The other day I wrote up some comments about a recent article from George Whitesides. If you’ve heard him speak on the topic of organic synthesis, you’ve probably heard most of what’s in that piece, but it’s a good summary of his position. Picked up roughly where I left off last time, he has this to say about innovation:
One measure of the health of a scientific field is its ability to generate new ideas (as opposed to extensions of already established themes), and to reinvent itself. A familiar idea in discussions of innovation is that it comes in different forms: for example, innovation can focus on new technology (where organic synthesis has tended to shine), or on new processes (where the most innovative work has often been done by process‐development groups in industry), or new business plans (for example, the decision by China to make low‐cost capital available for production of silicon‐based solar cells – a decision that has been enormously important in accelerating the implementation of solar energy). The question facing organic synthesis is not “has the need for new methods of syntheses disappeared?” but rather “What problems – intellectual, empirical, or practical – most require new ideas in synthesis?” Is the future for more of the familiar – what Kuhn called “ordinary science” – or for something more radical, more important, more different fundamentally? (More, perhaps, having the audacity of what Woodward, Eschenmoser, and others suggested and demonstrated 50 years ago?)
That’s an uncomfortable question, when you start to think about it. That’s not asking organic chemists what they can do, but what the most important and interesting questions are that they can contribute to. And it’s also asking, “Of the biggest and most important questions in general, which ones can organic synthesis help with?” Whitesides lists some of those in broad strokes (catalysis, materials science, synthetic biology, automation/mechanization of organic chemistry, etc.) and in more particular ones (molecular recognition, origin of life studies, sequence-specific polymers, new biocompatible materials, and more). It may or may not be a coincidence that what many people think of when they think of “organic synthesis” – total synthesis of natural products – does not impinge nearly as much on these topics as some of its practitioners might think.
So what are the most important questions that natural products synthesis can provide a key role in helping to answer? One that I can think of is unraveling complex biochemical pathways where more simple chemical matter just doesn’t seem to be able to make things clear. I would adduce rapamycin and FK-506 as examples of this, and there are many others. Indeed, some of the larger pharmaceutical molecules are getting into “non-natural-product” zones of complexity and molecular weight (although, to be sure, they’re generally much easier to make, since we’ve produced them (or their precursors) with that in mind. Modifications of the natural products themselves is another such field, and it’s not an easy one, either.
These are worthy topics, and there are others. But at this point, I want to being in another recent article, from Phil Baran at Scripps, introducing a special collection of total organic synthesis papers. This introduction is written by someone who’s well acquainted with criticism of the field. Interestingly, he and Whitesides are in agreement on what some of the interesting problems are (automation being one example), but that agreement definitely doesn’t go all the way. That’s because Baran’s article, as mentioned, is deliberately written as a defense of total synthesis, and it reads at times like a response to a prosecutor’s opening statement.
I agree with some of what Prof. Baran has to say as well. I think, for example, that he’s absolutely right when he says that the application of AI and automation to really complex molecules is still a long way off. We might disagree on just what a “long way” measures out to, but there’s no doubt that retrosynthetic planning of such molecules and their actual forward synthesis is a really significant challenge that only humans – and pretty damned competent humans, at that – are now able to meet. (Drug-sized molecules are another matter). Of course, Prof. Baran and I are in agreement about many other points as well, a big one (mentioned above) being the use of such complex molecules to work out biochemical pathways. There’s often no alternative, and there are several fields that would be in much worse shape if synthetic chemistry hadn’t evolved far enough to deal with such structures.
The key place where I think Baran and Whitesides, though, do not really come to a meeting of the minds is in the question of “Why?” Some of the responses given in Baran’s article – total synthesis trains students well, industry likes to hire people who do it, it’s a solid way to prove compound structures, it’s beautiful in and of itself – are the same justifications I was given when I was first working in the field in the mid-1980s. And it’s not that time has falsified all of these, but it may have made some of them a bit less compelling. It may seem odd to say it, but for some time I bought into this worldview completely, and even now I don’t completely reject it. But sometimes, I think it seems to the total synthesis community that you’re either for them or against them, and that apostasy is always a short, fatal, step away. The shortest and most fatal of those steps is wondering in general if total synthesis of natural products still pays its way, scientifically. Here’s Whitesides again:
. . .The trick will be to find classes of problems that return complex synthesis (Organic Synthesis, perhaps in an evolved and more expansive and ambitious form) to a central role in the future of the field, rather than having it become an extraordinary specialty or craft, admired but occupying an increasingly isolated place as the rest of synthesis moves on. The argument that complex synthesis, by itself, is beautiful is doubtless true, but also dangerous. Most societies have valued beautiful products of human imagination and skill, but paying to support the artists who produce them has been another matter entirely. And, unfortunately, the beauty of Organic Synthesis is not something that most non‐synthetic‐chemists can understand.
Technical expertise is not, by itself, enough to sustain a field (consider mechanical watchmaking or glass‐blowing). To prosper, Organic Synthesis must also solve recognizable problems.
That exact argument for beauty is one of the ones made in Prof. Baran’s article, actually. It’s not his main point – actually his main points and those of Prof. Whitesides might well end up being closer than you’d think – but it does represent the sort of sticking point that keeps coming up between practioners of the field and those outside it. I’m outside it, and have been for many years. I can understand it and appreciate many of its qualities, but I’m not able – unfortunately – to tell people that its best days are yet to come. They might be. But they might not.