I’ve been thinking a lot lately about Jacques Tati’s masterful 1967 work Play Time, which describes an antiseptic, colorless and angular world of the future, a bleak world that only relents when the characters get together for a drink. It’s always been one of my favorite films, and it occurred to me recently that it can be seen as a metaphor for today’s big pharma. This is an industry that has lost its soul. And the one thing that can save it is having time to play—because play is the only reliable path to innovation and the only way to avoid the catastrophes of hype-based science.
In my last blog, I suggested that pharma’s troubles are caused by businessmen with no understanding of the nature of the business they serve. (My key analogy was John Sculley, the man who pumped up Apple sales while systematically killing that which made Apple great.) An interesting point, however, was raised by a colleague who commented that while it was true that mismanagement had hurt the industry, a good scientist can find a way around management nonsense. What he found far more disruptive is management actively interfering in science—that is, managers who think they can make decisions on the content of his work, rather than the process by which he has to do it. These content decisions invariably come about by buying into the hype behind a scientific fad, as opposed to a process-oriented management fad, and so this blog is about hype-based science and how to avoid it.
Because of the windfall from pharma’s profit surge from 1995–2000, there’s really no shortage of examples of scientific snake oil: combinatorial chemistry, high throughput screening (HTS), kinases-based drug discovery, bioinformatics/human genomics, fragment-based drug design (FBDD), systems biology, etc. Although investment in each has reaped very little reward, I am sure there are many reading this thinking, “Wait a minute, I use those techniques, they aren’t snake oil!” But in my opinion, each of these has largely been hype-based science, with little to show and plenty to answer for. And attention and resources have been squandered that could have actually made drug discovery more scientific and, eventually, more of a process—the “domestication” of drug discovery, a term I happily borrow from David Shaywitz and Nassim Taleb.1 How much closer are we to rational design than we were twenty years ago? Hmmm?
Am I saying that bioinformatics or, say, FBDD are useless? Not at all. Most hype-based concepts do occasionally, eventually deliver; why should hype-based science in drug discovery be any different? What I am claiming is that a dangerous confluence has occurred in our industry, a confluence of weak scientific management and, more important, the stifling of the natural tendencies of real scientists to explore and understand new ideas—in other words, to play. Play sounds terribly wasteful to management, who are generally interested in immediate results. Since starting OpenEye, I’ve seen it largely vanish from modeling groups. Yet play is how you work out substance from hype, it’s how you get new domain knowledge that, properly used by management, saves you from disaster. Without it, management is likely to make bad scientific decisions—typically because they don’t know better and because their personal interests are too easily aligned with those selling the hype-based approach. How much easier to look like you are an inspired manager by catching the next great technological wave instead of actually managing scientists? How visionary, how far-sighted and, usually, how sadly wrong.
I’m going to go through my list of hype-based approaches, one by one. Although some have actually proved useful, I would claim this is either despite the hype or because the original proposition had mutated in the light of real-world frustrations. There are considerable commonalities here, enough so that I propose a set of litmus tests that should be applied to any newly proposed concept that make extraordinary claims.
Let’s start with the worst: combinatorial chemistry. Watching the industry get wild about combinatorial chemistry was like watching one of those disaster movies where a train goes off the rails while on a bridge over a deep canyon. Wonderful spectacle if you aren’t on the train. Completely useless? Worse waste of chemical resource and talent of the last twenty years? The original concept—making libraries of millions or even billions of compounds, either separately or in mixtures (to be deconvoluted later—yes, that worked so well)—was stupid from the get go. Why? Because it doesn’t matter how many compounds you make; what matters is how many drugs you make. What happened is that corporate collections became stuffed with literally millions of useless, barely soluble molecules. A common theme of most pharma hype debacles is illustrated here: the idea that more must be better, without any accounting for quality. Experience and expertise eventually led the field away from the concept entirely and towards parallel and robotic synthesis, and a more careful enumeration of useful reactions.
