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DBL%20Hendrix%20small.png College chemistry, 1983

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: derekb.lowe@gmail.com Twitter: Dereklowe

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November 23, 2010

Of Deck Chairs, Six Sigma, And What Really Ails Us

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Posted by Derek

We talked a little while back here about "Lean Six Sigma" as applied to drug discovery organizations, and I notice that the AstraZeneca team is back with another paper on the subject. This one, also from Drug Discovery Today, at least doesn't have eleventeen co-authors. It also addresses the possibility that not everyone in the research labs might welcome the prospect of a business-theory-led revolution in the way that they work, and discusses potential pitfalls.

But I'm not going to discuss them here, at least not today. Because this reminds me of the post last week about the Novartis "Lab of the Future" project, and of plenty of other initiatives, proposals, alliances, projects, and ideas that are floating around this industry. Here's what they have in common: they're all distractions.

Look, no one can deny that this industry has some real problems. We're still making money, to be sure, but the future of our business model is very much in doubt. And those doubts come from both ends of the business - we're not sure that we're going to be able to get the prices that we've been counting on once we have something to sell, and we're not sure that we're going to have enough things to sell in the first place. (There, that summarized about two hundred op-ed pieces, some of them mine, in one sentence. Good thing that I'm not paid by the word for this blog.) These problems are quite real - we're not hallucinating here - and we're going to have to deal with them one way or another. Or they're going to deal with us, but good.

I just don't think that tweaking the way that we do things will be enough. We're not going to do it by laying out the labs differently, or putting different slogans up on the walls, or trying schemes that promise to make the chemists 7.03% more productive or reduce downtime in the screening group by 0.65 assays/month. This is usually where people trot out that line about rearranging deck chairs on the Titanic, but the difference is, we don't have to sink. The longer things go on, though, the more I worry that incremental improvements aren't going to bail us out.

This is a bit of a reversal for me. I've said for several years that the low success rates in the industry mean that we don't necessarily have to make some huge advance. After all, if we made it up to just 80% failure in the clinic, that would double the number of drugs reaching the market. That's still true - but the problem is, I don't see any signs of that happening. If success rates are improving anywhere, up and down the whole process from target selection to Phase III, it's sure not obvious from the data we have.

What worries me is that the time spent on less disruptive (but more bearable) solutions may be taking away from the time that needs to be spent on the bigger changes. I mean, honestly, raise your hands: who out there thinks that "Lean Six Sigma" is the answer to the drug industry's woes? Right. Not even all the consultants selling this stuff could get that one out with a straight face. "But it'll help!" comes the cry, "and it's better than doing nothing!". Well, in the short term, that may be true, although I'm not sure if there is a "short term" with some of these things. If it gives managers and investors the illusion that things are really being fixed, though, and if it takes mental and physical resources away from fixing them, then it's actually harmful.

What would it take to really fix things? Everyone knows - really, everyone does. Some combination of progress on the following questions would do just fine:

1. A clear-eyed look at target-based drug design, by which I mean, whether we should be doing it at all. More and more, I worry that it's been a terrible detour for the whole project of pharmaceutical research. There have been successes, of course, but man, look at the failures. And the number of tractable targets (never high) is lower than ever, as far as I can tell. If we're going to do it, though, we need. . .

2. The ability to work on harder target classes. The good ol' GPCRs and the easy-to-inhibit enzyme classes are still out there, and still have life in them, but the good ideas are getting thinner. But there are plenty of tougher mechanisms (chief among them protein-protein interactions) that have a lot of ideas running around looking for believable chemical matter. Making some across-the-board progress in those areas would be a huge help, but it would avail us not without. . .

3. Better selection of targets. Too many compounds fail in the clinic because of efficacy, which means that we didn't know enough about the biology going in. Most of our models of disease have severe limitations, and in many cases, we don't even know what some of those limitations are until we step into them. Maybe we can't know enough in many cases, so we need. . .

4. More meaningful clinical trials. And by that I mean, "for a given cost", because these multi-thousand-people multi-year things, which you need for areas like cardiovascular, Alzheimer's, osteoporosis, and so on, are killing us. We've got a terrible combination of huge potential markets in areas where we hardly know what we're doing. And that leads to gigantic, expensive failures. Could they somehow be less expensive? One way would be. . .

5. A better - and that means earlier - handle on human tox. I don't know how to do this one, either, but there are billions of dollars waiting for you if you can. Efficacy is the big killer in the late clinic these days, but that and toxicity put together account for a solid majority of the failures all the way through. (The rest are things like "Oops, maybe we should sell this program off" kinds of decisions).

