
"The real problem in synthetic chemistry remains as it always was. How do you get 100% yield and 100% stereoselectivity in every reaction? This is the problem that every industrial chemist faces daily. They have a synthesis; they need 100% yield. It solves the pollution problem, because you have nothing to throw away afterwards. It does all sorts of things. What are we doing about getting these 100% yields?"
Panelist Breslow pointed out that chemists have found it difficult to identify field-wide problems, as is commonly the case in other branches of science:
"Chemistry has two unusual problems compared to some other fields. If you are a high energy particle field physicist you are really trying to find out if the unified field theory is correct or you are trying to find the last unknown boson. That is, the field has just a few central problems and if you are not pursuing one of these few goals you are not considered to be doing serious physics. On the other hand, chemistry is both lucky and unlucky in the sense that we don't have any such central questions. You can imagine formulating some, but they are very general, like what is the relationship between structures and properties. You can't take this seriously as a single target that we all can address, nor could you make a clear statement that you have actually solved the problem. So we have this tremendous diversity and not everyone agrees on what the important problems are. Some people may think that developing new methodology is terribly important; others that it is important to figure out crystal structures, or whatever. There are all sorts of things people think are important to do in organic chemistry. And that is both our strength and our weakness, because we can never say `Well, that was clearly a great problem, and now we have solved it!'
"The other problem we have is that we are not a natural science, in the sense that more than 95% of all known compounds are compounds chemists have made; that is pretty much also true of chemical reactions. In this regard, chemists are very different from other scientists. That is, what is the `synthetic astronomy'? What is the `synthetic geology'? This aspect of chemistry is very difficult for other scientists to grasp. They ask `why are you working on this problem? It is not a natural problem. Is it just a problem you have dreamed up? Are you just amusing yourself?' But, of course, we are not. We are really interested in all the chemistry that is possible, not just the chemistry that Nature happens to present to us. I think that one of the arguments against working only on the synthesis of natural products is that the richness of chemistry has grown by its extension beyond Nature into other areas, the creation of new polymers, not just biopolymers, the creation of new properties, not just the properties that came along in Nature. It is difficult to explain this to the public because they think we are just inventing problems in order to solve them, like doing crossword puzzles. But we have to explain that this really is not so, we are a very special science, and we are different from other sciences, and even other scientists sometimes don't understand what it is we do."
Panelist Bartlett expressed some concern about laying out agendas for people to work on, as follows:
"I am a little bit worried by the idea that we should try to predict or prescribe what we should do in the future. In hindsight, much of what we do turns out to be useless. The corollary is that ahead of time, we don't always know what is going to turn out to be useless. And whether we are working in organic synthesis, whether we are trying to understand noncovalent interactions, whatever endeavor we undertake, I don't think we are going to be able to tell ahead of time exactly what it is we should do. I think we have to let people's creativity drive them and time will tell what have been the important contributions."
However, panelist Eschenmoser challenged the audience with one grand, central problem:
"In the history of natural science, natural products synthesis has played a very special role, the demystification of nature. It started with the synthesis of urea by Wöhler in 1828 . The effect of that synthesis led to the feeling we can do it; namely, make compounds that are produced by living matter. Let me take a big jump, to vitamin B12 and palytoxin. Again, these Woodwardian Era total syntheses marked a step in demystification, namely that we can synthesize essentially any natural product if we just want to. That is, in the Woodwardian Era, the gradient of `structural complexity' was the direction chemists followed to find their targets. The natural continuation of this gradient would have been chemical synthesis, on a very broad basis, of biopolymers. However, this procedure of identifying targets was vigorously cut off by the discoveries in molecular biology.
"In my opinion, there is a problem that is central to organic chemistry alone and in which biologists cannot help us. We all agree in this Workshop that the emphasis in synthetic research is shifting toward the synthesis of properties, and not just compounds. Now, the most important property that we can attack by synthesis is the property of living. The problem, rigorously a problem of synthesis, is to study the laws, the rules, and the principles of self-organization of organic matter. We, as synthetic chemists, know that every step in a well-planned synthesis involves, in principle, a self-assembly process. We simply set the stage so that the participants of the synthetic step can assemble themselves. The big problem is to arrange the stage for self-organization leading to a whole cascade of steps without external interference. That is, we should strive to set the stage so that the products resulting from the first event of self-organization are programmed to assemble themselves for a second step, and so on.
