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Derek Lowe The 2002 Model

Dbl%20new%20portrait%20B%26W.png After 10 years of blogging. . .

Derek Lowe, an Arkansan by birth, got his BA from Hendrix College and his PhD in organic chemistry from Duke before spending time in Germany on a Humboldt Fellowship on his post-doc. He's worked for several major pharmaceutical companies since 1989 on drug discovery projects against schizophrenia, Alzheimer's, diabetes, osteoporosis and other diseases. To contact Derek email him directly: Twitter: Dereklowe

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August 5, 2011

Bernard Munos Rides Again

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Posted by Derek

I've been meaning to link to Matthew Herper's piece on Bernard Munos and his ideas on what's wrong with the drug business. Readers will recall several long discussions here about Munos and his published thoughts (Parts one, two, three and four). A take-home message:

So how can companies avoid tossing away billions on medicines that won’t work? By picking better targets. Munos says the companies that have done best made very big bets in untrammeled areas of pharmacology. . .Munos also showed that mergers—endemic in the industry—don’t fix productivity and may actually hurt it. . . What correlated most with the number of new drugs approved was the total number of companies in the industry. More companies, more successful drugs.

I should note that the last time I saw Munos, he was emphasizing that these big bets need to be in areas where you can get a solid answer in the clinic in the shortest amount of time possible - otherwise, you're really setting yourself up with too much risk. Alzheimer's, for example, is a disease that he was advising that drug developers basically stay away from: tricky unanswered medical questions, tough drug development problems, followed up by big huge long expensive clinical trials. If you're going to jump into a wild, untamed medical area (as he says you should), then pick one where you don't have to spend years in the clinic. (And yes, this would seem to mean a focus on an awful lot of orphan diseases, the way I look at it).

But, as the article goes on to say, the next thought after all this is: why do your researchers need to be in the same building? Or the same site? Or in the same company? Why not spin out the various areas and programs as much as possible, so that as many new ideas get tried out as can be tried? One way to interpret that is "Outsource everything!" which is where a lot of people jump off the bus. But he's not thinking in terms of "Keep lots of central control and make other people do all your grunt work". His take is more radical:

(Munos) points to the Pentagon’s Defense Advanced Research Projects Agency, the innovation engine of the military, which developed GPS, night vision and biosensors with a staff of only 140 people—and vast imagination. What if drug companies acted that way? What areas of medicine might be revolutionized?

DARPA is a very interesting case, which a lot of people have sought to emulate. From what I know of them, their success has indeed been through funding - lightly funding - an awful lot of ideas, and basically giving them just enough money to try to prove their worth before doling out any more. They have not been afraid of going after a lot of things that might be considered "out there", which is to their credit. But neither have they been charged with making money, much less reporting earnings quarterly. I don't really know what the intersection of DARPA and a publicly traded company might look like (the old Bell Labs?), or if that's possible today. If it isn't, so much the worse for us, most likely.

Comments (114) + TrackBacks (0) | Category: Alzheimer's Disease | Business and Markets | Clinical Trials | Drug Development | Drug Industry History | Who Discovers and Why


1. Rick on August 5, 2011 10:27 AM writes...

To put a finer point on it Derek, Munos 7th step in his 7-step process to improve R&D productivity is: "Cut R&D". Specifically, he recommends eliminating in-house corporate research and letting that be done by "outside" organizations.

I can't believe that, after the volumes of organizational research - which I would've thought Munos would've read, but maybe not, which is another scary thought - have addressed the questions "why do your researchers need to be in the same building? Or the same site? Or in the same company?" and found that "it often works best that way", Munos can offer wholesale trashing R&D without attempting to refute, or even acknowledge, this vast body of knowledge. But then again, he's a marketing guy, and in that world, the important thing is NOT what people know, but what you can convince them of, so this is about what I'd expect. Little wonder that R&D productivity has crashed under the "leadership" of Munos and his bretheren.

To better understand the avoidable stupidity of the situation, try the following thought experiment: give research scientists free rein to determine how marketing does its job and and predict the response of the business community. Fortunately, scientists don't try to tell marketers how to do their job nearly as much as marketers tell scientists how to do their, so I guess you could say the glass is only half-empty.