There are plenty of others, but I think that improvements in those would fix things up just fine. Don't you? And maybe I'm just slow-witted, but I can't see how changing the way the desks face, or swapping out all the business cards for new titles, or realigning the therapeutic area teams - again - are going to accomplish any of it. At best, these things will make the current process run a bit better, which might buy us some more time before we have to confront the big stuff anyway. At worst, they'll accomplish nothing at all, but just give the illusion that something's being done.

To be fair, there are some initiatives around the industry that address these (and the other) huge problems. As I said, it's not like no one knows what they are. And to be fair, these really are difficult things to fix. Saying that you want to get a better early read on human tox in the clinic, the way I just did so blithely, is easy - actually doing something about it, or even finding a good place to start doing something about it, is brutally hard. But it's not going to be as brutal as what's been happening to us the last few years, or what's we're headed for if we don't get cracking.

Comments (53) + TrackBacks (0) | Category: Business and Markets | Clinical Trials | Drug Development | Drug Industry History


COMMENTS

1. assay guy on November 23, 2010 10:07 AM writes...

Agreed, although I think your #3 is the big kahuna. Way too often we go after a target when we don't have solid validation, just because we can. And we also compromise on animals models because "it's too hard" to make truly relevant ones so we use those that don't come close to replicating the human condition, just because we can. Of course, I'm on the bio side so maybe I'm biased.

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2. gyges on November 23, 2010 10:08 AM writes...

Too few people seem to realise that pharma is a Black Swan endeavour (pun not intended but left in 'cos it's quite clever).

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3. Somite on November 23, 2010 10:26 AM writes...

It is disheartening to see Six Sigma offered as a viable solution when it has proven over and over to be a complete failure and ineffectual. What needs to be done is what you say: most importantly screen more better. Six Sigma can not help because screening should be targeted to the compund and a strategy designed by scientists, not MBAs. It is expensive but if the industry supported the people with skill instead of a parasitic management structure it would do much better.

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4. darwin on November 23, 2010 10:36 AM writes...

Derek, could you please distill this down into a Cliff Notes version, call it a Consulting Solution and provide some benchmarking milestones in order to get the attention of Pharma mgmt.

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5. anchor on November 23, 2010 10:43 AM writes...

Derek, all points well formulated. As the targets are getting difficult and finite, I am worried if the well qualified and displaced medicinal/biological individuals during the recent past from the major pharmaceutical companies will have any impact in terms of productive outcome.

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6. DrSnowboard on November 23, 2010 10:44 AM writes...

As you head in your heavy 1950's limousine at speed towards a fast approaching patent cliff, it must be tempting to get your chauffeur to start ripping the doors off and throwing out the seats in the belief that you can make your vehicle light enough to fly...

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7. chemtweeter on November 23, 2010 10:48 AM writes...

What about the process of selecting only the highest active in-vitro drug for further testing? Ron Breslow described SAHA as not the most active in vitro; the more active compounds caused too many side effects in human trials. Less active in-vitro candidates never got a chance to prove themselves. Does this have any traction?

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8. Hap on November 23, 2010 10:55 AM writes...

The problem with attempting to find a disruptive solution for your problems is that you don't know when you've done it until you have. You don't know if you're wandering into a dead end or whether you're on the right path but have either missed your turn or haven't gone far enough.

The seductive part of 6S and management fads is that they give feedback - you have an idea whether you're doing what you are trying to do - though you don't know if what you're doing is actually effective at your ultimate goal (kind of like biomarkers, at this point). It's worse than dealing with the fiscal problems that face our government - we know what those are, and how to deal with them, but the solutions are painful so we won't implement them - we don't know what the solutions for pharma are. I don't know whether people even know how to start looking for solutions.

If people do know how to find solutions for the list of problems above, another problem is that the knowledge is useful to everyone, so that finding a solution doesn't really give the finder an advantage, and hence companies don't want to spend their money on finding that knowledge. Consortia of pharma companies might both provide enough data and help with the self-interest problems.

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9. Morten G on November 23, 2010 11:03 AM writes...

Better handle on target validation: Both the Structural Genomics Consortium (Toronto, Oxford, Stockholm) and Center for Protein Research (Copenhagen) have started programs for chemical probe development. So academia are going more towards the idea that they don't need to develop drugs but they need to make small molecules that modulate the function of proteins so we can find out if this is a viable drug target (and for basic research both in cells and vivo).

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10. HelicalZz on November 23, 2010 11:17 AM writes...

