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Derek Lowe The 2002 Model

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

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

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February 1, 2011

The NIH's New Drug Discovery Center: Heading Into the Swamp?

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Posted by Derek

I've been meaning to comment on the NIH's new venture into drug discovery, the National Center for Advancing Translational Sciences. Curious Wavefunction already has some thoughts here, and I share his concerns. We're both worried about the gene-o-centric views of Francis Collins, for example:

Creating the center is a signature effort of Dr. Collins, who once directed the agency’s Human Genome Project. Dr. Collins has been predicting for years that gene sequencing will lead to a vast array of new treatments, but years of effort and tens of billions of dollars in financing by drug makers in gene-related research has largely been a bust.

As a result, industry has become far less willing to follow the latest genetic advances with expensive clinical trials. Rather than wait longer, Dr. Collins has decided that the government can start the work itself.

“I am a little frustrated to see how many of the discoveries that do look as though they have therapeutic implications are waiting for the pharmaceutical industry to follow through with them,” he said.

Odd how the loss of tens of billions of dollars - and vast heaps of opportunity cost along the way - will make people reluctant to keep going. And where does this new center want to focus in particular? The black box that is the central nervous system:

Both the need for and the risks of this strategy are clear in mental health. There have been only two major drug discoveries in the field in the past century; lithium for the treatment of bipolar disorder in 1949 and Thorazine for the treatment of psychosis in 1950.

Both discoveries were utter strokes of luck, and almost every major psychiatric drug introduced since has resulted from small changes to Thorazine. Scientists still do not know why any of these drugs actually work, and hundreds of genes have been shown to play roles in mental illness — far too many for focused efforts. So many drug makers have dropped out of the field.

So if there are far too many genes for focused efforts (a sentiment with which I agree), what, exactly, is this new work going to focus on? Wavefunction, for his part, suggests not spending so much time on the genetic side of things and working, for example, on one specific problem, such as Why Does Lithium Work for Depression? Figuring that out in detail would have to tell us a lot about the brain along the way, and boy, is there a lot to learn.

Meanwhile, Pharmalot links to a statement from the industry trade group (PhRMA) which is remarkably vapid. It boils down to "research heap good", while beating the drum a bit for the industry's own efforts. And as an industrial researcher myself, it would be easy for me to continue heaping scorn on the whole NIH-does-drug-discovery idea.

But I actually wish them well. There really are a tremendous number of important things that we don't know about this business, and the more people working on them, the better. You'd think. What worries me, though, is that I can't help but believe that a good amount of the work that's going to be done at this new center will be misapplied. I'm really not so sure that the gene-to-disease-target paradigm just needs more time and money thrown at it, for example. And although there will be some ex-industry people around, the details of drug discovery are still likely to come as a shock to the more academically oriented people.

Put simply, the sorts of discoveries and project that make stellar academic careers, that get into Science and Nature and all the rest of them, are still nowhere near what you need to make an actual drug. It's an odd combination of inventiveness and sheer grunt work, and not everyone's ready for it. One likely result is that some people will just avoid the stuff as much as possible and spend their time and money doing something else that pleases them more.

What do I think that they should be doing, then? One possibility is the Pick One Big Problem option that Wavefunction suggests. What I'd recommend would also go against the genetic tracery stuff: I'd put money into developing new phenotypic assays in cells, tissues, and whole animals. Instead of chasing into finer and finer biochemical details in search of individual targets, I'd try to make the most realistic testbeds of disease states possible, and let the screening rip on that. Targets can be chased down once something works.

But it doesn't sound like that's what's going to happen. So, reluctantly, I'll make a prediction: if years of effort and billions of dollars thrown after genetic target-based drug discovery hasn't worked out, when done by people strongly motivated to make money off their work, then an NIH center focused on the same stuff will, in all likelihood, add very little more. It's not like they won't stay busy. That sort of work can soak up all the time and money that you can throw at it. And it will.

Comments (36) + TrackBacks (0) | Category: Academia (vs. Industry) | Drug Assays | Drug Development | Drug Industry History


1. Virgil on February 1, 2011 10:33 AM writes...

" mental health. There have been only two major drug discoveries in the past century; lithium and Thorazine..."