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2. Matthew Herper on August 5, 2011 10:52 AM writes...

Two quick points: Bernard certainly still believes in focusing in areas where you can get proof of potential breakthrough efficacy early on. It's to that idea that If that didn't come through, it's my fault.

Rick, Munos certainly isn't saying to cut all R&D, but he is saying that it's now possible to allow a lot of the research to be done by small groups that are more loosely networked together. Part of the idea is to make it culturally easier for executives to kill more programs early.

Cutting R&D does not need to mean cutting R, either. I think a lot of this, in his vision, would be saved by not funding so many clinical trials, and by taking bigger, riskier bets on things like stem cell research, regenerative medicine, synthetic biology, etc.

Thanks for the discussion, Derek. It's much appreciated.

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3. lynn on August 5, 2011 10:55 AM writes...

I was speaking with Munos recently - he was promoting his outsourcing/innovation stuff - and I said, all well and good letting academics and others have a go at drug discovery - but they have no experience, no knowledge of drug discovery, of what the problems are, of what can go wrong. They will be spending too much time reinventing wheels that have already proved unworkable [like that novel elliptical wheel design]. Somehow, before one sends the innovators off to play, they should get some basic education. He didn't disagree - but I don't think he has internalized the role that experience and expertise play as a background to innovation. And, as Rick says [#1], that is the benefit of larger organizations - the possibility of spreading lore and expertise.

As to DARPA - some good stuff yes, but a lot of garbage funded too. Not that this is bad. The Bell Labs model was one that several Big Pharmas tried to emulate [at least a little] in the 80s, anyway - let a lot of good scientists do what they wanted and something would emerge. Things did emerge, there was a pipeline; but the advent of yearly evaluations based on short term "objectives" and the drive for efficiency stemmed that. I've always thought that the early stages of discovery, being quite cheap within a Big Pharma context, should have a reasonable amount of free time for scientists. Small groups could work on several projects at once - and commit to ones that were progressible. How to set up that sort of system in the present day economic climate?

I have been sitting on NIH study drug discovery study sections lately, and almost all of the academic proposals suffer from a lack of understanding of the obstacles to drug discovery. Grrr.

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4. SciParker on August 5, 2011 11:04 AM writes...

Derek, this trend dovetails nicely with the open innovation paradigm which companies like GSK are embracing whole-heartedly. Complimenting senior execs in a forum such as this is not always popular but this is one space where I feel strongly that the likes of Moncef Slaoui and Partick Vallance @GSK have been well ahead of the curve. The science park in Stevenage, Uk, promises to be a real engine of innovation that, far from threatening jobs across the piece, has the potential to secure future growth and deliver a 21st century pipeline. There is great hope that an entirely new "ecosystem" can be created in the park where the strengths of big and small companies can cross-fertilize to mutual benefit. Jackie Hunter, fGSK, has been an articulate proponent of this model and has written a widely-quoted piece on this, see She and a number of other ex-GSK-ers, Mike Barnes for example, are very active in this endeavour so I think we should keep a close eye on this spece.

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5. Anonymous on August 5, 2011 11:27 AM writes...

#2 Matt - While Mr. Munros may still beleive in "focusing in areas where you can get proof of potential breakthrough efficacy early on", that can be taken in differing ways. True breakthroughs on diseases that society cares about do not come "early". At least in terms of the time he seems to be monitizing those dreams.

If he is stating that using those distributed methods will clearly shorten that time from "conceptual breakthrough" to actual product, then OK. Still will take some years to prove that out.

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6. Anonymous on August 5, 2011 11:36 AM writes...

#4 - SciParker seems to be a recurrent PR tout for GSK - in varying names. Munos' seemingly novel POV aside, this is in fact not a new or singular stretegy. Most to all of the top Pharma's have been investing in decentralizing R&D, and improving the tools, org., and process to manage that vision. However, only GSK has seen to "green light" such obviously corp. PR statements.

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7. Anonymous on August 5, 2011 11:42 AM writes...


1) Your link doesn't work.