I've heard a few talks on lean six sigma related to R&D and clinical operations. I think it is harmful. I don't have a problem with it as a quality management tool / framework, but it needs to be applied where it best operates, and that is in a manufacturing / costumer interaction context.

Applying too many 'efficiencies' to an R&D or project oriented process seems to frequently incur unrecognized risks. It can certainly stifle any form of creativity / exploratory endeavors. I do think a project management framework i.e. effective planning and goal communication is needed to keep things moving forward, but it needs a degree (often large degree) of slack to allow for the inexactness / nature of the process.

When a drug is approved and making its way onto the market, by all means bring in the six-sigma suits to manage inventory, production, etc. But probably not before then.

Zz

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11. David on November 23, 2010 11:19 AM writes...

What's wrong with "putting different slogans up on the walls?" It's worked at least as well as most of the other ideas, and has been less harmful than many. It has the advantage of distracting the corporate folk.

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12. entropyGain on November 23, 2010 11:29 AM writes...

Swing and a miss...

Like most scientists would, you take a hard look at the problem at hand (Drug discovery & development) and address it directly. I don't think however that our ability to do drug discovery is the problem.

The immediate problem is leadership and culture.

Leadership is focused on mergers, acquisitions, layoffs... ie MBA/finance stuff, instead of saving lives. Focus the industry on medicine rather than M&A and it will make money long term.

The leadership has created a crisis of culture. How productive have the excellent scientists been in companies merging, laying off, etc for the last many years? It's hard to concentrate when feeding your family is at stake. When you rise to the top by being a good outsourcing manager or by championing the latest huge investment in 'omics, where does that get us? How many projects "failed" because management lost the will to win or the team was laid off due to a site closure? Was Josh Boger the last drug hunter to head a significantly sized company? Even genentech is now victim to Swiss MBAs.

Only the impending death of the dinosaurs and evolution of a new generation of hungry companies will fix the problem. This will take a while...

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13. barry on November 23, 2010 12:03 PM writes...

Hey Derek:
Your point #3 (targetting protein-protein interactions) is a subset of "targetted drug discovery" that you just ripped in point #2

As to your fifth point, The FDA's initial approval to go to market should be conditional on ongoing "Phase Four" data. If Phase Four doesn't meet the most stringent clinical endpoints (delta mortality?) approval should lapse.
B

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14. milkshake on November 23, 2010 12:08 PM writes...

I would first look at the schemes used to reward the top management. If the bonuses and stock option packages are tied to the quarterly reports and current stock price, the company execs will become mercenaries of the stock price. If you pay them lavishly to fake understanding of the problems (and to propose miraculous solution) they will duly fake and and peddle the management theory snake oil and urge yet another merger.

You don't expect the top execs to announce "We identified the root causes of our worsening business performance - and it is our lack of expertise, our heard mentality, alibism, our love of pompous baloney and superficial solutions and above all, our outrageous bonuses that give us incentives to act against the long term interests of this company"

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15. Anon anon anon on November 23, 2010 12:20 PM writes...

Barry (#13), take a look at the last line of point 1. Derek certainly questioned target-based drug discovery but says "*If* we're going to do it, though, we need" the following two points (emphasis mine).

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16. Anon anon anon on November 23, 2010 12:25 PM writes...

So, what's the alternatives to target-based drug discovery? Dosing animal models directly seems like it's too costly, which was one reason why target-based became more popular.

Another option is scientifically grounding traditional medicines but I wouldn't be hopeful that there are many artemisinins waiting to be discovered.

So, what're the alternatives to target-based drug discovery?

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17. Cellbio on November 23, 2010 1:55 PM writes...

Well, as a big fan of this blog, I look forward to it every day, I was quite underwhelmed by the list of suggestions. Predictive tox, inexpensive small trials that give us great clarity, the "right" targets, the ability to hit targets we currently can't. Really? This essential boils down to knowing all the relevant biology for impacting a target in humans and preclinical species, knowing all that is not known about the drug candidates pharmacology, knowing the interactions with other drugs and environmental exposures, and then having the ability to factor in variation of human genetics, and learning great things in small trials (how about a biomarker?).

A much better approach, IMO, is to be much more empirical. Suggestion #1 is the place to start, not by replacing target work, but by supplementing with good old fashion pharmacology (cellular, tissue, and to some extent animal models). Can't tell you how much crap goes forward due to "target mindset" that should not. The answer is not to abandon targets, but to restore pharmacology skills. Then once in the clinic, use your magical biomarker, but measure the most meaningful empirical outcomes, safety and efficacy. Simple approach, and costly. Trying to satisfy the dream list above would totally cripple drug discovery, and is, IMO, already doing so. Having spent much time in target choice, the validation requirements and risk aversion make it nearly impossible to advance novel ideas, and has companies preferring me-toos (which they think is more likely to be successful if the strategy is called me-better).