I beg to differ on that one Dr. Collins. Ever heard of fluoxetine, duloxetine, haloperidol, gabapentin, valproate, diazepam, methylphenidate? Clearly he doesn't know much pharmacology. Not a good situation for someone in charge of a drug discovery program.

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2. wwjd on February 1, 2011 10:49 AM writes...

This is something that should be cut to balance the budget. Stop wasting tax dollars.

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3. milkshake on February 1, 2011 10:52 AM writes...

why don't these nimrods buy one of the many abandoned pharma sites instead? The can get it for pennies on a dollar and set up a biotech incubator, with matching grants available for research projects in desirable areas?

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4. lynn on February 1, 2011 11:10 AM writes...

I wondered when you'de get around to this, Derek. I basically agree with you. I think there are important basic research questions that are necessary to move drug discovery forward and academe is the place to do it - in these days when Pharma does little basic research (it was not always thus). But academics and NIH in general do not seem to know what the problems are that need to be solved. I've made a point in my writings on antibacterial discovery to emphasize the need to solve the rate limiting problems - because if those are not alleviated, then no rational routes can go forward. For antibacterials - one major problem is how to get things into gram negative bacteria. Not easy. No need to find more targets or inhibitors of targets if you can't get to the targets. As you say, nice, specific phenotypic whole cell screens are one way around this [and Pharma used to do a lot of that BEFORE genomics led it astray]. So, hearing what Collins says they are aiming for does not hearten me. I hope they do bring in industry advisors; industry scientists, not managers! There is a lot of industrial expertise out there - much of it out of work.

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5. SP on February 1, 2011 11:16 AM writes...

"And although there will be some ex-industry people around, the details of drug discovery are still likely to come as a shock to the more academically oriented people."
I find it ironic that you'd be concerned about this when the post just above this is about 2400 people being laid off from Pfizer (albeit UK). There are enough pharma people around to staff this center several times over. The current NIH drug... I mean probe discovery network is mostly pharma refugees- some of the leadership is academic, but the professional staff running things almost all have pharma experience.

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6. Calm Down on February 1, 2011 11:45 AM writes...

What's wrong with applying the best practices from pharma minus the restrictions of being responsible to shareholders, plus the ability to publish all the results without worrying about IP?

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7. Lester Freamon on February 1, 2011 11:51 AM writes...

I just hope it's not too target oriented. The way the NIH could be useful is to simply find a slew of molecules that either 1) work well in phenotypic assays or 2) hit entirely novel targets, then do a modest medchem operation just to get to the point of stability and distribution after an IV/IP injection, and then (somewhat arbitrarily) test them in the, say, 25 most respectable models across different diseases with serious unmet medical need. It's a strategy that no VC would ever support, but it's pretty well validated in the history of drugs--just make some compounds that do something new and or powerful, and test them all over the place.

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8. Andrew Ryan on February 1, 2011 12:13 PM writes...

I completely agree with you Derek. I am working on a drug screen with a startup doing a whole-cell screening assay. That way, you know your drug works and gets into the cell (a bacterium, in this case) and then we can find the target later.

However, the screening people hate it. They want all target-based screens ("low-risk" as they put it, although low-risk drug screening is an oxymoron). They claim once something works on a target, then they'll see if it actually as the desired effect on a cell and they'll do chemistry to get into into the cell if necessary.

A major philosophical difference I suppose. In the case of antibacterials, all of our core scaffolds came from phenotypic screening, as for other drug classes I am not as knowledgeable.

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9. Jonathan on February 1, 2011 12:22 PM writes...

You seemed to be pretty complementary about their work last year:

That was done at NCGC, which is the high throughput screening center that will be part of NCATS, and is staffed heavily by ex-industry people.

Also, look at the diseases they're aiming at. Rare and neglected diseases aren't being well served by industry because there's no profit motive in it. Someone with giardia or schistosomiasis doesn't need a new drug that costs $30k a year if they live on a dollar a day.

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10. jimbo on February 1, 2011 12:27 PM writes...

