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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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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

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July 14, 2014

How to Run a Drug Project: Are There Any Rules at All?

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Posted by Derek

Here's an article from David Shayvitz at Forbes whose title says it all: "Should a Drug Discovery Team Ever Throw in the Towel?" The easy answer to that is "Sure". The hard part, naturally, is figuring out when.

You don’t have to be an expensive management consultant to realize that it would be helpful for the industry to kill doomed projects sooner (though all have said it).

There’s just the prickly little problem of figuring out how to do this. While it’s easy to point to expensive failures and criticize organizations for not pulling the plug sooner, it’s also true that just about every successful drug faced some legitimate existential crisis along the way — at some point during its development , there was a plausible reason to kill the program, and someone had to fight like hell to keep it going.

The question at the heart of the industry’s productivity struggles is the extent to which it’s even possible to pick the winners (or the losers), and figuring out better ways of managing this risk.

He goes on to contrast two approaches to this: one where you have a small company, focused on one thing, with the idea being that the experienced people involved will (A) be very motivated to find ways to get things to work, and (B) motivated to do something else if the writing ever does show up on the wall. The people doing the work should make the call. The other approach is to divide that up: you set things up with a project team whose mandate is to keep going, one way or another, dealing with all obstacles as best they can. Above them is a management team whose job it is to stay a bit distant from the trenches, and be ready to make the call of whether the project is still viable or not.

As Shayvitz goes on to say, quite correctly, both of these approaches can work, and both of them can run off the rails. In my view, the context of each drug discovery effort is so variable that it's probably impossible to say if one of these is truly better than the other. The people involved are a big part of that variability, too, and that makes generalizing very risky.

The big risk (in my experience) with having execution and decision-making in the same hands is that projects will run on for too long. You can always come up with more analogs to try, more experiments to run, more last-ditch efforts to take a crack it. Coming up with those things is, I think, better than not coming up with them, because (as Shayvitz mentions) it's hard to think of a successful drug that hasn't come close to dying at least once during its development. Give up too easily, and nothing will ever work at all.

But it's a painful fact that not every project can work, no matter how gritty and determined the team. We're heading out into the unknown with these drug candidates, and we find out things that we didn't know were there to be found out. Sometimes there really is no way to get the selectivity you need with the compound series you've chosen - heck, sometimes there's no way to get it with any compound series you could possibly choose, although that takes a long time to become obvious. Sometimes the whole idea behind the project is flawed from the start: blocking Kinase X will not, in fact, alter the course of Disease Y. It just won't. The hypothesis was wrong. An execute-at-all-costs team will shrug off these fatal problems, or attempt to shrug them off, for as long as you give them money.

But there's another danger waiting when you split off the executive decision-makers. If those folks get too removed from the project (or projects) then their ability to make good decisions is impaired. Just as you can have a warped perspective when you're right on top of the problems, you can have one when you're far away from them, too. It's tempting to thing that Distance = Clarity, but that's not a linear function, by any means. A little distance can certainly give you a lot of perspective, but if you keep moving out, things can start fuzzing back up again without anyone realizing what's going on.

That's true even if the managers are getting reasonably accurate reports, and we all know that that's not always the case in the real world. In many large organizations, there's a Big Monthly Meeting of some sort (or at some other regular time point) where projects are supposed to be reviewed by just those decision makers. These meetings are subject to terrible infections of Dog-And-Pony-itis. People get up to the front of the room and they tell everyone how great things are going. They minimize the flaws and paper over the mistakes. It's human nature. Anyone inclined to give a more accurate picture has a chance to see how that's going to look, when all the other projects are going Just Fine and everyone's Meeting Their Goals like it says on the form. Over time (and it may not take much time at all), the meeting floats away into its own bubble of altered reality. Managers who realize this can try to counteract it by going directly to the person running the project team in the labs, closing the office door, and asking for a verbal update on how things are really going, but sometimes people are so out of it that they mistake how things are going at the Big Monthly Meeting for what's really happening.