We don't know what we don't know, and won't advance too much relying on mouse genetics and biology. We have to get into the clinic: In Vivo Veritas.

Boy am I grumpy today.

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18. Pharmaheretic on November 23, 2010 1:59 PM writes...

Read this article about how bad companies supposedly operate. But isn't that how all large and many smaller companies operate.
---

Ten signs you work in a fear-based workplace

http://www.msnbc.msn.com/id/38206989/ns/business-bloomberg_businessweek

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19. milkshake on November 23, 2010 1:59 PM writes...

alternatives to target-based drug discovery: 1) cell cultures and 2) small-animal based phenotypic screening.

I have seen a high throughput screening done with super-fragile neuronal cell cultures - and most hits actually re-confirmed.

Whole animal primary screen used to be common in big pharma: Pfizer discovered Fluconazole by using guinea pig Candida vaginal infection model as a primary screen. Now compare the wonderfully simplified structure of Flukonazole with monsters like Itraconazole (optimized by using more simple assays)

More recent example of a success (that would not happen without mice as a primary screen) is Lyrica

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20. dave on November 23, 2010 1:59 PM writes...

This happens everywhere though doesn't it? Why work hard and do a good job if you can just do something that has absolutely no point but looks good for your next promotion. Trebles all round!

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21. Anonymous on November 23, 2010 2:17 PM writes...

all of Derek's points has be to be addressed with better science or scientists rather then more (cheap) labor.

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22. biobug on November 23, 2010 2:39 PM writes...

I have to agree with the comments blaming management over mechanism. Why aren't we right now implementing and working hard towards your suggestions to improve the basic discovery work (assuming they would be improvements) process?

Probably because current incentive structures are geared towards 1. short term financial results; encourages lay offs and mergers instead of innovation and R&D investment. 2. Numbers of candidates moved forward; encourages pushing anything with a rational story forward, regardless of relative quality or risk/reward. 3. Metric based discovery methods; has nothing to do with innovation. Creativity cannot be scripted, only encouraged. It is impossible to properly metric things with a 10 year development timeframe and a 90% failure rate.

I would suggest you create an incentive structure where everyone from the chemists in drug discovery to the suits in marketing gets a direct percentage of gross sales of an approved product they were involved in developing, along with smaller bonuses for pre-defined success in clinical development or discovery along the way. Make the incentive vest depending on time at company and on-project. Also create regular goal specific competitions (like improving assay output) between lab groups with monetary rewards for the best proposals. Then hire smart people at mediocre salaries, and watch them strive to actually invent and improve every step of the process.

This would encourage long-term thinking, creative innovation, employee retention, and would tie compensation to real world results instead of political BS and MBA jargon.

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23. thomas on November 23, 2010 2:48 PM writes...

"if we made it up to just 80% failure in the clinic, that would double the number of drugs reaching the market."

Not if you were just having them fail earlier, which is the aim of point 4. It would still be a Good Thing and would reduce costs, but it wouldn't necessarily increase the number of successful drugs.

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24. johnnyboy on November 23, 2010 2:50 PM writes...

"Here's what they have in common: they're all distractions."

hear hear. Of my work time in the biggest of big pharma, easily 20-30% was spent in meetings or other tasks aimed at "information sharing", "process optimization" and god knows what else. In 4 years in the same position, my supervisor changed 3 times, and the department went through 3 or 4 name changes (I forget). All of this in the name of increasing efficiency, all of it dictated by upper management types who, despite originally being scientists, hadn't done real science work for years. The funniest is when I hear big pharma executives saying they're implementing changes designed to make their company as efficient as small biotech - in order to really do that, they would have to immediately fire themselves, along with >50% of all managers.

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25. Derek Lowe on November 23, 2010 3:02 PM writes...

Cellbio - hey, I did say that they were things that everyone already knew. I like suggestion #1 the first, but I think that it's less likely to be implemented soon, given all the investment in the target-based stuff. If I had to pick - as in, start my own company - that's probably the way I'd go.

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26. g on November 23, 2010 3:31 PM writes...

With the pressures that we are seeing on reducing health care expenditures and lackluster improvement on existing therapies from drug companies, I don't expect for our health care system to be holding its breath for new drugs to solve its larger problems. Some where around 80% of new prescriptions are for generics (and expected to grow higher) and estimates for pharmaceutical growth in developed countries is very low compared to emerging markets. These factors are going to have a larger effect on the pharma/biotech business model than any sort of creative R and D. It seems that you are struggling to find solutions to help a business model that may be outdated.