2) Usually the GSK PR machine jumps on here AFTER they layoff thousands of people. Foreshadowing?

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8. MoMo on August 5, 2011 12:25 PM writes...

Lynn- Your comment about academics and "a lack of understanding of the obstacles to drug discovery" is curious to me.

What bothers you? I would love to know as a spirit who walks in both worlds. I can only guess that its a lack of understanding how important it is to have animal data that is meaningful and relevant.

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9. Matthew Herper on August 5, 2011 12:28 PM writes...

#5 -- Some breakthroughs do show themselves early. The argument is more that the risk is great no matter what you do, so swing for the fences, I think. Bill Chin, who co-write a Science Translational Medicine piece with Munos, was much more focused on this and did not agree with cutting R&D.

Would Lipitor be invented under this model? Probably not. But Munos seems to believe that the industry's problem has been chasing too hard after Lipitors (a me-too that changed the world) and ignoring innovation.

What GSK is doing may match Munos' ideas in intent, but I'd question whether it really matches what he's saying here. I do think simply saying "well companies have been outsourcing a great deal" is not quite getting the point.

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10. David Lilienfeld on August 5, 2011 12:46 PM writes...

There's a fundamental difference between DARPA and any other model: DARPA not only funds lots of projects, only some of which will be fruitful, it also does so in lots of institutions with different cultures. That's quite a big difference, and it may explain in part the success DARPA has enjoyed over the years.

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11. lynn on August 5, 2011 12:46 PM writes...

@MoMo#9 - My experience is with anti-infectives, particularly antibacterials. Animal work is important and, with antibacterials, very predictive; but most NIH grants seem to put animal work way downstream when, in industry, we would do it much more upfront to get an idea of PK, efficacy, etc. But it is more a question of what the problems are in selecting targets [or maybe not needing to select targets at all]; of setting up HTS; how to do negative controls; recognizing the likelihood of resistance arising with most targets, knowing that just because your compound hits your enzyme, it is probably killing your bacterium by another mechanism; knowing it's really easy to kill bacteria - but much harder to do it without killing the host; realizing that we do not know how [rationally] to get a compound into a gram negative bacterium, so that finding an inhibitor of yet another gram negative enzyme is not addressing the hardest part of the problem. Lots of that kind of stuff. I'm sure there are other problems in other areas of drug discovery, too.

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12. LabRat2CodeMonkey on August 5, 2011 12:51 PM writes...

Perhaps,"SciParker",you meant this link:
One question for you, SciParker: What has been the uptake at the Stevenage Science Park so far? I heard a rumor that it's not been great but I may be mistaken. Finally, I'm not sure the wider scientific community here in the UK thinks so highly of the guys you've mentioned but, once again, I may be wrong and people would like it to succeed as opportunities are diminishing.

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13. JC on August 5, 2011 12:53 PM writes...

GPS, nightvision goggles & the like do not have to be approved by the FDA before they are deployed.

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14. Anonymous on August 5, 2011 12:53 PM writes...

#10 - What past breakthroughs have "shown themselves early"?

I agree that innovation can be boosted by applying network sciences to innovative discovery. Perhaps we need to differentiate between "outsourcing development" which has been well-in-hand for twenty years, versus this newer idea of improving how researchers interact (virtually as opposed to on the same site.) "Decentralized research" is a clumsy phrase, but as a scientist I see hope for it.

However as a scientist, I again look for signals of proving any such hypothesis. Again, proof of this will take some years. Breakthroughs in understanding disease and interventions will still take years to prove out safety and efficacy in models that regulators mandate. Unless R&D will be less fettered by such rules and ethics in other regions.....

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15. drug_hunter on August 5, 2011 1:22 PM writes...

Just so we're all clear: Lipitor did not "change the world." It was not, repeat NOT, a medical breakthrough. Mevacor was the breakthrough. Medical practice (and clinical outcomes) would not be dramatically different if lipitor or Crestor didn't exist but the other statins (e.g. Zocor) were still around. Please do not refer to lipitor as anything other than an incremental innovation.

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16. MoMo on August 5, 2011 1:24 PM writes...