So yes indeed, you can (as is so often the case) screw things up in both directions. That's what makes it so hard to law down the law about how to run a drug discovery project: there are several ways to succeed, and the ways to mess them up are beyond counting. My own bias? I prefer the small-company back-to-the-wall approach, of being ready to swerve hard and try anything to make a project work. But I'd only recommend applying that to projects with a big potential payoff - it seems silly to do that sort of thing for anything less. And I'd recommend having a few people watching the process, but from as close as they can get without being quite of the project team themselves. Just enough to have some objectivity. Simple, eh? Getting this all balanced out is the hard part. Well, actually, the science is the hard part, but this is the hard part that we can actually do something about.

Comments (14) + TrackBacks (0) | Category: Drug Development | Drug Industry History | Life in the Drug Labs


COMMENTS

1. bhip on July 14, 2014 8:47 AM writes...

A couple of thoughts re: improving discovery & development processes.
1- Decrease the value of clinical candidate numbers to the drug discovery organization (re: bonuses, impact on career trajectories) while increasing the value of the candidates surviving through Ph2. This will cut down on the lily gilding that rewards progressing weak compounds into the expensive development path.
2- Have an independent Due Diligence division within the company to kick the tires of discovery/development efforts with the same diligence that is used to evaluate external opportunities.

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2. biotechbaumer on July 14, 2014 9:29 AM writes...

Agree with @bhip on both accounts although point #1 is theoretically sound, it is difficult to implement in practice with long time-lines for Ph2 readouts and trying to value 'soft' metrics as incentives for scientists.

Point #2 is also interesting and I imagine somewhat similar to what GSK did with its DPUs and essentially giving project teams, three year BD-like option agreements.

I believe having very clear Go-No-Go decision points is imperative and think that projects can linger for a long time when these GnGs are not clearly defined and/or constantly re-jigged to pushback timelines --- something that is inherent for project teams with an 'at all-cost' mentality. Resources are not unlimited so portfolio management is key but with good execution to extract high quality data, coupled with stringent GnG decision points, I believe PTLs are well equipped to make sound, scientific decisions.

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3. CMCguy on July 14, 2014 9:35 AM writes...

Excellent post on the balancing act for Go/No Go decisions drug R&D projects face and correct that its the science can be more readily tackled in many cases. However you do state "But I'd only recommend applying that to projects with a big potential payoff - it seems silly to do that sort of thing for anything less." Of all the variables and unknowns in the equations the Marketing analyses often seem the less robust therefore can be mislead by the "potential" in both directions and still may never know till very late in the investment cycle whether drug will ever be a commercial success.

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4. Anon on July 14, 2014 9:57 AM writes...

@1 I agree with your second point. Internal (and only internal) due diligence groups should be able to kick the tires, but not be given so much power that it gets out of hand. These groups should already exist in large organizations as part of the M&A activities they've become so dependent on.

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5. John Spevacek on July 14, 2014 10:17 AM writes...

I was once able to kill a program completely. Everyone agreed that I was right and it should die. Best of all, it stayed dead.

http://www.rheothing.com/2011/02/how-to-kill-project.html

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6. Chrispy on July 14, 2014 11:03 AM writes...

The first thing you need to do is uncouple the fate of programs from the fate of those running them. And this should cut both ways: no bonuses based upon hitting straw-man goals like number of compounds made or number advanced into Phase I. In fact, dismantle bonuses altogether: they incentivize the wrong things (like gaming the system).

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7. Dr. Manhattan on July 14, 2014 1:55 PM writes...

Having been on a team that pretty much exhausted all options, we put together a presentation & document to end the program. Fine. But, there was push back from management and mutterings that we "had failed" since we did not progress to the next stage. I suspect this happens quite often, and is another unspoken reason why teams soldier on long past the point where they know themselves that it is pointless.

Postscript: In our case, it took another 16 years by another company until a compound emerged in the class we were working on, and it was a topical rather than an oral which was our mandate.