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27. exMRK on November 23, 2010 4:03 PM writes...

In my view, it's all about people issues.

There will be no pharma renaissance until corrupt pharma leaders actually start to serve jail time and are banned from the industry; until ill-informed leaders are replaced with people with top expertise (you know - no more McDonald's types for the CEO role), and until rank and file don't have to be looking over their shoulders every minute waiting for a pink slip. Job instability fear hampers creativity and productivity.

Until these really fundamental issues are addressed, there will be no Springtime for the industry.

Lean six sigma? Only a fool could believe such principles apply to drug discovery, more an art than a science. See above re: qualifications of leaders.


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28. CMCguy on November 23, 2010 4:12 PM writes...

Maybe I am over extrapolating but I would suggest most of the points get down to "focus on doing good science" as a means to improve drug discovery. Science, particularity geared to drugs is very complex requiring hard work from many diverse but cross connected disciplines plus typically a bit of favored fortune and often unpredictable and long process. At times we still may not know everything might wish to know in the biology or how a drug actually works but if one can properly influence desired responses then will have something that achieves the goal for application of the Science. I think that where Pharma by-and-large has gone astray when shifting from core and attempted to then implement so many of the "distractions" or other fads as quick and easy fixes.

On the other side I recognize that much of Biotech has faltered because of an over focus on just research science and therefore to be truly successful as a company/bring forth a drug must have complementary development, manufacturing, quality along with business, management and marketing skills.

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29. pete on November 23, 2010 4:29 PM writes...

I don't know the solution. But it seems to me that the dumbest move for the industry would be to trend away from supporting diverse approaches to drug discovery.

History is dotted with robust drugs that were identified using very different approaches: for example, via "disease phenotype" top/down-driven screens VS. bottom/up molecular target- (or pathway-) driven screens.

The rub is that neither approach has been universally applicable.

That is, the former approach depends on having a well-chosen animal model/cell culture system of disease. Particularly a model system whose disease phenotype can faithfully report when there's a selective interruption of the underlying disease process. Very tall order, that one -- but it's worked stunningly well in some instances.

The other approach assumes that the [genetic/chemical/biomarker]-screen that got you your Molecular Target/Pathway in the first place really has it's arms wrapped around the root cause of the disease in the wider human population. Another very tall order - but one that's also paid off well in certain instances.

So - One thing I DO know: Finding drugs ain't like designing widgets.




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30. Cellbio on November 23, 2010 4:41 PM writes...

Thanks for the reply Derek, fair point, and I did say I was grumpy today. btw, hope to meet you someday.

You make a good point about the investment in the target approach. Unfortunately, it runs through to include the FDA. Was helping a smallco with an agent that worked well in animal models, displayed no tox concerns, but did not have a mechanism that was well described. There was great reluctance to allow Ph1 dosing. Thought process was in line with... 'if we can represent a plausible mechanism, then we can provide rationale for benefit, which makes uncertainty about adverse events a reasonable risk.' I understand, but think this logic meets a comfort factor rather than truly assuring human safety. So, even if not a molecular target, I think a well defined pharmacology profile pointing to biochemical impact is required in today's climate.

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31. dearieme on November 23, 2010 6:48 PM writes...

I know that Freudianism is a busted flush, but you must admit that it gave us a few handy phrases. "Displacement activity" is one: or "management science" as some like to call it.

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32. Galenus on November 23, 2010 7:03 PM writes...

I am surprised that AstraZeneca scientists could publish such a paper with a straight face. After all, this is the company that spent $40 billion in R&D since it was created in 1999, and got 3 drugs (in the US) for it. Is this really a recipe for the rest of us, or a roadmap for a race to the bottom?

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33. Anonymous on November 23, 2010 7:36 PM writes...

To paraphrase Hanns Johst, "When I hear the words six sigma, I release the safety on my Browning."

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34. Anonymous on November 23, 2010 11:49 PM writes...

Derek - I think you (and anyone else) is delusional if you think that "we don't have to sink". We've already struck the iceberg, the captain and crew took the lifeboats (or were those golden parachutes), many of the passengers have already drowned and the big giant behemoth is going down fast. The rest of us are all just trying to bail out the water in vain quibbling amongst ourselves about whether a bucket or a beaker works better and pointing fingers at who's to blame. We're all on a ship of fools at this point.

Problem: pharmaceutical R&D failed to deliver enough new drugs to sustain growth.