High throughput screening (HTS) was a natural counterpart to combinatorial chemistry and pharma’s reoccurring binges of compound acquisition. Want more drugs? Just screen more compounds. I suppose that would work if you screened more compounds that are likely to be drugs. Yet in the history of HTS only one drug has been “discovered.” “But,” you might say, “a lot of drug leads have been discovered.” True, but that’s not how the technology was sold—i.e., hyped—and then you have to compare it to alternate approaches, such as focused screening, fast followers, even computational methods like similarity searches. In addition, HTS is notoriously noisy—we’ve all seen, I suspect, the scattershot graphs of successive HTS screens on the same compound collection. Not for nothing was the phrase “HTS rescue” invented. False positives cost money. Repeated screening costs money. I’d conjecture that the real return on investment, in the billions of dollars at some companies, is hard to find. In fact, some (successful) companies, such as Lilly, have abandoned HTS altogether. So is the idea of faster, bigger screening a bad one? Of course not. We all want faster, cheaper and better. However, any engineer will tell you to pick two. HTS chose “faster and cheaper,” when it should have chosen “faster and better.” Once again, quality of information was sacrificed for quantity. How much better if the basic science of measurement had been supported, if speed and quality had evolved hand-in-hand? As happened, for example, in the chip industry. New fabrication plans cost billions (i.e., not cheaper) but they are ever faster and more accurate.
Kinases. I was first introduced to the idea that pharma was going to design kinase inhibitors in 1994, while visiting Glaxo. I distinctly recall thinking two things. The first was that it seemed dubious to design drugs for proteins that all had ATP in common, simply because of specificity; the second was that it was unclear what the biological case was for wanting to mess with such a central component of cellular machinery. Now, there have been some spectacular successes where the biology has been clear, such as Gleevec, but has the investment of many, many billions of dollars come close to break-even twenty years later? Many I’ve talked to do not think so. I am very familiar with one company that abandoned its traditional (and highly lucrative) areas to go “big” with kinases. In the ten years that followed they had one minor success story. Still, I’m conflicted about claiming that kinases are a total fad. The biology that has emerged, the wonderful dendritic maps of kinase families, the spectacular successes of Gleevec, possibly PLX4032 from Plexxicon for Raf kinase—these are all good, good things. But has the resources devoted to kinases as pharmaceutical targets by the industry as a whole paid off financially? Almost certainly not. Have many opportunities been lost in traditional areas? Absolutely. So what could have been done differently? Well, this is one area where support of academic research would have helped: why not pay academics to play? It would have helped to have known much more of the biochemistry and the nature of the underlying biology, but the rush to not get left behind prevents that. It’s all or nothing, go big or go home.
Remember the whole bioinformatics mania? Useful, no doubt, but it hardly revolutionized the industry. I recall seeing a presentation in the early ’90s by Bill Hasletine, founder of Human Genome Sciences. It was awesome. And yet, when the FDA actually approved their treatment for lupus last year, it came as a shock because most people had forgotten who they were. (And for the record, they are the company that so convinced SmithKline of the value of bioinformatics that SK never recovered and had to become a part of GlaxoWellcome). And the less said about the hype surrounding the Human Genome Project the better. Personally, I found it reprehensible and scientifically disingenuous to hype the effort as a fount of new medicine instead of what it was: a foundation for our future understanding of how we might one day make new medicine. But, hey, without the hype we wouldn’t have got the funding to do the project, right? Well, actually, no, since Craig Venter was doing it anyway and more efficiently. (Yet Venter’s commercial experiment—Celera Corp.— lost money every fiscal year and is currently being purchased for less than 3% of its peak value.) As with kinases, bioinformatics has been interesting, but the return on investment has been negligible. Most bioinformatics groups in pharma disappeared or were subsumed into other groups four or five years ago. Once again, a lot of information but very little quality. The quality was wrapped up in the biological relevance, something still lacking from most of the genome. Even the much-touted efforts to associate genes with diseases have been mostly a dry well: correlations found by one group are commonly disputed by later research, and even those that persist usually offer only glimpses of the underlying etiology.