@3 Milkshake

Excellent point! Makes too much sense though.

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11. Gerry on February 1, 2011 12:42 PM writes...

Dear Derek, linking genes to disease, in my opinion, is very important, but even more important is finding mechanisms that explain why genes lead to disease. To correct these defects we have been using small chemicals with quite some success. However, the model has picked all low hanging fruits and we need a paradigm shitf. That change of thinking has much more probability to arise in the academia where pressures for profit won't interfere with free thinkers. Dr Collins effort will bring talent to think about treatments and whenever talented people are let to fly things can happen.

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12. NJBiologist on February 1, 2011 12:55 PM writes...

@1: Yeah, that bothered me, too. (By the way, I'd add MAOIs and TCAs.) But if you expand the list to include a lot of what you named, you have to walk away from the assertion that it's all been accidental discovery.

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13. SP on February 1, 2011 1:15 PM writes...

3- Can you imagine the outcry about "government takeovers" if the NIH took over an abandoned pharma site? Not saying the outcry is justified, but these days few outcries are.

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14. Aidan on February 1, 2011 1:18 PM writes...

I might add a similar result was achieved with the DOD's biodefense efforts (billions of dollars spent, no useful drugs).

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15. Pete on February 1, 2011 2:30 PM writes...

Something like this could just work if they stick to an objective of using fundamental science to reduce the risks to Discovery organisations of exploiting new targets and disease mechanisms. A successful phenotypic screen will achieve a degree of target validation (even if you don’t know the target at this stage) and identify potential tool compounds. However, successful phenotypic screens will require access to good compound libraries and that takes time and $$$ to put together. Screening in animals does raise ethical issues (I don’t believe that you’d be able to do this in the UK although things may be different in the US). A better understanding of the Blood Brain Barrier would also reduce the risk of tackling CNS targets and the technical capability to measure (unbound) brain concentrations is well beyond some Discovery organisations. Whether you need to have a whole new institute to do this is debatable.

Milkshake’s comment “why don't these nimrods buy one of the many abandoned pharma sites instead?” is especially noteworthy. First ‘nimrod’ is the name of a maritime reconnaissance aircraft which is currently in the UK news because they’re being scrapped (to howls of protest) because they’ve got a bit over budget. Secondly today’s news from Sandwich reminds us that pharma employees also get abandoned.

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16. hypnos on February 1, 2011 3:16 PM writes...

I would suggest that they focus on some third-world diseases instead of CNS. The fruits are hanging significantly lower, big pharma is staying out for obvious reasons and there is a lot of unmet medical need out there. Unfortunately, thats probably not gonna happen using US taxpayers money.

In general: To me, its not completely clear whether the commercial model is the right one for pharma. Thus, it might be useful to give the public one a try.

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17. hypnos on February 1, 2011 3:19 PM writes...

I would suggest that they focus on some third-world diseases instead of CNS. The fruits are hanging significantly lower, big pharma is staying out for obvious reasons and there is a lot of unmet medical need out there. Unfortunately, thats probably not gonna happen using US taxpayers money.

In general: To me, its not completely clear whether the commercial model is the right one for pharma. Thus, it might be useful to give the public one a try.

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18. CMCguy on February 1, 2011 3:37 PM writes...

I too wish them well, particularly if they can maintain a focus on under-served diseases and can possibly bridge some to the gaps between what is known and how to treat. I am concerned that this effort could dilute the continued success in basic research which is fundamental to NIH as represents a alteration of mission focus. Further complication is largely prompted by Congressional pressure who are mandating "more tangible" applied results, so appears reactionary in response. Even with experienced staff not clear if the atmosphere will be truly conducive or encompassing enough to this type of work where lacking direct development/and Clinical interactions the impact on quality of the "candidates" will suffer greater barriers to becoming an actual drug.

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19. SP on February 1, 2011 4:22 PM writes...

They are focusing on neglected diseases- I believe that TRND is being rolled into this center.

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20. anonymous on February 1, 2011 5:18 PM writes...