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8. WizardOfBoz on July 14, 2014 2:37 PM writes...

Its interesting that no one addresses the real issue: Often neither the program team nor the management team have a clue whether to kill or not kill the program. Quick: does that lack of a green flash in the 28th well of a 96 well plate tell us that we'll see 12 months of progression-free survival in our trial? Or, our dog tox results came back and there were no issues in the range of plasma concentrations and mg/kg dosing we are contemplating in humans. Do we green-light trials? Or, our Alzheimer drug showed a faint signal in Ph I testing. Do we say "what the hell?" and put it into Ph 3, merely because we got nothin' else?

Having helped used appropriate science to kill several different targets, I can say that sometimes neither the scientists with five year's commitment, nor the VP whose bonus or job may depend upon keeping a program going are real enthusiastic about killing a program. So incentive matters, too. Dr. Manhattan's experience is, I think, all too common.

As far as "skin in the game", is the VP's bonus "skin". Is the researcher who wants to work another 14 months and then retire, but who will be laid off if the program is killed. Will she be enthusiastic about an early kill?

Rich Heaslip (then at Wyeth - VP of Portfolio Mgmt) once asked a question. He gave a scenario of a promising program, then mentioned that there was a hint of hepatoxicity. More specifics were there, but the question he asked the audience was "Do you kill the project?". The audience was silent, then someone said quietly "It depends". Exactly! And it shouldn't!

The problem is that there is enough ambiguity in traditional methods of analyzing data that the deciders can pretty much decide whatever they want. And it's no surprise then that our batting average at every level is low.

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9. Barry on July 14, 2014 9:47 PM writes...

This is not separable from the science. Science is about falsifying hypotheses. What can't be falsified may be the truth. We go into drug discovery with the hypothesis that modulating (usually blocking) this enzyme/channel/receptor/protein-protein interaction will change the course of a disease (in a profitable way). If we are not working towards falsifying that hypothesis, we may be doing engineering, but we're not doing science. If it can't be falsified any other way, then we take it through Clinicals and to market.

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10. Anonymous on July 15, 2014 4:55 AM writes...

The biggest problem is that we worry too much about false negatives (killing a project that could ultimately succeed) and not enough about false positives (advancing projects which could never succeed). The latter are way more costly but take more balls to deal with.

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11. Anonymous on July 15, 2014 5:00 AM writes...

^ Or the other way round, but you know what I mean...

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12. P.K. Peedee on July 15, 2014 8:07 AM writes...

A well-planned, written scope of work at the beginning of the project is very helpful. It's rare to let a CRO get away with changing contract terms as a project proceeds, why not hold drug discovery and development teams to the same standards?

Laying out up-front go-no-go decision points with quantifiable endpoints, then sticking to them is often enough to encourage good kill decisions well before GLP tox. Do you understand target distribution and dynamics? Does your compound have sufficient binding and ADME properties to get to, bind, and modulate the target? If the answer is no to any of these, either go back and make it a yes, or bring on the coup de grace.

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13. biotechie on July 15, 2014 11:17 AM writes...

Going back to the conceptual issue of how to make a no-go decision, perhaps a better solution is a hybrid? Get everybody working on different drug discovery teams so that they remain close to/informed about the challenges of the bench and clinical science, but don't give them go-no-go decisions on their own projects; just give them that right on other teams' projects. Thus, team A gets to make a decision on whether team B's project goes forward, and team B on whether team A's project goes forward. That way, the people making killing decisions are close enough to the work to understand the problems, but they do not have so much investment in a project that they resist clear signals it should be killed. Obviously this is much more applicable to a small team than a larger company

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14. Cassandra on July 23, 2014 1:26 PM writes...

@13, your recommendation might work in an unfallen world and/or one in which teams A and B truly are motivated by the science and only the science. In a postlapsarian organization where people must SAY all reasons are scientific, but where other agendas may occur under the surface, there would seem to be opportunity in your approach for company politics to grow TEETH.

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