Fragment-based drug design (FBDD). Snake oil? Those are fighting words, as many love FBDD. Some companies, such as Astex, were founded on the idea. That would be Astex Therapeutics, recently merged with SuperGen for less money than the total venture capital pumped into them since 1999. Yes, starting with small molecules and building up is a legitimate method (isn’t that just the old idea of the “anchor and grow” method of Howe and Moon?2), but is it an effective method—i.e., stacked up against traditional methods? That’s quite unproven. Certain insights would probably only have been gained by screening fragments—but is it a new paradigm for drug discovery or, as one colleague admitted, what you do when nothing else works? That’s a lot to go into here. My opinion is that mid-sized molecules, around fifteen to twenty heavy atoms, make sense, but really small molecules produce almost no useful information and have too high a false positive rate. What is for sure is that the useful applications of FBDD will not be what were initially hyped. And I think a lot of basic experiments (play) have not, even today, been done. For example, it is unclear to me how often molecules bind the same way as the fragments from which they were elaborated, or what the enrichment rate is of molecules bearing active fragments, compared to base-line enrichment, or when (if) FBDD produces active compounds any faster than standard structure-based drug design. No one, other than Abbott, has succeeded in joining up multiple active fragments in an active site. That would be the same Abbott that announced they were giving up FBDD. There may well be utility in FBDD but the suggestion that it is a front-line approach to all drug discovery is hype-based science.
Systems biology. I’ll keep it short: systems biology is another unfortunate attempt to rebrand biochemistry (lest anyone forget, the first being to call it “chemical biology”). Biochemistry is a real science. It is built upon the foundations of Krebs, Buchner, Sumner, Kornberg—all great scientists—and with many great contributions over the years. Such work is dedicated to understanding how the molecules of life work and work together. What exactly needs rebranding? Most of systems biology is hype and that which isn’t is just plain old biochemistry. Look it up in Stryer.3 That it should be necessary to rebrand, to re-hype, such a fundamental and wonderful science says much about current scientific leadership and granting agencies.
I could add many other examples: biologics, stapled peptides, outsourcing, workflow tools, cloud computing, RNA-based therapeutics, structural biology (does it actually help drug discovery more than the traditional development of SAR?), even computational chemistry. Perhaps especially computational chemistry! So can we, as a community, avoid hype-heartache in the future? In an attempt to be useful, not just negative, here are my five general principles:
1) Beware of technologies being sold to management, not to bench-level scientists.
It’s not (just) that management won’t understand the issues; they often have misaligned incentives. The kudos for bringing in a new and useful technology, for showing how you have “innovated” (if only by buying it) is often irresistible. And if it all goes wrong, as it often does, management has either moved on, propelled by the anticipated glory yet to arrive, or can blame the proponents for fooling them. A common excuse is that everyone was doing it or that someone with a Nobel Prize told him or her it was a good idea.
2) Ask if the fundamental scientific issues have been addressed.
And I don’t mean by those selling the hype; I mean by scientists not vested in the approach (or in a competing approach). Another common ploy of hype-sellers is paper churn. If you are attuned to this one you’ll eventually see a proponent of a method show a graph illustrating how the rate of publication is ramping up on this topic. As if this means anything other than that there are lots of people willing to believe hype. Publication quantity is no guarantee of quality. Yes, a good idea will generate lots of papers—but so do bad ones. The incentives of journals are to publish.
3) Work out if more is actually better.
A recurring theme in the examples above is that more must be better. More compounds, more screening, bigger chemical pathways, more gene sequences. No one really asks if the inevitable loss of quality is worth the increase in quantity. I find this curious because there are standard statistical techniques from information theory that answer this exact question. Yet I’ve never heard of them being used—perhaps a future blog, talk or product from OpenEye? A good rule of thumb ought to be that more is seldom better unless it is also at least roughly as accurate.
4) When in doubt, buy the results, not the technology.
From a senior industry figure, and a rule to live by. If someone claims they have a great new way of producing active compounds, see if you want to buy the compounds. If someone wants to sell you a measurement technique, buy the output. Now, if you repeatedly like what you get, sure, buy the technology. But what’s wrong with first buying the results, not the hype? It’s a rhetorical question, but the answer appears to be the fear of being left behind (big pharma’s desperate need to act like lemmings). In most of the examples here, the wise company would have lost nothing by waiting until the hype wore off, and in fact would have gained much. Buying the results of the hype rather than the hype is a hedging strategy, in the original sense of the word.