"That is, in essence, the problem of self-organization. In this Workshop, we have seen that there are two rather different kinds of self-organization. One is non-covalent self-organization, which biologists strongly depend upon. The other is covalent self-organization, which is a problem of synthesis.
"You may say that understanding how life originated is a dream that is going too far, that we will never know how life originated. However, my belief is that the statement `we can never know' is nothing more than an opinion. It is our duty, our task, to deal with this uncertainty. I would guess that we can realize in organic chemistry a model for self-organization that led to life within perhaps a few decades. Perhaps in twenty years organic chemists will be able to present a system in which self-organization happens. We should not continue to leave that problem to the biologists and the physicists. When I participate in symposia on self-organization, I find physicists and biologists who burn with the question of understanding how organic matter self-organized toward life and both recognize that actually the problem is one of organic chemistry. But there are only a few organic chemists at these symposia. This is unfortunate. We organic chemists have already once abdicated a most beautiful, most important problem of natural product chemistry to non-chemists. I speak of the DNA helix. To recognize how Nature stores information by that base-pairing was probably the most important problem Nature had in store for chemists. But it was biologists who solved this beautiful chemical problem. There is nothing wrong about that; after all, we are just part of science. But I sometimes wonder how students would view organic chemistry today if they could read in their books that organic chemistry solved the problem, if not of the helix itself, at least of the principal of base pairing, which is a rigorously organic process.
"You may say that in order to tackle such a problem we must know what life is. No! It is exactly one of the goals of this kind of research to find out what life is. Because life can be rationalized fully only when we can understand its beginning. This is the opportunity of organic chemistry to contribute to this central question."
5. Given the past accomplishments in total synthesis, what kinds of total syntheses are appropriate in the future? What kinds of total syntheses should not be pursued?
As panel moderator, I ventured the following opinion on the question of kinds of total synthesis projects that are counter-productive:
"There definitely are kinds of total syntheses activities that people should avoid. One of our problems is that many practitioners don't exercise sufficient judgement about whether a synthesis represents an improvement over prior art. It damages our collective image when someone publishes a total synthesis of a compound that has been synthesized several times before, and the new synthesis is twice as long and uses steps that proceed in poorer yield. This kind of total synthesis does not represent an advance, but is really a step backwards.
"These inferior syntheses are not usually created on purpose, but begin with a good idea that just doesn't work out. The chemist then does whatever possible to complete the synthesis, usually involving a much longer and more cumbersome route than was originally envisioned. In the end, we have an inferior synthesis that is published anyway. I think that this is a practice that we should reconsider. It would be better for the field if people would just bury those projects as failures and not carry on just to get a publication that does not represent an advance in our ability to do synthesis.
Professor Carl Johnson, of Wayne State University, responded to this point of view as follows:
"I just want to make a brief comment on your suggestion that many total syntheses should be buried. I think that is a disservice. When one tries to develop a strategy for the synthesis of a molecule and the strategy doesn't work, sharing this failure can be just as stimulating to other chemists as sharing a success. Publication of a failed idea points out weaknesses in our tools and chemistry can benefit from having these weaknesses identified. Of course, we have to reach a reasonable compromise between these two positions. I do not take the position that everything that is tried should be published and I don't think that you really think that every total synthesis that didn't go off exactly like you thought it would, or didn't beat the last one in overall yield or number of steps should be suppressed. In short, I think there is merit in sharing failures."