Solution: reduce investment in R&D, hire the least experienced/cheapest labor you can find and market the hell out of what you have.

Even if the industry ramped up R&D to twice what it used to be, it's too late.

(One day they will teach the folks in B-school why that plan didn't work.)

Let's face it, the industry has fired far more scientists than they have hired. I don't care what paradigm you want to dream up for fixing this boat, the gig's over....even if the band plays on.

BTW, songs from the playlist included: The Blockbuster Blues, The Combichem Cha-cha, The Genomics Gavotte, The Proteomics Polka, The Offshore One-step, The Sigma Six Shuffle, and, the band's cueing up their encore, Working at the WalMart Whip.

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35. entropyGain on November 24, 2010 1:58 AM writes...

Today's Amira news emphasizes how badly the business model is broken, even for small companies. Real drug hunters started a company a few years ago, kicked butt, made drugs, made deals, took them to the clinic...

Then, staff cut in half, founders leave, management to focus on development of clinical assests...

Maybe the founders just want to do it all again, but lot of time, money, effort wasted in building again from scratch.

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36. Swimmer13 on November 24, 2010 4:43 AM writes...

I agree with 34. None of this stuff is going to save the industry as we know it. It's going to crash and burn and then something (as yet unspecified) will rise from the ashes. I'm already swimming away from the wreck and all this 'six sigma' and so on is scientists trying to carve out new careers for themselves that will survive their own individual shipwrecks. Who can blame them - wish I'd had a bit more foresight myself!

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37. ThomasR on November 24, 2010 5:29 AM writes...

The pharmaceutical industries problems are not realizing that our understanding of human physiology is infinitesimally small. Consider that the human body processes ~ 15 trillion bits of information per second. You just can’t apply a standard business model when developing treatments for something that complex. It will basically be a random process for the next few millenniums or so…..

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38. Cellbio on November 24, 2010 10:10 AM writes...

EntropyGain,

I'd be interested to hear your thoughts about why Amira shows the business model is broken. I could see one aspect maybe, that being the value of clinical leads is too low to support a small company. However, I also think that however painful the shift in Amira's focus is to current staff, and to be sure it is, being able to make that transition to development of clinical assets is a natural transition for successful companies, a testament to the success of the drug hunters.

Amira is not Merck, so the founding team can't pass their outstanding chemical matter off to a large development organization and return to the bench (hoods) to do it again and again. At some point, the investment thesis changes, and though a tough decision, from the outside, it does seem like a good business decision. Founders may have to start again, but what they created gets a chance for clinical success, and the dollars were not available for Amira to support those clinical trials and create more IND candidates that could be developed. Lack of capital for discovery and early development is a problem (maybe that is what you see?). Wonder if an Amira-like start-up could get funding today?

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39. Bryan on November 24, 2010 11:34 AM writes...

Regarding #2 and #3:

The assumption you're making, Derek, is that there are 'better' (single, magic) targets out there somewhere.

I'm guessing this is a large part of the problem.


Certainly, the data pouring out of the GWAS studies indicates that most common and complex diseases are not likely to be adequately treated by some drug which hits the 'magic target'

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40. Anonymous on November 24, 2010 2:24 PM writes...

Cellbio

While we only know what's on the surface of the Almira news, let's assume for the sake of discussion that it is what it looks like. Investors booting scientist/founders & research to milk the development assets they created. Let's further assume that the founders were smart enough to write employment contracts, vesting schedules etc to take care of themselves. The question is then what happens to a productive discovery team and the individuals that comprise it?

Re the team: it is disbanded. Financial pressures will force individuals to take what jobs they can find and while a few may end up together, the team is gone. Drug discovery is a team sport where the group dynamic may be as important as the skills of the individuals. Therefore this aspect of the business model is broken because it rewards success with destruction -- an evolutionary dead end.

Re the individuals: Happy holidays! Great job, you may have helped millions, made lots of coin for the investors & management. We will generously provide outplacement services and counseling. How was their equity structured? Will they ever benefit from the drug they created? Generally, once you leave there is seldom a mechanism to retain upside for the little guys. Again success penalized. The business model here is broken because it disincentivizes the individuals from succeeding. Why put in those extra hours/nights/creative energy to make a drug when all your doing is putting yourself out of work?

Re the company: The investment thesis now becomes flipping assets, they've walked away from the concept of creating assets. Where will the next clinical candidates come from? The company is now a dead end, just waiting for an exit. Upside is limited to whatever the company can be sold for based on the success of current assets. There will be no more genentech's or amgens if this is the business model. Again, another evolutionary dead end.