5) Thou shalt always play.
The only sure way to get to the other side of Hype Hill, to get to the real utility, is to play. You have to be prepared to let talented people goof around, sometimes with substantial budgets, and develop expertise. A couple of examples from outside our industry: Ray Dolby, who founded the eponymous Dolby Labs in 1976. He engendered a culture of experimentation that has had few parallels. His engineers could buy any equipment they liked, as long as it was less than a couple of hundred thousand dollars! Today Ray is worth $2.7 billion and his company has an enduring reputation for innovation as well as profits. Or consider when the British tried to interest the American armed forces in the Harrier JumpJet. After a few flights the American test pilots began in-flight manipulations of the adjustable thrusters that were only supposed to be horizontal in flight and vertical in takeoff, risking expensive structural failure but learning that the plane’s real value was maneuverability. It helps having “management” willing to buy you new toys if you break the old ones!
Play is not cheap: people playing means people not contributing to the apparent bottom line. Tati’s great Play Time, in the end, did not make money—it’s a risky business, movies and drugs. But if you want to innovate, to avoid the pitfalls of hype, you have to commit to play time—invest in constructing a climate of curiosity and experimentation. Let real science take root. And stick with it.
1. “Drug research needs serendipity”, David Shaywitz, Nassim Taleb, http://www.fooledbyrandomness.com/FT-Drugs.pdf
2. “Computer Design of Bioactive Molecules: A Method for Receptor-based de Novo Ligand Design”, J. B. Moon, W. J. Howe, PROTEINS: Structure, Function and Genetics, 11:314-328 (1981)
3. Biochemistry. Lubert Stryer. 4th Edition (the one with the GRASP pictures!)
Don't do it man. Pharma R&D, in its current incarnation, needs to die. And be replaced by a completely new one. One that is composed of participants truly interested in solving problems, instead of the current-day jokers. Seems to me, that any attempt to cure pharma, will still result in retaining some of the old (cancer is rarely ever fully eliminated). So better that it die completely, and be replaced by new nimble startups. - ayatollahOfTheOutcomes
you promised the second part of this blog - it's eagerly awaited! When will it be posted? Thanks, Matt
How Well Can Fragments Explore Accessed Chemical Space? A Case Study from Heat Shock Protein 90 http://pubs.acs.org/doi/abs/10... Some interesting insights from Rod Hubbard, also chemists starting from very similar fragments diverge into different structures. - Chris
"I tried to get the 'father' of the field of vacuum-water transfer energies, Dick Wolfenden, to come out of retirement and make some more measurements but his response was that it was very difficult to countenance getting a student involved in this work, given the lack of publication appeal"
Could OpenEye sponsor someone who is interested in this kind of stuff and send him/her over to the Wolfenden lab for a year long project? (Incidentally I work next to Dick Wolfenden and as you know, he is a real gentleman and a really nice guy) - Ash
Dick proposed a summer student (that we would fund) but was unconvinced as to the value for that student's resume (he doubted he could get such work published). His most tempting offer was to train me to make the measurements!- something I would have loved but other responsibilities get in the way. I know he's a great guy and if he really could get a student for a year I could probably raise the money. It's something I've been meaning to go back to. - Ant
I remember a talk by John Dixon (ex AZ) on a similar theme with similar targets and he also included molecular biology.
Was HTS hyped as a way to discover drugs, I've only ever thought of it as a way to find potential leads, did I miss that hype wave? We often spent months whittling back the hits from HTS to a much smaller structure "minimum pharmacophore" that we then thought of as the lead, so it is probably no surprise that I actually find fragment-based approaches quite attractive. - Chris
I believe it was. There was definitely the concept in the air that if you just made enough and screened enough compounds drugs would drop out of the air... - Ant
Sorry I'm coming to this late (I only just saw it via the OpenEye linkedin group).