I responded to Professor Johnson's comments as follows:
"There are two kinds of situation in which synthetic organic chemists give the impression that this is some sort of activity that we do for our own amusement, that we are not really trying to further science. For example, the following scenario is not uncommon: A chemist whose primary interest is developing new methods has a good idea for a new reaction, tries the reaction, and finds that it does, indeed, work with some generality in simple situations. The chemist then looks around for some natural product target to serve as an advertisement for the new reaction. He finds a compound, say the mating pheromone of the red leaf moth, and proceeds to carry out a multistep total synthesis that features the new synthetic method as a key step. The synthesis requires a total of 15 steps, one of which is the newly-invented reaction. The problem is that someone has published ten years ago a three-step synthesis based on much simpler chemistry. In fact, I think that people who develop methods should show that the invention is an advance by solving a problem that cannot be solved as easily using existing knowledge.
`The other common scenario is the synthesis that is based on a novel method or strategy, and which starts out well but bogs down along the way because the protecting groups don't work out or something of that sort. We end up with a long, unwieldy synthesis, one that starts out well but ends like a `land war in Asia.' This doesn't do the field of synthesis any good. Why not just publish a Note about the novel method or strategy itself. Why slug your way through a 50-step synthesis of strychnine now that Overman has made it in 15 steps. I think it would be best to cut your losses, publish your method and then get onto something that really is new again."
"Whatever the reason, when we publish in 1994 a long synthesis that is inferior to a shorter, 1984 synthesis, we appear foolish to those looking from outside into our field. As Professor Breslow put it, we appear to be `. . . just inventing problems in order to solve them'."
Panelist Barton spoke on the question as follows:
"R. B. Woodward used to believe in planned synthesis. He had the kind of mind that could integrate the knowledge of the day better than anyone else and he really could plan a long synthesis and, frequently, execute it. Now a days, I don't think that we, in the academic world anyway, should go in for planned synthesis with known reactions, known reagents, and known principles. However, we must also recognize that good things can come by accident, even out of a well-planned synthesis and the orbital-symmetry correlations that came out of the vitamin B12 synthesis is a good example of the unplanned fruits that can come from a planned synthesis. So let us not be too dogmatic.
"Of course, there are some natural products, particularly those from marine sources, where it is extremely difficult to get hold of enough to do any biology. In this case there would be a justification for total synthesis, even if it is planned along fully predictable lines.
"Furthermore, I think we should make a distinction between what our friends in Industry should be doing and what people in Universities should be doing. I think in Industry a planned synthesis is a very good thing to do. Because if you can execute that synthesis with greater than 90% yield in every step, you will certainly have a satisfactorily planned synthesis. But in the University, we are not supposed to be doing useful things like that because we are supposed to be original. As a University scientist, my general rule would be `if you know how to do it, you shouldn't do it.' Instead, you should try to find things that you don't know how to do and solve those problems."
Dr. I. Ujváry, of the Hungarian Academy of Sciences, made the following statement:
"I would like to suggest three criteria for an appropriate total synthesis; `the three Es of total synthesis.'
1. Essential, in terms of providing essential chemical information, structure information, or biological information.
2. Economical, in terms of yields (100%), use of environmentally-friendly reagents, and requiring few steps.
3. Elegant, in terms of its intellectual content and artistic impact."
Panelist Eschenmoser responded as follows:
"Art is always a bonus to synthesis. It is marvelous that we have this bonus, but there is, I think, a kind of obligation of chemists to be serious about the question of what we are doing. An obligation towards the public. We have to seriously analyze whether we are doing right or whether we undergo apparitions that have to be stopped. And therefore I think that the artistic aspect of a synthesis, beautiful and marvelous as it is, should not be a justification for carrying out a total synthesis. As Einstein put it, `Let elegance be the affair of tailors and cobblers.' If your problem is truly essential then you don't care about the elegance. The more essential your first E is, the less important your last E becomes. Fortunately, we do often encounter elegance and beauty and art in our profession, but that is not our justification for doing synthesis."
