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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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June 18, 2013

Bernard Munos on The Last Twelve Years of Pharma

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Posted by Derek

Bernard Munos (ex-Lilly, now consulting) is out with a paper reviewing the approved drugs from 2000 to 2012. What's the current state of the industry? Is the upturn in drug approvals over the last two years real, or an artifact? And is it enough to keep things going?

Over that twelve-year span, the average drug approvals ran at 27 per year. Half of all the new drugs were in three therapeutic areas: cancer, infectious disease, and CNS. And as far as mechanisms go, there were about 190 different ones, by Munos' count. The most crowded category was (as might have been guessed) the 17 tyrosine kinase inhibitors, but 85% of the mechanisms were used by only one or two drugs, which is a long tail indeed.

Half those mechanisms were novel - that is, they were not represented by drugs approved before 2000. Coming up behind these first-in-class mechanisms were 29 follow-on drugs during this period, with an average gap of just under three years between the first and second drugs. What that tells you is that the follower programs were started at either about the same time as the first-in-class compounds (and had a slightly longer path through development), or were started at the first opportunity once the other program or mechanism became known. This means that they were started on very nearly the same risk basis as the original program: a three-year gap is not enough to validate much for a new mechanism, other than the fact that another organization thinks that it's worth working on, too. (Don't laugh at that one - there are research department that seem to live only for this validation, and regard their own first-in-class ideas with fear and suspicion).

Overall, though, Munos says that that fast-follower approach doesn't seem to be very effective, or not any more, given that few targets seem to be yielding more than one or two drugs. And as just mentioned, the narrow gap between first and second drugs also suggests that the risk-lowering effect of this strategy isn't very impressive, either.

Here's another interesting/worrisome point:

The long tail (of the mode-of-action curve). . . suggests that pharmaceutical innovation is a by-product of exploration, and not the result of pursuing a limited set of mechanisms, reflecting, for instance, a company’s marketing priorities. Put differently, there does not seem to be enough mechanisms able to yield multiple drugs, to support an industry. . .The last couple of years have seen an encouraging rise in new drug approvals, including many based on novel modes of action. However that surge has benefited companies unequally, with the top 12 pharmaceutical companies only garnering 25 out of 68 NMEs (37%). This is not enough to secure their future.

Looking at what many (most?) of the big companies are going through right now, it's hard to argue with that point of view. The word "secure" does not appear within any short character length of "future" when you look through the prospects for Lilly, AstraZeneca, and others.

Note also that part about how what a drug R&D operation finds isn't necessarily what it was looking for. That doesn't mesh well with some models of managment:

The drug hunter’s freedom to roam, and find innovative translational opportunities wherever they may lie is an essential part of success in drug research. This may help explain the disappointing performance of the programmatic approaches to drug R&D, that have swept much of the industry in the last 15 years. It has important managerial implications because, if innovation cannot be ordained, pharmaceutical companies need an adaptive – not directive – business model.

But if innovation cannot be ordained, why does a company need lots of people in high positions to ordain it, each with his or her own weekly meeting and online presentations database for all the PowerPoint slides? It's a head-scratcher of a problem, isn't it?

Comments (29) + TrackBacks (0) | Category: Drug Development | Drug Industry History


COMMENTS

1. petros on June 18, 2013 8:26 AM writes...

Unfortunately the article is behind a paywall
At least one fast follower comes to mind that has been a great commercial success. Merck's sitagliptin has greatly surpassed the original gliptin, Novartis' vildagliptin, and driven the uptake of this whole class.

Although approved just before the period of Munos' review, Merck had previously managed to completely dominate the leukotriene antagonist market despite montelukast being the third in class agent!

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2. bboooooya on June 18, 2013 8:35 AM writes...

I've always liked this phrase from KBS' Nobel lecture "Many of you learned to tolerate my style of directing research (an oxymoron perhaps?)".

Sadly, this (http://dilbert.com/dyn/str_strip/000000000/00000000/0000000/000000/00000/0000/100/137/137.strip.gif) is the philosophy most MBAs believe in.

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3. exGlaxoid on June 18, 2013 8:53 AM writes...