I'm sure you're just trying to be intentionally provocative Ant so that's all good - but, as you yourself comment, it's not that any of these things are useless. What upsets me more than over-hype is this sort of anti-hype though. And in this way you rather contradict yourself. If we were this negative about everything we'd never try anything, and in fact we would never be playing at all. We live in an over-hyped world, and over-hyping something for upper-management is often the only way to get them to let us scientists do it. In the end we generally get to do it though - so we get to play, and by bringing lots of methods/ideas together we succeed - and often we fail too.
Believing that any one technique/approach to drug discovery is right in every occasion would be totally delusional! No-one does. Drug design fails for many reasons.
Sometimes we use ROCS. Once it almost gave us a clinical compound straight out the box! Generally it doesn't. But usually it helps.
HTS is very useful at finding hits, particularly for novel targets, and they eventually turn into drugs (in about 1% of cases!). Pretty much every drug that has made it to market in the last 10 years started out this way.
FBDD is useful sometimes, and sometimes behind the curve - it depends on the target. Some targets, like BACE for instance, you pretty much have to start with fragments. Fragment-"Aided" drug design is a more useful concept. Astex and Abbott have both progressed this area immensely and certainly improved conceptualization of rational drug design - even if, like you say, it's not that different to "anchor and grow" that came before.
It is possible to make exquisitely selective kinase inhibitors (if that's what you want to do), or compounds which work in cells/animals via inhibition of multiple kinases simultaneously. Kinase inhibition via allosteric and PPI sites is also possible.
In answer to one of several un-truths: "No one, other than Abbott, has succeeded in joining up multiple active fragments in an active site", I offer this shameless act of self-promotion - containing 12 examples of fragment linking from numerous companies:
I think you have assume there's a few unpublished examples too (I can tell you for certain that there are at at least 2 companies).
Contained in this paper is the use of FMO-QM calculations to rank fragment hits by the ratio of electrostatic vs. dispersive interactions. I can overhype this for you if you like!
Totally agree with your 5 general principles. 1) though is unavoidable - there are 3 types of buyers in every transaction and one of them is always management. Sometimes 4) might be the difference between $500K and $5M so isn't always the best way to go about things! 5) is clearly vital. Every company that claims to be a scientific company has to allow "play" otherwise not a lot happens. I think some do. - Rich.
I appreciate I can come across as overly negative- I think there are some good ideas out there (next blog!)- but I am really not aware of an excess of 'anti-hype' in our field. Anti-hype is, I think, just critical reasoning, which is what I think science is about. Rather there is far too much uncritical acceptance of ideas that *seem* like they ought to work.
You state it is "delusional" that one technique is going to be right in every case, in which case I'd suggest that yes, pharma has been pretty delusional. I've been here long enough to have seen these very claims and to see companies buy into the delusion. My point is that a more scientific approach would have avoided the excesses and lead to faster progress. Rather, people get trapped by their own hype. We should be more skeptical, given the history of recent years:
"In science, the burden of proof falls upon the claimant; and the more extraordinary a claim, the heavier is the burden of proof demanded. The true skeptic takes an agnostic position, one that says the claim is not proved rather than disproved.", Marcello Truzzi, Zetetic Scholar, #12-13, 1987
I think nearly all things hyped that I have seen in the last 20 years have been claims "not proved".
As for your claim that every drug in the last 10 years coming from HTS- that's a claim I'd like to see you back up. Since many drugs are fast followers those can't be claimed to be HTS successes (unless you are claiming transitive success!). Furthermore, that discounts biologics. Furthermore, my point was (explicitly) that HTS was not sold as a "lets find leads" technology. It turned into that. Finally, if a major company like Lilly can stop HTS, and Merck move towards focussed screening.. well, defend *your* claim!
On joining up fragments, I admit the comment that "only Abbott have made this work" was based on several comments by several major figures in the field, not on evidence, and so thanks for your article. From which I quote:
"However, a review of the literature shows that such events are relatively rare.."
If I have sinned in the extreme of my abnegation, forgive me. Success via the path hyped by Abbott is merely, "relatively rare". I think my general contention stands.
