About this Author
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: Twitter: Dereklowe

Chemistry and Drug Data: Drugbank
Chempedia Lab
Synthetic Pages
Organic Chemistry Portal
Not Voodoo

Chemistry and Pharma Blogs:
Org Prep Daily
The Haystack
A New Merck, Reviewed
Liberal Arts Chemistry
Electron Pusher
All Things Metathesis
C&E News Blogs
Chemiotics II
Chemical Space
Noel O'Blog
In Vivo Blog
Terra Sigilatta
BBSRC/Douglas Kell
Realizations in Biostatistics
ChemSpider Blog
Organic Chem - Education & Industry
Pharma Strategy Blog
No Name No Slogan
Practical Fragments
The Curious Wavefunction
Natural Product Man
Fragment Literature
Chemistry World Blog
Synthetic Nature
Chemistry Blog
Synthesizing Ideas
Eye on FDA
Chemical Forums
Symyx Blog
Sceptical Chymist
Lamentations on Chemistry
Computational Organic Chemistry
Mining Drugs
Henry Rzepa

Science Blogs and News:
Bad Science
The Loom
Uncertain Principles
Fierce Biotech
Blogs for Industry
Omics! Omics!
Young Female Scientist
Notional Slurry
Nobel Intent
SciTech Daily
Science Blog
Gene Expression (I)
Gene Expression (II)
Adventures in Ethics and Science
Transterrestrial Musings
Slashdot Science
Cosmic Variance
Biology News Net

Medical Blogs
DB's Medical Rants
Science-Based Medicine
Respectful Insolence
Diabetes Mine

Economics and Business
Marginal Revolution
The Volokh Conspiracy
Knowledge Problem

Politics / Current Events
Virginia Postrel
Belmont Club
Mickey Kaus

Belles Lettres
Uncouth Reflections
Arts and Letters Daily
In the Pipeline: Don't miss Derek Lowe's excellent commentary on drug discovery and the pharma industry in general at In the Pipeline

In the Pipeline

« Spending and Publishing | Main | Holiday Organic Synthesis: Chocolate Pecan Pie »

November 23, 2010

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

Email This Entry

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


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.

Permalink to Comment

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).

Permalink to Comment

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.

Permalink to Comment

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.

Permalink to Comment

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.

Permalink to Comment

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...

Permalink to Comment

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?

Permalink to Comment

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.

Permalink to Comment

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).

Permalink to Comment

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.


Permalink to Comment

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.

Permalink to Comment

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...

Permalink to Comment

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.

Permalink to Comment

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"

Permalink to Comment

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).

Permalink to Comment

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?

Permalink to Comment

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.

Permalink to Comment

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

Permalink to Comment

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

Permalink to Comment

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!

Permalink to Comment

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.

Permalink to Comment

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.

Permalink to Comment

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.

Permalink to Comment

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.

Permalink to Comment

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.

Permalink to Comment

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.

Permalink to Comment

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 mo