Lynn-Thanks for the answer! I hear you about the promiscuous effects of "antibacterials" and the lack of their understanding by academics, but it occurs in Pharma too.

But its derivative of the "ugly baby" syndrome in Pharma where no one wants to admit that their drug-child is covered with warts and has fangs dripping blood. Meanwhile its perturbing all 4 macromolecular synthesis pathways.

But you would do well on the SBIR study sections and your observations may change, as small companies are quite cognisant of this while the academics apply to the NIH to discover and develop their membrane-shattering molecules.

But that is what good drug hunters should do, recognize toxic molecules above all, early and often. But you also realize by now that ego and thoughts of blockbuster fame and grandiosity interfere with rational thinking while drug-baby sits in the corner, sprouting horns and drooling.
And the only people worth dosing with it are Pharma MBA's as they will not be missed.

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17. Matthew Herper on August 5, 2011 1:38 PM writes...

Lipitor changed the world by generating $11 billion in annual sales.

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18. lynn on August 5, 2011 1:48 PM writes...

@momo #16 I am on SBIR panels - and I do think the grants are better than the RO1s. But there is still a lack of knowledge. Also, as to Big Pharma, in my day, we made it standard practice to give our own compounds the hardest time. We would admit to the "ugly baby". However, I agree that later on [one of the reasons I left] it became harder for folks - at the bench and higher up - to admit the problems in any program. Bad way to do science.

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19. MoMo on August 5, 2011 1:54 PM writes...

Thanks again Lynn! Then you'll be seeing applications from my new company "MoMo Pharmaceutics" where our motto is "More Molecules-Less MBA's".

And now back to Derek Lowe's continuing saga-

"How Pfizer Destroyed the World"

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20. DrSnowboard on August 5, 2011 2:09 PM writes...

@sciparker - so what exactly in Jackie Hunters track record is there that says she should be listened to / prioritised overother opinions, other than she is "fGSK"?

Will a proponent of contracted out virtualised research please give us a concrete, real life example where it has proved to be a genuine success? And by that I mean a compound from screen to patient, not picking up a cpd post P1 and punting it down the road picking up more investment? Just one, please, I like evidence based arguments.

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21. BiotechTranslated on August 5, 2011 2:38 PM writes...

#10: I agree completely.

How many breakthroughs have we seen fail in phase II or phase III trials? There is a certain amount of pre-clinical evidence that you can gather to test if your new molecule is going to be a breakthrough, but you're still at the whims of the multi-million dollar clinical trials.

I hate to judge ideas based on where they are coming from, but Munos is a sales/marketing guy, not a scientist. I think he is lacking a certain level of understanding of the drug development process and where the risk really lies.


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22. darwin on August 5, 2011 2:39 PM writes...

Hmmm...ask a surgeon how to fix a problem and he tells you it needs to be cut. Mundos has successfully discovered the last retarted idea that has been left untouched by mgmt.

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23. r.pal on August 5, 2011 2:43 PM writes...

Given the fact that 90% of human genome consists of bacteria and viruses and since these depend on the host for survival it is probable that here species may be mounting an attack on drugs and making them less effective or generating a inflammatory process that makes the disease worse with unintended side effects. The focus is shifting to metagenome and what role these play.

A fresh approach is needed to replace the one diseases one receptor and one drug approach

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24. Chrispy on August 5, 2011 2:54 PM writes...

I have to agree with drug_hunter that Lipitor was an incremental change, scientifically speaking. The $11B in sales has a lot more to do with marketing than science. More to your point, MH, the world change was probably the triumph of marketing over science in this industry, and Lipitor is really only a refection of that.

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25. BiotechTranslated on August 5, 2011 3:18 PM writes...


I have no doubt that marketing played a large role in Lipitor's sales, but atorvastatin had a lot of things going for it, that the other statins didn't (or at least Pfizer got the data for it first).

* atorvastatin is better tolerated a higher doses (many of the other statins have dose limiting side effects)
* atorvastatin reduces cholesterol levels to an overall greater degree than many other statins (related to point #1)
* atorvastatin got approved for reducing triglycerides before all the other statins
* unlike other statins (when Lipitor was first introduced) atorvastatin's starting dose got a majority of patient's LDL levels under control, reducing the need to dose, test, adjust dose, retest, etc. (Doctors like that!)