Finally, concerning my five points, point 1 is not unavoidable at all, i.e. pitching stuff to management not to the bench-level. The key words here are "not to" - Of course management is involved but when it is exclusively management, that is when the trouble starts. A well-functioning management involves AND listens to the bench-level and I've seen this greatly diminish, which is why hype often works. On point 4, of course you have to do the economic assessment- but do it! Pharma has such resources available the damage is often done by gung-ho investing in new things, rather then cautious shopping. Glad we agree on point 5! Which is the main one of the essay anyway.
Thanks for the thoughtful thoughts. - Ant
"For example, it is unclear to me how often molecules bind the same way as the fragments from which they were elaborated"
Thanks. I appreciate *some* work has been done, I would simply claim that it's hardly been exhaustive, has it? The first paper you cite, Barelier et al, is on one system, the famous Abbott Bcl system, which did prove amenable to FBDD, and actually seems to support my conclusions. I quote:
"Finally, the study reported here shows that the fragments not included in leads will interact with their preferred binding site, which can be different from the site they occupy when they are included in the larger molecule and illustrates the nonadditivity of fragments in protein-ligand binding."
The second paper, the famous Shoichet & Babaoglu paper, doesn't come to firm conclusions one way or another.
The final paper describes deconstructing a cyclic five amino acid peptide to different four amino acid peptides that bind similarly- hardly 'fragments', although they do also describe a dimethylguanylurea that binds similarly- a nice study.
But my point here is that these are anecdotal and, in two of the three cases, actually unconvincing for the general hypothesis that fragments bind in similar ways when incorporated into larger molecules. Only last week I saw a talk by Steve Burley, from Lilly, who gave an example of a simple pyrazone that when you add a methyl completely switches where it binds!
A real field, a real scientific field, would have established by now what the actual probabilities associated with this phenomena actually are. Instead, I would claim it's still unknown from case to case. -Ant
I agree, little work has been done on this question, and many others in the pharma-related sciences. Let's extend the quote backwards to see what you said right before this...
"And I think a lot of basic experiments (play) have not, even today, been done. For example, it is unclear to me how often molecules bind the same way as the fragments from which they were elaborated,"
Really, you imply, purposefully or not, that no one is doing these experiments. These experiments are hard (postdoc & grad student years are not cheap) even for a single system, doing it for all systems will require a lot more work. When the first people who do work in a field (those cited above) aren't given any credit for the hard work they did do, why would anyone want to pursue more? When it is written off an unconclusive, and what preliminary 'play' work isn't unconclusive, that's not very encouraging. At the end of the day, people must get something out of these very difficult projects (quantifying unknowns, fighting dogmatic ideas, etc), or you simply won't be able to attract grad student & postdocs to them. - Anonymous
I couldn't agree more. I tried to get the 'father' of the field of vacuum-water transfer energies, Dick Wolfenden, to come out of retirement and make some more measurements but his response was that it was very difficult to countenance getting a student involved in this work, given the lack of publication appeal. This, despite the importance of such measurements to the testing and evaluation of, well molecular modeling! When I say "I think a lot of the basic experiments..have not.. been done", I do not mean no one at all has tried, I mean the facts of the matter have not been well established. Am I surprised that sometimes fragments bind similarly to elaborated molecules? Of course not. Do I know the tolerances for this to occur? No, and no one else does either- and that has importance, I would at least claim, for the utility of FBDD. Hype rules over substance- it's much easier to get funding, either commercially or from governments for the next great thing than to actually develop a sound, scientific basis for what we do. That's why this is not a very scientific field and why progress is slow. What frustrates me is that it would not take a lot of money to change this- but as I've blogged before, the NIH wants 'translational' science, whatever that is, and pharma simply has lost the perspective requited for long-term endeavor. - Ant
I agree. The funding agencies are not serving scientific progress, just progress at any cost. I'd love to see NIST or the NSF step up and fund scientific work like vacuum-water transfer energies or pKa determination, both of which would eventually help drug discovery immensely.
I also agree that the facts of the matter w.r.t. FBDD have not been established at all, 3 preliminary studies at least got very good papers out as a result though, so there is some publication appeal, and those authors received funding to do the work, so all hope is not lost. But, of course, these studies all came well after the hyped sale of FBDD, and weren't done by the people selling it.