Dr. J. P. Snyder, of the Institute for Research In Molecular Biology in Rome, addressed the panel as follows:
"I was most excited by the suggestion of Professor Eschenmoser that the really large and unsolved problem of the origin of life might be a target in which to use total synthesis as a tool. However, if synthetic chemists are really to make progress toward solving such a large problem, I think they need to expand their horizons. I work for a small company here in Italy and our goals are to cure diseases, particularly the diseases of osteoporosis, hepatitis, problems of depression, AIDS, and so on. When a young synthetic chemist comes into our company, we no longer describe them as chemists, but as scientists. Such individuals have some interesting opportunities, because in order to really get one's teeth into a big unsolved problem like the origin of life, one must use ideas and concepts that come from other disciplines and integrate those ideas and concepts with the principles of organic synthesis. And so I would suggest that where total organic synthesis might come to have meaning above and beyond the circle of chemists alone is in situations where there is tight intellectual integration, a creative approach to using these tools to solve truly unsolved problems that affect the lives of large numbers of people. This is applied not only to problems in chemistry but in a vast range of disciplines. But this will require that you no longer identify yourself merely as a chemist, but as a scientist. You must to use all of the tools of science, not just synthesis, but whatever is available to solve the problem. It seems to me that is where synthesis is likely to play the greatest possible role."
Dr. W. Ripka, of Corvas International, in San Diego, spoke as follows:
"I thought Professor Eschenmoser's statement of purpose was really eloquent. This is the sort of thing we need more of in chemistry, an overall theme of what we are trying to do. A lot of what we talk about tends to be somewhat fragmented. Many people are doing parts of what Professor Eschenmoser said. Certainly, Paul Bartlett is with his work trying to understand why small molecules bind to large ones. Certainly, Professor Breslow's work on artificial enzymes is another component. But I think it is very important to have an overall theme as to why we are doing these things. And I thought Professor Eschenmoser's explanation of that in terms of self-organization is exactly the type of thing that we as chemists should do more of. I should like to ask the panel, all of whom are academics, how well do you think the academic community is doing in terms of setting the kinds of overall goals of the kind Professor Eschenmoser expressed?"
I responded to Dr. Ripka's question as follows:
"I think the academic community is answering the challenge only partly. I do think there is a group of people in academe who are synthesizing for some reason that I can't really categorize other than self-enjoyment and have lost sight of the fact that they should be trying to improve chemistry. There was certainly a time when it was exciting to conquer a molecule, just like it was exciting to climb the Eiger. But it has been demonstrated time and again that we can climb these mountains. We have invented all kinds of very creative crutches like protecting groups and very expensive reagents, like selenium instead of bromine, and things of this sort. We now have to drop some of these crutches and try to get back to using fundamental materials and doing things without protecting groups. That is really the challenge for the academic community. I don't really think it is important that the molecule I work on be biologically active or have importance to materials science. I think it is important that I try to find creative new solutions to complex synthetic problems. I think that there is some considerable activity in the academic environment in creating new ideas and new methods, but I also think there is a lot of `turning-the-crank, mundane, just-do-it-and-publish-it type of research. It is this sort of activity that has brought criticism to the field."
6. To what extent can the values of natural products total synthesis also be realized if we direct our efforts instead toward the synthesis of `unnatural' products?
This subject came up many times and in many forms during the discussion. A clear statement of the situation was made by panelist Breslow in his opening remarks:
"I would like to put the question in the most negative way I can and then I will come back to a more positive view of it. Let's imagine that you are explaining to someone who is not a chemist what you do when you are a synthetic chemist. They say `Oh, that's very exciting You make all sorts of new molecules, and it must be very interesting to find out their properties.' You say, `No, we only consider it to be synthesis if we make known compounds. If we make new compounds, that doesn't count. And there is a very serious rule that exists in many quarters that only the synthesis of natural products is a true synthesis, because it is the only one that has the challenge that you don't invent your target.' So then the person says, `Well, that's interesting. But if the material is fairly rare, even if already known, perhaps your synthesis contributes to the supply.' You say `No, we often use relays, and we consume more of the final product than we actually make, so the result of the synthesis is a decrease in the world's supply of the material.'