OK, I'll stay anonymous for this comment because I work at NIH. This announcement is, in my opinion, an embarrassment - not what they want to do, the wording of the announcement. As pointed out above, the comments on CNS drugs are absurd and inaccurate.

This is not NIH's first foray into drug development. NIH, through the National Cancer Institute's (NCI) Developmental Therapeutics Program (DTP) made significant contributions to drug discovery and development over the past 50 years. In fact, they played a major or a supporting role in the development of more than half of the available therapies for cancer, including many of the best known drugs. They do this in collaborations with academics, small companies and Big Pharma but rarely take public credit for their contributions. The most visible was probably taxol, NCI did most of the work, BMS claimed most of the credit and all of the market.

I'm amazed that F. Collins and his inner circle wouldn't acknowledge NCI DTP's extensive contributions to drug discovery as evidence that NIH could do the same in other therapeutic areas.

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21. Jose on February 1, 2011 5:43 PM writes...

Re: Neglected diseases.... 99% of the solutions for these have nothing what-so-ever to do with small molecules, new or otherwise (drug resistant TB being an exception). I've been on both sides of the pharma fence, and:

The solutions are health system strengthening, sanitation, vector control, better roads, etc. and throwing money at drugs that can never possibly make it to the end of a 40 km dirt road to the last village out there is just a criminal waste. It sounds like sexy and progressive research, but it simply isn't what's needed.

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22. pete on February 1, 2011 6:19 PM writes...

@ 20 anon at NIH
On top of all the concerns raised by you and others here, I also wonder how this will impact the size of budget slices available for existing research branches within NIH. Sounds like it will result in smaller pieces of the pie, or worse.

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23. anonymous on February 1, 2011 7:45 PM writes...

@ 22 pete
You asked a question that is on the minds of all of us at NIH. On the plus side, I hear on the grapevine that the new institute will be hiring more chemists. Rumor has it that they hired some big shot from Wyeth to head up the med chem efforts (MacKew? McKew? McQue? something like that).

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24. GreedyCynicalSelfInterested on February 1, 2011 11:07 PM writes...

If this center has the political sponsorship that Amtrak has, it will never run out of money. I'd get a job here if I was a chemist. They need to hire a good lobbyist or several dozen. Governments love loss-making enterprises or other places that practice value-destruction.

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25. Spiny Norman on February 1, 2011 11:08 PM writes...

Obviously, the real purpose of the new center is to identify therapeutic uses for resveratrol derivatives.

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26. CR on February 2, 2011 2:02 PM writes...

@Spiny Norman...
I think those wonderful ideas are best done by the only people that know how to do drug discovery - the pharma industry. Those government and academic types wouldn't be smart enough to jump on that - and be able to acquire it at such a cheap price.

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27. Sili on February 2, 2011 3:07 PM writes...

What's wrong with applying the best practices from pharma minus the restrictions of being responsible to shareholders, plus the ability to publish all the results without worrying about IP?
Because not being beholden to the shareholders is un-American.
This is something that should be cut to balance the budget. Stop wasting tax dollars.
Yeah, because this is certainly the main cause of the deficit.

Not that I don't agree that Collins is wastrel, but cutting this doesn't mean the money get directed somewhere more worthwhile - more likely they'll be poured in the Pentagon and TSA with the rest of your taxes.

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28. Disruptive on February 2, 2011 5:35 PM writes...

While the focus on genomics is fine, why exclude proteomics? The FNHI biosignature effort excluded proteomics. Depression biomarker grants go to genomics, inflammation markers, and BDNF and CSF markers, EEG and Imaging.

Solid basic research on blood based protein markers for depression diagnosis and treatment efficacy, are in universities now.

Pharma only wants compounds that are ready for trials. As one key Pharma said " we don't care about biomarkers in depression (unless they are companion diagnostics) and we don't care about antidepressant drugs. We have been burned too badly." Another gave a presentation at SfN and said they spent millions on duplicating a Phase II on efficacy of a new compound, repeating it 3x getting different results each time. So they canned it.

NIH focus is on bipolar and schizophrenia.

