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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: Twitter: Dereklowe

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June 24, 2014

Taking Risks - You Have To, So Do It Right

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Posted by Derek

In case you hadn't seen it, I wanted to highlight this post by Michael Gilman over at LifeSciVC. He's talking about risk in biotech, and tying it to the processes of generating, refining, and testing hypotheses. "The hypothesis", he says, "is one of the greatest intellectual creations of our species", and he's giving it its due.

I agree with him that time spent rethinking your hypothesis is often time well spent, whether for a single bench experiment or (most especially for) a big clinical trial. You need to be sure that you're asking the right question, that you're setting it up to be answered (one way or another), and that you're going to be able to get the maximum amount of useful information when that answer comes in, be it a Yes or a No. Sometimes this setup is obvious, but by the time you get to clinical trial design, it can be very tricky indeed.

For drug discovery, Gilman say, there are generally three kinds of hypothesis:

Biological hypothesis. What buttons do we believe this molecule pushes in target cells and what happens when these buttons are pushed? What biological pathways respond?

Clinical hypothesis. When these pathways are impacted, why do we believe it will move the needle on parameters that matter to patients and physicians? How will this intervention normalize physiology or reverse pathology?

Commercial hypothesis. If the first two hypotheses are correct, why do we believe anyone will care? Why will patients, physicians, and payers want this drug? How do we expect it to stand out from the crowd?

Many are the programs that have come to grief because of some sort of mismatch between these three. Clinical trials have been run uselessly because the original drug candidate was poorly characterized. Ostensibly successful trials have come to nothing because they were set up to answer the wrong questions. And ostensibly successful drug candidates have died in the marketplace because nobody wanted them. These are very expensive mistakes, and some extra time spent staring out the window while thinking about how to avoid them could have come in handy.

Gilman goes on to make a number of other good points about managing risk - for example, any experiment that shoulders a 100% share of the risk needs to be done as cheaply as possible. I would add, as a corollary, ". . .and not one bit cheaper", because that's another way that you can mess things up. At all times, you have to have a realistic idea of where you are in the process and what you're taking on. If you can find a way to do the crucial experiment without risking too much time or money, that's excellent news. On the other end of the scale, if there's no other way to do it than to put a big part of the company down on the table, then you'd better be sure that getting the answer is going to be worth that much effort. If it is, then be sure to spend the money to do it right - you're not going to get a second shot that easily.

The article also shows how you want to manage such risks across a broader portfolio. You'd like, if possible, to have plenty of programs that are front-loaded with their major risks, the sorts of things that you're not necessarily going to have to hopping around the room with crossed fingers while you're waiting for the Phase III data. It's impossible to take all the risk out of a Phase III, true - but if you can get some of the big questions out of the way earlier, without having to go that far, so much the better. A portfolio made up of several gigantic multiyear money furnaces - say, Alzheimer's or rheumatoid arthritis - will be something else entirely.

Comments (10) + TrackBacks (0) | Category: Clinical Trials | Drug Development


1. Anon on June 24, 2014 1:15 PM writes...

As someone at 5 person virtual biotech I'm thinking about these three points at almost every decision I make in addition to IP and regulatory (maybe a little manufacturing).

With that said, I don't see how large companies are successful in this modern environment (wait a second...are they successful?) I especially don't understand how someone such as a lawyer by training can make it so high at these companies. They just don't have the background to be able to put the pieces together and consistently make good broad decisions.

Example: You are trying to get an approval and a FDA reviewer makes a comment about your LLOQ. You have to consider what method you can pull off (require some scientific background and knowing any issues you had establishing your prior LLOQ), you have to think about how this may alter your clinical data. Maybe going too low is unfavorable. Maybe your product gets erratic down low? Or maybe you know that a small change can help your AUC over 6 months. Got to have some business sense to figure the costing and the time it may take to do this (and place it in the context that you may or may not be trying to beat someone to market or are on a limited budget, but who isn't these days). You also have to place this in the context of going through this review process in the past and knowing what you can get away with (because the FDA won't TELL you what they want, but instead make a non-binding suggestion which hopefully "they" remember a year from now when the employees have changed). Or maybe you just need to spend time convincing that reviewer they should be looking at another metabolite instead.

This is completely off topic, but because of the the background needed to be successful there are actions talented people take that we never see. A successful leader will not simply pick the drug with the most check marks (data, market, ip protection, etc), but guided it through the cracks.

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2. Barry on June 24, 2014 1:27 PM writes...

At the center of Drug Discovery is Research, at the center of Research is Science, at the center of Science is Falsification. As drug discoverers, if we're not working towards an experiment that could falsify the hypothesis that "modulating the activity of this enzyme/receptor/porter/channel/gene will alleviate/cure this disease" we're not doing it right.

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3. Heteromeles on June 24, 2014 2:19 PM writes...

I see that the cartoon Non Sequitur was thinking about the same topic today:

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4. road on June 24, 2014 2:20 PM writes...

@2 Barry -- That's an interesting point, but a poor choice of words...

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5. Thomas on June 24, 2014 3:04 PM writes...

What I was wondering about: Intel and Cisco often have departments competing. Intel for th enext CPU design, and Cisco even has 2 or 3 offices in different continents designing for a bid or solution for a single customer.

Are the same methods used in pharma? I suppose trials could be central; they are the way to select 'the winner'. Or are projects too big and undefined, and selecting the 'winner' too difficult/expensive?

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6. Anonymous on June 24, 2014 4:13 PM writes...

@5: I'm not exactly sure what you are asking, but GSK tried to have "Centers of Excellence" compete against each other for funding, but that didn't work out too well for anybody.

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7. Anon on June 24, 2014 4:24 PM writes...

@6 Were those DPUs competing directly against others with the same target? I naively thought they were different.

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8. Boghog on June 24, 2014 4:25 PM writes...

@4 road -- I think a good point that perhaps could be stated more succinctly:

do the key experiment that could kill the project as early as possible

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9. Cellbio on June 24, 2014 8:32 PM writes...

I think it is much better to state the goal as to do the key experiments that clarify the initial proposition as early as possible. It does not sounds as neat and clean as killer experiment or go/no go, but many trial results land in the gray zone rather than black or white. The problem I see is that in these circumstances it is common for decision makers to hold to original concepts and struggle with a black and white decision, it worked or it did not work, when certain things are abundantly clear but not acknowledged. For instance, the commercial hypothesis may have had assumptions about product performance, convenience or market breadth, that are shot even though the clinical hypothesis remains viable when a segment of the population responds or most do but for a duration short of convenient dosing modeled for a compelling product profile. Instead of re-examining the value proposition, it is common to claim partial victory and then back up to take another run at the brick wall while holding firmly to original aspirations. Walking away from stone cold failure is easy, invoking killer experiments sounds clean, but it gets real messy when early studies produce in-betweens with low power studies, especially for start-ups lacking the luxury of multiple Ph1s to nail dose, schedule and population questions.

Getting there quick for value inflection and limits of cash means making a lot of best guesses. I left big pharma for start-up land but see the pros and cons of both sides. In bigco, we'd measure twice and cut never. In smallco, we leave a lot unmeasured and cut enthusiastically. Utopiagen lies somewhere in the middle.

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10. cliffintokyo on June 30, 2014 11:03 AM writes...

This is an excellent post which really helps sharpen the focus of our thoughts.
One small quibble: Could we use "marketing concept" and keep "hypothesis" for scientifically based extrapolating?
I know that my objection destroys the easy to remember paradigm (KIS), but I dislike the implication by association that there might be something scientific about marketing. Perhaps I am being snobbish though?

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