Warner-Lambert/Pfizer certainly did the marketing right, but it wasn't like they were pushing snake oil either.


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26. petros on August 5, 2011 3:19 PM writes...

When I was last at Stevenage a few months back, while the Science Park buildings had made progress there was still no indication of any takers for the facilities being built.

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27. AKS on August 5, 2011 3:37 PM writes...

You state "I don't really know what the intersection of DARPA and a publicly traded company might look like (the old Bell Labs?), or if that's possible today. If it isn't, so much the worse for us, most likely."

Yeah, running a public pharma company like DARPA probably doesn't make sense. But Francis Collins could conceivably run his new drug discovery initiative this way and maybe it would work there.

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28. drug_hunter on August 5, 2011 4:09 PM writes...

@25 (BiotechTranslated) - No one thinks Lipitor was snake oil. Agree with you 100% it was an improvement. The factors you listed are reasonable. My point is that these were incremental. That's not a bad thing to achieve, if you can't come up with anything more transformational. It is certainly better than failure.

Anyone who thinks Lipitor "changed the world" must be focusing more on the amount of money it made than how transformational for medicine it really was. Just a fundamentally different worldview. Guess that makes sense for someone writing for Forbes, but hopefully is less common among Derek's audience.

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29. Rick on August 5, 2011 4:19 PM writes...

Matt #2, I beg to differ. At heart, Munos' proposal is based on a common managerial misconception that drug discovery research is scalable and fungible in a manner similar to software code writing or house-painting. (i.e. if four painters can paint a room in a half-day, two can paint it in 1 day and one can paint it in 2 days) Every drug discovery team manager I've ever known knows you need a critical mass of researchers, working in sufficiently close proximity that they'd see each other every day in the lab, hallway or cafeteria. Below that number, you could still get lab work done and occasionally get interesting data, but as far as formulating, collecting and testing the diversity of ideas and information that comprise successful discovery research, you're wasting money because it doesn't work. Munos' proposal would cut corporate R&D below that critical mass, effectively eliminating it even though it would have headcount allocated to it.

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30. BiotechTranslated on August 5, 2011 4:30 PM writes...

@28 (drug_hunter)

Fair enough. I would argue that as a class, the statins are a breakthrough. A 60% reduction in cardiac events is huge, especially with a class of drugs so well tolerated. Merck deserves credit for bringing the first statin to market, although the initial work was done in academia by Endo.

Unfortunately, credit is assigned in drug discovery the same way it's assigned in investing: after the fact. Pfizer did luck out when they developed Lipitor, since there was no way they could have known it would have the efficacy profile I mentioned above.


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31. Shalon Wood on August 5, 2011 4:50 PM writes...

"I don't really know what the intersection of DARPA and a publicly traded company might look like"

As a computer programmer, the first thing that came to my mind (right around the word 'company', and before I got to your suggestion of Bell Labs) was Xerox PARC.

Interestingly, if you look at all the things they failed to commercialize (e.g., the GUI), it might be hard to argue that it was (in practice, rather than theory) run with an eye toward making money, which might have contributed to its success with regards to innovation by allowing for things which were not obviously profitable to get a small budget for experimentation.

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32. Rick on August 5, 2011 5:59 PM writes...

Shalon #31 Thanks for mentioning Xerox PARC! I agree that it is rich with examples of the challenges and missteps associated with managing a talented, diverse research program.

To your point about lack of focus on making money: a lot of people consider the GUI story to be an example of the opposite - too narrow focus on making money... fast. If management had had more expansive vision and timelines, Xerox could well have been the company that invented the personal computer and Apple would just be a fruit. Instead, they couldn't think beyond their preconceived ideas and short profit timelines and, voila!, Apple is a legend and Xerox PARC, plus an unknowable number of breakthrough ideas, are lost and gone forever.

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33. Clueless on August 5, 2011 6:01 PM writes...

Is there really a common model of success for a pharma or pharmas? Every successful drug has a story of it's own. Don't Pfizer things around to none.