Why is Depression NOT a focus of NIH and Pharma?
WHO says it will be the second leading cause of disease worldwide by 2020 and is the leading cause of disability, premature morbidity and mortality in the US now affecting 21MM.This doesn't even include awareness of the serious issues with the military, PTSD, and suicide.And suicides in college students. Depression is the main cause of suicide.

All antidepressants on the market today are the result of serendipitous discoveries over 50 years ago. Only major improvement is in side effect profiles. While important, all of these still drugs work only about 30% of the time.

Depression is a global public health threat.
It is time for NIH and pharma to wake up and spend on the best available science now, not just genomics.

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29. Pharmtastic on February 2, 2011 5:46 PM writes...

Well the NIH is not setting up anything new, it is just piling up a bunch of already existing NIH programs under this new supposedly "Drug Discovery center" or NCATS. According to their website -

"For the most part, the budget and staff for each relocated program will remain with that program. Thus, the overall budget for NCATS will be the sum of the imported programs—an amount much smaller than the several billion dollars currently being spent on translational research by existing Institutes and Centers."

And the proposed budget is only about 900 million. So I don't think we need to really worry about them "throwing billions of dollars down the drain" again.

Pls do check out their clarification -

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30. Luysii on February 2, 2011 6:45 PM writes...

I'm far from sure that we know just what our drugs are doing, even when we think we do. For a totally unexpected mechanism of action of one of the tricyclic antidepressants - see

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31. Anonymous on February 3, 2011 1:53 PM writes...

The fundamental premise is wrong. The belief that government oversight to create a "pharmaceutical company for the people", not tainted by greedy capitalists, flies in the face of the free enterprise system that created the only industry in which thh U.S. is world-leading.

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32. lithobid on February 3, 2011 5:10 PM writes...

It's about time somebody decided to focus on bipolar disorder!

Although Li is the 'gold standard' it leaves a lot to be desired. Most bipolar patients end up on a cocktail arrived at through 'Rx roulette'. The atypical antipsychotics and some of the drugs used off label have awful side effects compared to potential benefits.

After anaphylaxis from two new drugs my shrink had me try (Seroquel and Cymbalta), we have reached an agreement to stick to drugs available as generics, since they've been around long enough that most of the side effects are well-known. (No offense intended to anyone.)

If this effort should come to pass, and an effective treatment for bipolar disorder comes to market, I would willingly give it a try, especially if the side effect profile is reasonable and I could ditch at least 2 of the 4 meds I currently use.

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33. Druceratops on February 4, 2011 5:59 PM writes...

@6 Calm Down - I would disagree about the "without worrying about IP". Certainly strong IP protection will go a long way in convincing investors/stakeholders that there will be a potential return on the capital required to perform late stage clinical evaluation of the product candidates. Given the relatively modest budgets being discussed for the center, it is clear that when the time comes for the big ticket studies, someone outside will need to pick up the tab and they will want the IP in place. Moreover, the center can't exactly ignore FTO issues either...

@13 SP - I am quite sure that if the government purchased or leased an existing facility to house their employees at fair market value from a private organization that no longer planned to use it there would be no outcry whatsoever. It happens all the time (for proof go to your local strip mall and see the military recruiting offices or visit the many federal satellite offices housed in privately owned space leased to the government).

@14 Aidan - Just to clarify, the Bioshield / BARDA program that you linked to is an NIH program not a DoD program. This is not to say that DoD has not had its share of issues along these lines.

While I do think that there are some important lessons from Bioshield that should be heeded, probably the closest existing analog for the New Drug Discovery Center would be the Vaccine Research Center at NIAID. In the latter case they focused developing candidates based primarily on a relatively novel, unproven approach (DNA vaccines) that had substantial theoretical upside. In the roughly 10 years of the VRC's existence they advanced candidates for two diseases (HIV and ebola marburg) into Phase II clinical testing and have candidates in a third disease are (influenza) in non-clinical testing. Time will tell whether this was a worthwhile finanical investment for the American taxpayer.

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34. David on September 10, 2011 10:59 PM writes...

It is childish to believe that one or two genes lead to a disease. Gene therapists could not get over this idea yet like the NIH.

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