And yes, there is a widespread lack of capital for discovery and early development. Fewer options for Amira-like startup to fund today. As big pharma continue to march off the patent cliffs like lemmings, there will be less and less investment for discovery, there will be less new development pipeline, less approvals, less revenue, less investment....

5 years from now, anyone who somehow managed to finance a compound to Phase II will be in the driver's seat. I just hope they're smart enough to use it to build a real company rather than simply flip it and give up.

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41. CMCguy on November 24, 2010 3:50 PM writes...

#38 Cellbio while I intellectually understand the concept for staffing switch that goes along with the natural and often drastic transition from discovery to development I would hesitate to use the term successful company unless are qualifying as temporary survival. Indeed it is a big dilemma to sustain R efforts when the huge costs of D start to occur and funding sources seem to swing opposite to the stage most needed. Fundamentally R works best when connected strongly to D and vise versa. Plus in long term D will become just as obsolete if there is no R so where is the success. #40 Anon has good outline of impacts.

Correct Amira is not Merck so do not have same options but I am uncertain if Merck is Merck anymore as both R and D are seemingly shadows of former capabilities, largely by self inflicted wounds. Problem is generally most Big Pharma seems to be extremely overly business/marketing focused and even though the pump money back into R&D the environments are not highly conducive. Harking back to the start of Derek's post it is probably stuff like Six Sigma that either drives away or inhibit innovation potential that does exist.

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42. Cellbio on November 24, 2010 6:24 PM writes...

# 40, thanks for engaging with thoughtful comments.

First, it is what it looks like, won't say more, but have some insights.

Team is disbanded, but careers are limited, so don't buy the evolution parallel of a dead end. Applied to the field in general, not an evolutionary dead end if the founders do realize gain, and repeat the process or motivate others to do the same. They will realize personal gain after their departure, since they are major equity holders in Amira. The argument of individuals not being incentivized is not correct, unless there driven by salary only.

Also don't see this at all as flipping assets, but rather moving on to prove the value of the created assets. Actually, I think the reason they are in this predicament is that flipping assets, at least as I define that phrase, doesn't pay anymore with large up-fronts that fuel your company. Do agree that today's climate does not allow for another genetech or amgen. I think this is a true failure of the investment thesis today, but the counter argument is that biotech investment is, I think, a net negative, especially if you drop amgen and genetech from the equation, so as much as I like the model, who would look at three decades of biotech investing and risk 100 MM or more to make another soup to nuts company?

CMCguy, interim success is a much better concept to have invoked. They created assets worthy of development, success for that stage. I agree with your R&D statements, and your assessment that it doesn't work in pharma or big biotech, so I opt to work on the R side in small cos. Yes it means the likely outcome is feeding the beast, but I do not see this as bad, or asset flipping, but the natural progression of our business which will have the dollars for big D in pharma, and the engine of discovery in smallcos.

Maybe Six Sigma mindset drove the Merck scientists to start Amira in the first place? Would be the first positive influence I know of....

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43. entropyGain on November 24, 2010 8:09 PM writes...

Cellbio -

I'd specifically left the founders out of my comments (forgot to sign #40). I hope they do do it again and if anyone can maybe it's them.

My comment on rank and file scientists not being incentivizes was that in all likelihood they have options that expire at some period after their departure- probably before the value is realized. If they're lucky they actually have RSUs that they can hold. But I've seen time and again scientists cut to free money for development with their options expiring underwater. A year later after the development of their compound succeeds money comes in, remaining management gets lots of juicy stock/bonus etc, and the grunts who made the compounds are still looking for jobs that have permanently gone overseas.

I agree that current investment thinking will not allow another amgen/genentech/vertex to be built from investor dollars... I do however think we as an industry and as a society need to find a way to do it anyway.

Maybe the small european family owned pharma's are the correct model (though they've been under pressure as well). At least they can think long term. The problem is they bootstrapped in a post WWII era when making money from drugs was a different business. The problem they face now is a couple generations distance from the founder's who built them.

Overall, we're strip mining discovery when what we need is a sustainable way to farm it.

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44. Cellbio on November 24, 2010 8:43 PM writes...

EG

Great comments. Agree the "grunts" are hurt the most.

Hope you've got some ideas on how to be sustainable in discovery. The most viable model I see today is one in which the workforce moves around a lot more than prior times, companies come and go, but the pool of discovery talent remains "sustainable" due to pharma's need to replenish pipelines. Of course, the sustainable nature of the model has to address issues you raise like having a persistent interest in the value you create as a worker, RSUs over options.

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45. FBomber on November 24, 2010 11:25 PM writes...