I think that the observational and serendipitous way to novel drugs has done very well. When we made compounds for specific programs of early discovery, they were also put into the High Throughput screens, which at one time were over 100 per year. The VAST majority of compounds found as hits in the HTS were not from compounds made for that program, and many were not even "predicted" to have any activity by any models or theories.

There are some targets which are more amenable to designed ligands, such as estrogen ligands, where a phenol seems to be key. But for many targets, the hits obtained from HTS came from many random sources, and to me it shows the folly of trying to direct research only in certain profitable areas, as molecules don't seem to take direction well. Also, the commercial people have been wrong so many times on predicting a compounds success.

I would argue for going back to more cellular and animal screening, more simple HTS for those areas with known receptors, and more preclinical work on more compounds (rather than trying to pick only "one" winner for every project). Also, we need a way to do clinical trials more cost effectively, whether via shorter phase 3 and then some phase 4, or by being more realistic about risks and cutting back the size of clinical trials.

Unfortunately, the FDA, congress, and lawyers have nearly killed the pharmaceutical discovery business, so that will all likely happen elsewhere, where costs and risk are lower, and then we will only be able to buy the newest drugs over the internet from overseas, without ANY real regulations or oversight, much like the generic industry that they have created overseas.

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4. Hap on June 18, 2013 9:02 AM writes...

Or Lipitor? It was preceded by Pravachol, Baycol, and Zocor (and what else?), and it did pretty well (and Zocor didn't do badly, either).

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5. Anonymous on June 18, 2013 9:03 AM writes...

Bernard mirrors what I have come to believe over 15 years in industry - that we don't 'break' a disease. What the industry is good at is turning a fundamental breakthrough into a medicine. And yes this happens effectively randomly across disease space and doesn't fit into big pharmas model of letting marketing decide which diseases we will work on.

Disease areas and Bio/Chem groups (a relic of our academic heritage) should all have gone and Discovery should be as fully projectized as possible. Project teams should then be assembled around the approaches with the best human evidence that they will work whatever the disease and the modality of approach selected following that. Disease expertise can be bought on a consulting basis and of course you would need a decent bunch of scientists selecting the projects based on the data alone but most of the middle and upper management could be bypassed.

I believe George Merck gave a great quote about profits following the medicine and about remembering that. Bernards article reaffirms this in another way.

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6. Anon on June 18, 2013 9:05 AM writes...

So basically, "let scientists be scientists...just not the academic kind"
I kid! ;-)

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7. Hap on June 18, 2013 9:25 AM writes...

Sorry...I'm not sure how quickly the statins followed each other (Pravachol was early, and probably Zocor, but I'm not sure about the others).

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8. petros on June 18, 2013 9:58 AM writes...

The statins US approval dates

1987 lovastatin (Mevacor)
1991 simvastatin (Zocor)
1993 fluvastatin (lescol)
1996 atorvastain (Lipitor)
1997 cerivastatin (Baychol)
2003 rosuvastatin (Crestor)
2009 pitvastatin (Livalo)

Permalink to Comment

9. petros on June 18, 2013 10:01 AM writes...

and
1991 pravastatin (Pravachol)

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10. flem on June 18, 2013 10:18 AM writes...

I would bet 2nd or later entries almost always do better if they are approved based on biomarkers or acute symtoms: e.g. ranitidine vs cimetidine; enalapril vs captopril; simvastatin vs lovastatin; valsartan vs losartan; etc. Exploiting better dosing or development strategies make this feasible. However I suspect the same cannot be said for drugs approved based on outcomes (e.g.most oncology drugs) Any thoughts?

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11. DrSnowboard on June 18, 2013 10:30 AM writes...

http://www.nature.com/nrd/journal/v12/n6/full/nrd4035.html may be relevant. However, given that HIV cpds are excluded from the analysis on the grounds of 'unusual dynamics' and given that combination regimens seem to be increasingly used in other therapeutic areas, perhaps 'in the CNS and Statin markets' could be added to the article title

Permalink to Comment

12. exGlaxoid on June 18, 2013 10:45 AM writes...

In the past, a mediocre drug might be approved as the first of its class, then other companies could build on it's pros and cons to create better compounds. Examples might be Tagamet, Rezulin, several early antibiotics. But each was allowed to go to market, and that created an incentive for others to follow and improve on it. Now, very few first in class drugs are approved, as they are not "perfect", thus killing the class and causing other companies to abandon the class before having a chance to improve the class.