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34. Clueless on August 5, 2011 6:09 PM writes...

Those who say Lipitor is only a me-too drug have no idea what innovation truly means. Lipitor is different and the best in class, and that is innovative.

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35. Anonymous on August 5, 2011 6:41 PM writes...

Perhaps I'm naive, but I'd say the solution to big pharma's research woes is back to the basics: (i) hire smart people and give them a broad canvas (ii) get them in the lab (not in their offices) to work on difficult problems (iii) outsource routine work where reliable expertise exists outside and (iv) hold on to institutional knowledge.
Good things happen when smart, interested, hardworking people work on challenging problems. That's where innovation comes from. Not from "tools to measure it". I won't dignify rest of Munos's thoughts by commenting on them but
I can almost bet that the ROI in Munos's outsourcing model is going to be less than in R&D orgs (otherwise life science VCs would have grown into Pfizers of the world).

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36. BiotechTranslated on August 5, 2011 9:18 PM writes...

@ #35 (Anonymous)

You know what? You should start an R&D consulting firm and I'm serious about that comment. I agree 100% with your points about how to run an R&D organization.

If any company wants to run an effective R&D organization, they only have to create the environment where it is allowed to flourish. Effective R&D groups tend to be that way, not because they have the "right" strategy, but because they don't have outside forces messing things up.


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37. Esteban on August 5, 2011 9:29 PM writes...

Munos is giving the same talking points as the leadership of his employer (Lilly). I know firsthand as I'm a recent ex-employee. Two prominent themes in recent years at the company town halls have been: (1) big mergers don't work; (2) outsource as much R&D as possible. Research employees are naturally reassured by #1 and terrified by #2.

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38. Nuclear Option on August 6, 2011 1:59 AM writes...

In cancer drug development, we fundamentally need more and more creative shots on goal. Clinical studies of mechanistically new compounds, ideally in focused and leveraged groups of patients. It is just totally irrelevant whether these molecules derive from academia or industry.

The pharma discovery model is changing, as I see it, because internal R&D is destined to fail to produce molecules profitable enough to influence the balance sheet of companies addicted to lifestyle drugs and old impactful agents like statins. It is less an internal supply problem than an internal demand problem.

My experience is transferring technologies from my academic lab into commercial entities staffed by industry professionals. The transitions have been very smooth, and fresh eyes with industry experience invariably contribute tangibly to the direction of the research. But overall we set them on the right path, and the handoff has been far more collaborative than corrective. Most importantly the molecules are in the clinic, prioritized in the way you raise your only child as opposed to running a daycare of molecules championed by chemists who have lost their voice in handoffs to clinical development teams or worse scientIsts from another company made redundant by a merger/purchase.

My sense is that creative drug discovery might best occur in a well-resourced environment comfortable with long discovery timelines required to prosecute historic targets (myc, ras, etc), and where long-term commitments are made to supporting champions. Academia is only one such place, but moving forward academia can only play a larger role in discovery chemistry due to financial pressures on pharma in a changing economic and political environment. To the topic of this post, more directly, academic handoffs do lend themselves well to prompting clinical experiments, if positioned into project-focsued companies with a uniformity of opinion and laser focus on what proof of concept entails.

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39. Morten G on August 6, 2011 2:23 AM writes...

I fail to see the difference between cutting all of R&D and cutting all of sales and marketing (S&M).

Basically I see a clash of incentives/goals: S&M marketing have quarterly goals, R&D has the goal of NMEs. When the incentives of rest of the organisation are aligned to either of these the whole organisation suffers. A CEO who's bonus is based on sales figures will cripple R&D and a CEO who's bonus is based on NME's will cripple R&D.

In other chemical industries a project set to run over two years is considered to be really out there.

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40. Roburr on August 6, 2011 5:55 AM writes...

*4. SciParker

Are you real?

Sorry but when I showed this thread to a GSK-Stevenage insider her comment was you must a corporate plant.

Morale within GSK Discovery is simply awful: fear rules, and instead of "great hope", everyone is simply bunkering down for another massive cull from the ongoing DPU reviews.