@25

" - as in, start my own company - "

Hmmmmmm- imagine the legion of talent you would have banging on the door.

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46. Anonymous on November 24, 2010 11:39 PM writes...

Hilarious "The Blockbuster Blues, The Combichem Cha-cha, The Genomics Gavotte, The Proteomics Polka, The Offshore One-step, The Sigma Six Shuffle." - I LOVE IT. Currently I'm playing the unemployed underground.

Hey guys I don't mean to spam but I've created a forum call CafeChemist. It's like cafepharma is only just for chemists. Company boards may come later due if there is interest.

If you are interested in holding a long term discussion over there feel free. Registered users or anonymous posting allowed. No ads or fee's just doing it because I think we need a place.

Again not to take anything away from Derek's blog, but theses comments sections disappear over 2 weeks.

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47. anonymous on November 25, 2010 2:56 AM writes...

26 and 34 are on the right track. But let me go further. Are we really less scientifically successful than we were 30 years ago? I don't think so. Here's the real problem: Putting a drug on the market, and having it be a commercial success, are NOT scientific/technical problems. The FDA is not set up to approve more than about 20 NCEs a year. If the industry brings 50 good NDAs forward in a year, there will still only be 20 approvals (more or less). This isn't a conspiracy theory, but the agency faces a variety of constraints on what it does, and it has to answer to its various constituencies. For example, let me ask: Who pays for drugs? We all do, but we pay through insurance companies and through various branches of state and federal government. Do these payers really want to see new drugs approved? Of course not. And of course pharma companies spend a lot of money on lobbying and advertising, so you see that influence as well. The net outcome: 20 new drugs a year. And of course some of these will be for orphan indications or small markets. This output, of course, is not enough to feed the pharma beast. They're doing their best with this situation; i.e. trying to extend the lifetime of each drug that is approved (biologicals, evergreening, etc), and trying to maximize the market served by each NCE. But payers are less willing (and able) to pay than they were. Will there ever be more lipitors and diovans? I'm not so sure. Pharma will just be a smaller industry in the future. And drug discovery will be done on the cheap as much as possible, because the pockets just won't be as deep as they were. This is the grand experiment that is going on at most of the big pharmas today: Can we scrap the huge research infrastructure, and yet pick up enough stuff from universities, eastern Europe, or cash-strapped biotechs to keep the enterprise going with a cheaper R and D burn? I don't think it's really a scientific problem.

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48. Annette Bak on November 25, 2010 7:25 AM writes...

I believe that organizational issues are at the hear of the pharmaceutical industry's problem. A leaner organization industry wide with more business focus may indeed be a solution.

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49. processchemist on November 25, 2010 9:33 AM writes...

@Entropygain

"Maybe the small european family owned pharma's are the correct model (though they've been under pressure as well)"

Few years ago, a small european company (family owned etc.) turned to the usual big consulting firm for a solution to the their crisis. Obviously, the consultants said: layoffs. The (old) owner said: thanks a lot, no massive layoffs in our company, goodbye.
But the R&D budget underwent anyway to what I can call (as external observer, after almost five years) a "structural cut".
And I know, first hand, of many other examples. The urgence to cut costs spreaded everywhere.
Also one of the main questions is "what will happen when the next generation of owners will get the leadership?".

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50. pete on November 26, 2010 11:44 PM writes...

@ 48
Reorganize all you want. Cut staff. Focus on business.

Oh, and don't forget. Before you go home for the evening, remember to ask the scientists to make you a drug.

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51. DCRogers on December 2, 2010 5:41 PM writes...

@10: "costumer"

Beautiful.

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52. befuddled on December 2, 2010 6:33 PM writes...

@47, anon,

Do you really think that the FDA actively avoids approving drugs because another branch of the government doesn't want to pay for them?

While it's true that the FDA probably couldn't handle 50 NDAs a year in it's current state, but I think we can all agree that it's unlikely to face that situation in the foreseeable future.

Whether health care financers, public or private want to pay for a new drug depends on the circumstances, I think. I don't think they would want to pay for a new proprietary statin that couldn't offer compelling advantages over the existing drugs. Nor would they want to pay huge sums for another oncology drug that makes a difference of a few months at best. But I'm sure they would be happy to pay for a drug that actually decreased overall medical costs.

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53. John on December 18, 2010 12:43 PM writes...

Placing tremendous weight on 3-D structures found in co-solvents completely alien to anything in vivo or crystal structures for that matter (because we're cystalline in vivo ;) ) was stupid 20 years ago, and is still stupid today. People love sitting on their butts at the computer playing with those figurines though.

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