We all know that ibuprofen, aspirin, Tylenol, penicillin, and many others would never be approved today, yet they are all still useful drugs, which have lead in most cases to better ones. But now that process is stopped long before a better drugs can be found.

Permalink to Comment

13. John Wayne on June 18, 2013 11:19 AM writes...

I'd like to expend on what commenter #12 said and relate it to a previous post by Derek; when an invention is new it is usually not very good. Improvements are often made subsequent to the breakthrough, and then it gets progressively better.

Let's relate this to the drug industry with a specific example: we have to be willing to accept a mediocre treatment to prevent the onset of Alzheimer's disease. The term "we" has to include chemists, biologists, project managers, clinicians, key opinion leaders in medicine, the people who pick what companies work on, the FDA, and insurance companies. It could be argued that the complexity of our system is making it hard for us to get anything new done. Great drugs aren't usually going to come fully formed out of the ocean like Aphrodite; even if that does happen from time to time, it doesn't represent a reasonable business model.

Permalink to Comment

14. simpl on June 18, 2013 11:47 AM writes...

re #6 "let scientists be scientists..." That is close to home. How about "let scientists be entrepreneurs - with the company's money"? That allows non-linear progress upon interesting observations, and competition for a stake also explains why there is intense peer and management interaction, despite all the disparaging comments in a recent thread on the Merck reorganisation.

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15. Anonymous on June 18, 2013 12:38 PM writes...

#5: George Merck: "profits follow the medicine"

Perhaps for companies -- for researchers (esp. small biotech), "firings follow the medicine".

And for management: "bonuses precede the medicine". (But follow the firings?? :-/ )

My head hurts.

Permalink to Comment

16. Entre prendre on June 18, 2013 12:47 PM writes...

#14 "let scientists be entrepreneurs - with the company's money"

That sounds more like a kid at Dysneyland.

Permalink to Comment

17. Dr. Manhattan on June 18, 2013 2:08 PM writes...

"why does a company need lots of people in high positions to ordain it, each with his or her own weekly meeting and online presentations database for all the PowerPoint slides? It's a head-scratcher of a problem, isn't it?"

Indeed! And as programs fail under these people, they move on to other companies where their "experience" is touted. Back in the early 80's, most of my senior managers could point to drugs they helped develop. That's not very common these days...

Permalink to Comment

18. CMCguy on June 18, 2013 2:46 PM writes...

I can argue that (mis)Management by bottom-line MBA thinking has done much damage to drug industry innovation in past several decades however we can not lose sight that R&D community has not been flawless in the missteps. #6 states "let scientists be scientists...just not the academic kind" and I think often industry scientists can get overly absorbed in their field/work where they do forget both missions to directly aid patients and remain a viable business (therefore act more like academics). Yes there must be a certain amount of freedom for drug hunters but if left unfettered they could wind up in the middle of the woods after a long wandering path to nowhere and get eaten by bears. Need to be adaptive and focused at the same time which is a had balance to achieve and then sustain.

There has always been much chasing and energy spent by R&D types on the "next best" approaches as panaceas to improve drug discovery with most being over-hyped and ending up at most providing tools. Majority of these supposed advancements probably appear to have started as good scientific concept that were over simplified and grabbed onto by people lacking sufficient knowledge to understand total picture but in positions where were easily convinced had to be better that old ways. At the same time much complicity of scientists who also bought in or remained silent when realized limited potential in real world.

Wouldn't most people agree if we understand a disease mechanism or mechanism of action of a drug its a good thing and likely to increases odds of success? The above evaluation may suggest it does help but only in a narrow sense with a price being other opportunities are missed. I worry as both the mentally that dominates and lack of good critical mass that is present that pharma/biotech can not be re-invigorated to have the balance to seek new knowledge then learn how to focus to bring new drugs forward

Permalink to Comment

19. drug_hunter on June 18, 2013 4:32 PM writes...

Not trying to be snarky, but is there anything new in this paper? We need more novel targets, and we need to let our scientists explore freely. Updating the analysis by including the latest approved drugs is useful, but the message has been clear for a long time now. Right? Does anyone see an intellectual breakthrough in this paper?