"Now, this makes total synthesis sound fairly crazy, so what is the argument in favor of it? I think there is a value, and that is in having a specific, predetermined target. We are not permitted to put in an extra methyl group or to leave a methyl group out just to make the synthesis easier. We must make exactly what's there, and if we don't know how to do it, we had better figure out how to do it.
"Since this is a principle value of total synthesis research, it follows that there is no great argument for saying that once a compound has been made the problem is solved. Morphine and strychnine have each been synthesized several times, and each new synthesis that contributes new insights and new chemistry is as valuable as the first synthesis. That is, the value of a total synthesis is not just that we have conquered another mountain.
"Thus, natural products synthesis does have value because of the discipline that is enforced by the necessity of preparing the target in exact detail. My research group does a great deal of synthesis. However, whereas our synthetic targets generally have structural details that are highly desired, other parts can be varied without much effect on the desired property. Thus, we can modify our target somewhat to take advantage of available methodology or to avoid serious synthetic problems. When I am feeling particularly self-effacing, I contrast what we do in synthesis with what natural product synthetic people do. They have a specific target and they fire an arrow at it and try to hit the bulls-eye; we shoot an arrow into the wall and then we paint a bulls-eye around it.
"However, I do strongly object to the idea that the only valid synthesis is the synthesis of a naturally-occurring target. That definition is too restrictive. There are many other perfectly good synthesis targets, and synthetic work directed at these targets will not only advance biology or materials science, but will also advance chemistry. We are not yet a service science; at least that is not our only function. We have serious things to do within chemistry itself. Important molecules that will answer serious theoretical questions in organic chemistry remain to be made."
I addressed the audience on this point as follows:
"I would like to reiterate Professor Breslow's observation that there is value in the enforced discipline that comes naturally in the synthesis of a natural product. I call your attention to one slide in Professor Bartlett's lecture about rational design of enzyme inhibitors. You will recall that, using his CAVEAT program, Professor Bartlett designed a molecule that he thought might fit nicely into a certain enzyme active site. The problem was then to synthesize this complicated potential inhibitor and test the theory. However, you will recall that the actual compound that Professor Bartlett synthesized had an extra methyl group on the benzene ring. Now, this methyl group was predicted to be totally out of the picture in the enzyme-inhibitor complex, so it really shouldn't matter if it is there or not. Professor Bartlett jokingly told us that this methyl group was introduced because of the `EOS factor,' meaning `ease of synthesis.' That is, it was a lot easier to synthesize the molecule with the superfluous methyl group than the simpler structure without it.
"This situation exactly illustrates why natural product synthesis is more valuable for the purpose of furthering synthesis as a tool than synthesis of equally complex structures that we just make up."
Dr. J. C. Orr, of the Health Science Center at the Memorial University of Newfoundland, spoke as follows on this issue:
"I would like to suggest that the editors here might devote a little section of their journals as a sort of `chemistry bazaar,' wherein those who are biochemists or biologists and need specific compounds could get together with synthetic organic chemists who are looking for projects. For example, I work in a medical school and quite often people come to me and say, `I would love to have this compound to test for certain biological properties. Do you know how it can be synthesized?' Often I am just too busy to sit down and do this."
I responded to Dr. Orr as follows:
"That is an interesting suggestion. However, recall Professor Barton's statement that if an academic chemist knows exactly how to synthesize a given compound, he shouldn't be doing it. I agree that we want to be making organic synthesis a better tool every time we do carry out a multistep synthesis. Therefore, if there were such a `dating-service' connecting biologists who want specific compounds with chemists who are looking for `relevant' synthesis projects, I would hope chemists would only tackle problems in which there is the opportunity to develop some synthetic method or strategy, or in some other way to add to our knowledge about how to do synthesis. Furthermore, I think it is important that chemists who really want to contribute to the improvement of synthesis as a tool avoid using the EOS factor, as Professor Bartlett put it. We must discipline ourselves to synthesize exactly the structure desired, and not make changes just to make the synthesis easier."