Ruth Kirschstein was in some ways the only champion of this issue, fighting to raise the funding levels at the NIHGMS, which does at least use some of its funding on these basic science questions. I'm not sure which funding body should be funding this kind of research (it is clear not many are willing), but it will likely need a champion inside the agency to make it happen. - Anonymous
I fully agree on the need for "play". When I tell my management that our ability to innovate depends on having enough room to play and explore, they object that surely the routine bench work must be innovative, because (!) we are a research group... The idea of the scientific cookie factory (predictably) delivering great drugs as the (predictable) result of (predictable) routine work continues to appeal to managers, but it doesn't work. The recent hype for "lean management" has done catastrophic damage by eroding the "play" time.
As for technologies, I think all the things you listed have their value as additions to the scientific toolkit, and we should not forego them when they can be useful. The problem is a pharma management that is always looking for the next panacea, instead of accepting that it is going to take hard work, luck, and a wide range of tools and skills. Worse, they don't even get the panaceas right, because they think they have solved the problem when they have bought the box, and ignore the "scientific assembly required" label. Usualy they are bored by their new toy well before they have made it productive. - Mutatis Mutandis
Eventually most hyped concepts deliver some value (not always- fusion power anyone?) I'm arguing for a swifter, more efficient march to that point, if it exists. Current management folly in pharma makes the excesses of the hype-cycle worse not better and I think there are some concrete things that the field could do to improve things. Not that I'm hyping the idea ;-) - Ant
The real issue is not the technology but the panacea-centric view of Pharma & Biotech management(and most of the scientists whose advice they seek). Technology is a good servant but a poor master.
Rant on! -Pete
You forgot the hypest hype of all, the current saviour, the so called personalised medicine, not new, more of a hopeful mutton dressed as lamb. A bag where many companies throw many different things, some serious, some frivolous, some in an effort to cajole us into controlling what we should eat, drink, smell, watch, who should we meet, have children with..., which drugs we should take...., and all of these sometimes just mentioning very poor probabilities. No doubt drug response, diagnostic or prognostic biomarkers are great tools if show decent specificity. Love the concept. I am definitely for it. And yet if not specific, why to bother, I always wonder why the 40, 50, 60...% of non responders should pay for it to no avail, unless a life threatening case?
Hard to avoid the pitfalls of hype when blessed, revered, adored by most of venture capitalists. They are hype experts. The more hype, the more IPOs or trade sales and thus goal achieved. Good timing, good exit. Removed from the final, real value of products, drugs sometimes. Then it can go to rack and ruin. - Smallweed
That is another one, it's true. And you raise a good point about VCs. The role of VCs is to fund something and then turn around and sell for more to the greater fool. As such, where would they be without hype? But that's their job, they aren't supposed to be contributing to economic or scientific progress, merely their bottom line. You could say the same thing about pharma execs except, unfortunately for them, their bottom like *does* depend on economic and scientific progress. - Ant
but if not them, who will foot the bill for the necessary and longer lasting economic or scientific progress associated with drug discovery and development, that is, translated innovation (not trendy dogmatism)? Governments? Alas enough on their plates already. SBIRs? batty riches? Lottery winners? footballers? Or would all companies have to do fee for service to fund their in house development? Am not fond of this hybrid model, at the end of the day neither is done competitively ,but if it were really profitable, it would be the only way to PLAY independently, innovate.
A bottleneck I am afraid, and bloody well gripped... - Smallweed
I hear this all the time- "we all hate VCs but where would we be without them". Most of the huge pharma we know and, er, love were NOT founded by VCs. Rather they were started by wealth interested in long-term return. It's like vineyards- you don't see VCs buying into wine production, do you? Why not? Wine making can be very profitable. Because, of course, it takes a long time to get your money back. Instead, vineyards get started by people who care, can afford it and are prepared to wait. Tried any of the Francis Ford Coppola wines recently? They're not bad, and getting better..