Permalink to Comment

20. obvious on June 18, 2013 7:53 PM writes...

Pharma's central problems are:

1) An expanding industry chasing fixed output by academia/NIH due to stagnant govt funding.

2) Chasing the same biology as everyone else in the name of blockbusters/franchises, rather than being opportunistic and selecting the best targets.

This has nothing to do with hit rates, but there is also gross misallocation of pharma resources to end-of-life diseases where life quality and life span elasticity are negligible. U.S. needs a NYCE-like committee to throttle the $90,000 Rx that extends life only 3 months. Fine if some folk want to pay out of pocket, but society can't afford it for all.

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21. Renee on June 18, 2013 8:00 PM writes...

"We all know that ibuprofen, aspirin, Tylenol, penicillin, and many others would never be approved today, yet they are all still useful drugs, which have lead in most cases to better ones."

As a non-pharma chemist, why is this? Is it because of too many serious side effects with these drugs? Even penicillin?

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22. johnnyboy on June 18, 2013 10:08 PM writes...

@21: Aspirin: too many side effects. Tylenol: frighteningly low therapeutic index (ie. difference between therapeutic dose and toxic dose).
Ibuprofen and penicillin would probably still be approvable.

Permalink to Comment

23. MTK on June 19, 2013 7:48 AM writes...

I did not read the paper, so excuse me if I'm misrepresenting things here, but isn't the phrase "pharmaceutical innovation is a by-product of exploration" just a euphemism for dumb luck? It's not even an outcome or intended product of exploration, but a by-product.

If that's the case that dumb luck is the most important factor than management is somewhat irrelevant. You can do it any ol' way you want. The only real decision is how many rolls of the dice do I want to make and how much money do I want to have on each roll.

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24. Hap on June 19, 2013 8:53 AM writes...

Aren't there a bunch of aphorisms about that, though? Not all luck is blind, or dumb. We didn't make the universe, and we don't know where all the treasure is hiding - all we can do is use the knowledge we have to make good guesses and be prepared for what we find.

What seems to be one of the problems with pharma management is their unwillingness to follow the consequences of what their people find. Just because you don't like the answers you get and select for those who will give you the ones you do like does not obligate biology or chemistry or medicine to accede to your illusions. If you don't trust scientists with your money (probably reasonable - it isn't our training, or authority), why should you trust management with science (which they don't necessarily know, and can't manipulate in any case)?

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25. DrugA on June 19, 2013 9:21 AM writes...

To #12 and #13. Drugs do not have to be perfect to get approved. They only have to have benefits that outweigh the risks, as shown by data. Drugs with horrendous toxicities get approved when they are better than other options (think oncology, MS). But if a drug is not better than placebo, it should not be approved. If it harms more than helps, it should not be approved. If it is better than placebo, but appears inferior to existing treatments (I say "appears", because statistically and medically, it is rarely clear-cut), then the drug is likely to be approved when it is possible to describe some situation or group of patients who should get it (eg patient subgroups, second line treatment, etc.) There is no evidence that drugs don't get approved because they aren't perfect.

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26. NJBiologist on June 19, 2013 11:28 AM writes...

@21 Renee, 22 johnnyboy: Ibuprofen has the same lethal GI bleed issue as aspirin (and every other COX-1 inhibitor); penicillin is prone to causing allergic reactions ranging from a rash to anaphylaxis.

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27. Get Lucky on June 19, 2013 11:58 AM writes...

Pharma-Biotech industry: Comes down to harnessing luck as an industrial product. I heard that said in this very blog I think. And we in Biotech wouldn't have it any other way. Too many variables, too many unknowns, all about shots on goal and taking risks. Risk-adverse behavior is not fruitful here. Look it up.

Permalink to Comment

28. Dr Livingstone on June 19, 2013 5:40 PM writes...

Discovering drugs is still more akin to journeying into a dark continent than putting a man on the moon.

Not comforting to controllers who give audiences to journals with a high impact factor, but strangely reassuring to responders who give reality a daily audience at the bench and/or PC...

Permalink to Comment

29. London_Chemist on June 20, 2013 2:46 AM writes...

@22 Forget ibuprofen: nephrotoxic and can aggravate asthma.

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