Panelist Breslow made the following observation on this question:
"Sometimes there is a tendency, particularly from those in the pharmaceutical industry, to say that anyone who has not been synthesizing natural products is not suited for work in that industry. I think that attitude is a mistake and one I worry about. An awful lot of what I do is synthetic organic chemistry. I wouldn't let a student graduate who had not made a new molecule, because synthesis is the one unique tool that only chemists have. Physicists and biologists can talk about molecules, but we can make them. We must never forget that we have this powerful ability, or leave it out of the training of our students.
"On the other hand, people should recognize that there is a significant amount of synthesis that goes on in many areas of organic chemistry, usually not identified specifically as synthetic chemistry. For example, in the molecular recognition business, students probably spend at least 80% of their time making the molecules they are going to study. I think that is an activity that ought to be recognized."
7. To what extent has computer-designed synthesis reduced the need for total synthesis research?
Although not specifically advertised as a sub-topic for the discussion, this question was brought up by Professor D. Arigoni, of the ETH, in the following way:
"I agree to a very large extent if not totally with Professor Barton's statement that if know you can do it, you should not do it. But I wonder from this point of view, Derek, how you (or other members of the panel) feel about computer-assisted total synthesis?"
Panelist Barton responded as follows:
"Well, I think that if it's in the computer, it's a known fact. So, if the computer predicts how you can do a synthesis, it will be a summation of known facts. That's fine. People in industry should certainly use that tool. I don't think it has value for people in the academic world because it just limits them to the use of known facts, known reagents, known reactions, and known principles."
Professor U. Jordis, of the Technical University of Vienna, disagreed with this view:
"I would like to disagree with Professor Barton's view of the computer synthesis planning. In my view, the computer allows you to ask new questions that you could not otherwise ask"
Panelist Breslow made the following observations about the value of computer-designed synthesis planning:
"Often when we devise a synthetic plan, we are so interested in the methodology or using a certain key reaction that we lose sight of the starting material. We tell ourselves we are going to find it in Aldrich or Fluka or something like that. Then at the moment of truth we realize that we had better see what sort of starting material we have after all. This is where computers might help. As human beings, we are limited with our sense of vision. We can't see everything even for a fraction of a second. Perhaps we can see it but then we lose it. And if there is a tool out there, be it a computer or a machine or something that can actually make me see things and freeze those frames on a computer screen to tell me here are some possibilities for you to choose from, without invading my brain, without telling me the first reagent is going to be this, the second is that and the third is going to be that. Just to give me a choice of starting materials, then I think that would be very interesting."
8. What about `biomimetic' synthesis?
Strictly speaking, `biomimetic synthesis' implies that one prepares a compound by the same method used by Nature for biosynthesis of the compound. However, chemists commonly use the term in a more general way--meaning that a synthesis is inspired by a probable or even possible biosynthetic construction of bonds. That is, it is often possible to deduce from the structure of a natural product what the starting material must be, and by application of sound mechanistic ideas about electron movement, it is often possible to propose a sequence of steps that might have been used by Nature. When a chemist is inspired by such considerations to design a synthesis, and then proceeds to reduce the plan to practice by experiment, this is often called a `biomimetic' synthesis, even if there has been absolutely no experimental work directed at determining the actual biosynthetic pathway.
Although the subject of biomimetic synthesis was really allocated to another panel discussion, the subject did come up several times. It was first introduced by panelist Eschenmoser as follows:
"I think it would be very helpful if Professor Heathcock would expose his two types of synthesis of the squalenoid alkaloids. What these syntheses show us is that we can greatly reduce the number of steps in huge synthetic projects if we pay attention to biomimetic ideas. That is, you can really go much too long a distance when you try to use vigorously unnatural chemistry to make a natural compound. Nature did not have so much freedom in producing her natural products. Indeed, Nature has apparently been restricted to a surprisingly large extent, and we should not start to synthesize really complex natural products without checking whether by adapting to the natural channels followed by Nature, we might be able to plan or achieve an optimal synthesis."