To quote Roger Sayle, "VCs are the sinks in the zero sum game" - Ant
VCs, not my kindred spirit. Hare-brained, overweening and sanctimonious popinjays, albeit rare exceptions. But those pharma you mention were founded YONKS ago, past, not right here right now. Nonetheless, weekly lotto and/or golf to mingle with the patient vineyardist´s extant and filthy (unreachable that is) lucre don´t hurt.
Haste makes waste. Most of the times.
True! But they must have been serious undertakings even back then- by which I mean, why isn't long-term wealth attracted to drug discovery these days? I half wonder if David Shaw isn't an exception that proves the rule - i.e. perhaps he is really a long-term investor. He's put his money behind dynamics helping drug discovery- and that'd CERTAINLY a long term investment ;-) Ant
Luckily, many more exceptions, I trust.
Perhaps, generally speaking, old long-term money has a taste for less crowded beaches (back then, when those pharma were founded, needy and pre RCT era). On the contrary, today´s nouveau VC riches, many at least, relish the idea of obtaining rapid returns (no wonder, their origins) from the reverse gentrification in the (over)populated and yet thought improvable drug discovery/development/marketing world nowadays. Perhaps.
Certainly, a long term investment PROBABILITY that is. By the way, haven´t you ever felt tempted to go all the way? Or half the way? And thus getting closer to personally reaping the ultimate fruit, certainly confirming the value of the initial undertakings with your own two hands/eyes? And thus doggedly applying all those shrewdly blogged reflections, sentiments, advices, insights, arguments, experiences, hunches, in one word, knowledge about the industry and its management? - Smallweed
You know, when OpenEye was freshly minted people would ask me if I wanted to design drugs (as if all it took was a few ROCS runs!). My reply was that as long as people were using our tools, I saw no need. In fact, my response to one VC who asked, "Why, don't you want us to invest so you can put all these great ideas to work designing drugs?" was that I had some of the most heavily capitalized companies in the world doing just that - why did they think their paltry millions where going make any difference?
These days, when I look at the lunacy that prevails in major pharma, the lack of basic science in the field, and my belief that there really are some good ideas out there (which I will cover in my next blog), I do revisit the idea- with the right level of long term finance you bet I believe I could do better. But I also see some of the companies that are less stupid (finally) doing well, so that pulls me back from the brink of my megalomania. Perhaps Darwin is at work and the industry will become (on average) more rational by natural selection. A guy can dream, can't he? - Ant
"Why, don't you want us to invest so you can put all these great ideas to work designing drugs?" was that I had some of the most heavily capitalized companies in the world doing just that - why did they think their paltry millions where going make any difference?
"4) When in doubt, buy the results, not the technology.
From a senior industry figure, and a rule to live by. If someone claims they have a great new way of producing active compounds, see if you want to buy the compounds. If someone wants to sell you a measurement technique, buy the output. Now, if you repeatedly like what you get, sure, buy the technology. But what’s wrong with first buying the results, not the hype?"
I feel there's a bit of a disparity here. Shouldn't people wait to buy your technology until after 1., you've repeatedly sold them leads generated by ROCS/EON/FRED runs on their targets, and 2., they've checked to see how many actually bind in the pocket? - Hibob
I once read "all you need is ignorance and confidence and the success is sure", "dont part with your illusions when they are gone you may still exist but you have ceased to live" and "it´s never the things we do that we regret the most. it´s the things we did not do, haven´t done. Or can´t".
A shake with the three sifted through daily prosaic life and off we go...
I see. Sympathise. It would be fun to wallow in the drug dev mud though. Intelectually at least. - Smallweed
Very interesting article. Two quick questions. You write...
"Yet in the history of HTS only one drug has been “discovered.”"
Which drug is this? And is it possible to take a stab at how many of the leads that were identified eventually led to approved drugs? - Anonymous
That's a good question. I'd assumed the actual answer was "none", after talking to a lot of people in the field. But then I was reliably informed that there is a recent review article where there's a Japanese example of an actual 'discovery'. I didn't have time to track it down, though. The second question is harder and I know of no such survey- even then it's hard to know what one would make of such a number- I'm not saying HTS can't find you leads, rather is it an effective way to find leads relative to other methods. - Ant