Right now, the science park feels like an irrelevance - the first buildings look more like tombstones.

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41. Bernard Munos on August 6, 2011 6:04 AM writes...

I am sorry I missed this very interesting discussion, but I appreciate the feedback. I would also like to clarify a few points.

1. The role of drug research is to translate cutting-edge knowledge into novel therapies. As companies attempt to do so, they must tackle two formidable challenges: (1) produce enough innovation; (2) make it affordable

2. History has shown that nearly all breakthroughs come from engaging in high-risk, unconventional research. The implication is that if one wants to be innovative, one has to be bold, and the bolder the better.

3. Corporate R&D labs used to be places where scientists could conduct unfettered research, and investigate bold hypotheses. That model worked well, and allowed the companies that practiced it best to grow into what became the big pharmas. Things started to change about 20 years ago when a new crop of non-scientist leaders in the industry came up the idea that scientists needed to be responsive to the needs of the market. In their view, those needs are articulated by marketers, and scientists should discover and develop compounds that meet the 'needs' identified by the marketing folks. End of the scientists' independence to pursue opportunities as they arise in science. This quickly resulted in runaway madness, in which scientists were asked to produce drugs that feed their companies' marketing franchises. Misguided techniques such as portfolio management were embraced, and 'sophisticated' planning exercises in which drug candidates are selected and advanced to replace drugs losing patents became the norm.

4. Unfortunately, this is not the way science works, and this new model produced tepid innovation, and not much of it. As Ted Torphy, VP of External Innovation and Advanced Technology at J&J aptly puts it: "therapeutic franchises focus on existing pie[s], not on creating new pies. Simply put, therapeutic franchises don’t make breakthrough drugs. Breakthrough drugs make therapeutic franchises".

5. To put it differently, the scientists' jobs is NOT to be responsive to the needs of the market, as seen by the marketers, but to discover therapeutic breakthroughs, wherever they can find them. And the marketers' job is NOT to worry about the permanence of their cherished 'franchises', but to market these breakthroughs. And if they cannot do that, they bring no value to their companies.

6. One implication of this single-minded focus on breakthroughs is that companies should restrict their funding to them, and de-fund everything else. Not to pick on AstraZeneca, but does Seroquel really need to be supported by 72 phase III and 39 phase IV trials? How much money has this focus on blockbusters diverted from the search for breakthroughs? This is a company with 80% of its sales going generic in the next 5 years, but it still has 6 recruiting phase III trials for Seroquel. And yet, there are very smart scientists at AZN, but, instead of being allowed to find the next breakthrough, they are asked to bring Nexium + aspirin to the market. This is an extreme, but not unique example of the dysfunctionality that the blockbuster mentality has brought to the industry. Almost every company has similar examples.

7. To the extent that big pharma scientists can come up with novel hypotheses and ideas that can transform therapy, they should get the funding and freedom to pursue them. Let's remind ourselves, however, that innovation is a by-product of culture, NOT a by-product of six-sigma, portfolio management, organization, or anything else. And the current big pharma culture with its emphasis on process is hardly a place that fosters innovation (with happy exceptions for companies such as Novartis). To put it differently, innovation cannot thrive upon law and order. Until big pharma accepts that and recreates an innovation culture (which they used to have), they will have to look for it outside, among the myriad small pharmas where 'mad scientists' can still roam free.

8. Even if big pharma recreate an innovation culture, they will need to cultivate an external innovation network to assemble a portfolio of potential breakthroughs that is broad enough to mitigate risk effectively. This is another discussion, but an essential aspect of drug R&D that must be integrated into any successful model. More about it in another thread.

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42. Casalini on August 6, 2011 6:07 AM writes...

Reading the GSK discussion brings to mind Colin Powell's warning before the 2003 Iraq invasion: 'China shop rules. You break it, you own it.'

Moncef Slaoui and Partick Vallance - how long before Derek is blogging about YOUR Damascene conversion?

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43. Hopeless on August 6, 2011 8:00 AM writes...

General practitioner Munos' prescription for R&D malignancy at lethal dose is good for cancer patients like Pfizer and AstraZeneca at best.