I repled to these comments as follows:
"Let me just make one observation about this because I think it is an example of the value of doing total synthesis of natural products. In the project that Professor Eschenmoser is referring to I spent probably five years trying to force designed chemistry using carbanions and other well-behaved organic reagents onto a structure. And it was only after four or five years, that some light dawned and we saw how Naturemight do this using some very simple chemistry and it turned out that this very simple chemistry works in the laboratory very well.
"In a way, planned syntheses using conventional reagents and biomimetic syntheses are related in the same way as the two methods for finding enzyme inhibitors, as described for us by Professor Bartlett in his lecture on Monday. You recall that he talked about `rational design', but he also described the `combinatorial' approach. When we approach a synthesis biomimetically, we are taking advantage of the biodiversity of Nature. Nature has had lots of time to be a process chemist and find the most efficient and most economical way to solve some of these big problems. Much of this chemistry is not known to us. At least its not obvious to us, and it is only by trying to solve these problems in the laboratory that we will perhaps discover some of this very nice, simple, environmentally-friendly chemistry."
On the subject of biomimetic synthesis, I would also like to quote a passage that was authored by Panelist Eschenmoser in the abstract of his classic article on the origin of the molecular structure of vitamin B12 [3c]:
"The goal is to arrive experimentally at a perception of the biomolecule's intrinsic potential for structural self-assembly. This potential, together with the specific type of reactivity related to the biological function, is considered to be responsible for the biomolecule having been chosen by natural selection. The chemical rationalization of the structure of biomolecules is an objective of organic natural product chemistry. The field of natural product synthesis provides appropriate conceptual and methodological tools to approach this objective experimentally."
It is not really possible to summarize a discussion such as the one held in Ravello on Thursday afternoon, May 12, 1994, but we can at least review some of the cogent points that emerged.
There was general agreement that total synthesis still does have intrinsic value as a method of structure proof in many cases, particularly where stereochemistry is involved. It was also recognized that it is sometimes the only way to obtain sufficient amounts of rare natural products with which to carry out biological experiments.
Furthermore, there seemed to be agreement that this form of research is an excellent way to train students, particularly those headed for careers in pharmaceutical chemistry or biological sciences. However, it was pointed out by several that we educators need to do more to teach our students just how to identify significant problems, and that we need to do more to encourage the kind of breadth that is increasingly necessary in the modern world of science.
The case was strongly made that, in spite of the recent significant achievements in the arena of total synthesis, we still have far to go before we can accomplish practical syntheses of any desired structure, no matter how complicated. We have come a long way from Wöhler's synthesis of urea to the Woodward-Eschenmoser synthesis of vitamin B12 and Kishi's synthesis of palytoxin. However, even these monumental synthetic feats are only big steps along the long road toward synthetic perfection. It will probably take another 150 years before chemists will be able to prepare non-biological compounds of comparable complexity in a truly practical manner. So there is still value in our trying to solve larger and larger problems by simpler and simpler means.
However, the point was also made that we must be aware of opinion in the community. Practitioners of multistep synthesis must continually question what they are doing; they must carefully evaluate their synthetic approaches to assure that each synthesis really does have the potential to teach us something new, be it a new method or a new strategy of synthesis. Professor Eschenmoser eloquently made the point that total synthesis has played an important role in the history of organic chemistry - the demystification of Nature. It would seem that the case has now been made and the time has past when we need to do fully planned synthesis solely for the purpose of convincing ourselves or the world that we can do it, that we can make anything if we are just willing to work hard enough.
The point was made that synthesis is a unique tool that chemists have, that this ability to make things to study, rather than just studying what Nature provides for us, sets chemists apart from other scientists. It was also pointed out that chemistry, unlike some of the other sciences, does not have an agenda of `big problems.' Along these lines, Professor Eschenmoser challenged us to use synthesis to address a really big problem - understanding how life began! This bold suggestion, particularly his ambitious estimate that we might achieve a model for the kind of self-organization that may have led to the beginning of life in just a few decades, clearly caught the imagination of many participants in the discussion and no doubt provided an inspiration that many of us took with us as we returned home to our own research programs.