Phil Needleman's Ten Commandments of Drug R&D - LifeSciVCLifeSciVC

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Phil Needleman’s Ten Commandments of Drug R&D

Posted March 27th, 2013<br>in Biotech startup advice, Pharma industry, Translational research

Pharmaceutical R&D is a very low velocity, high cost process, which makes it hard for any individual to gather the large body of experience required to inform better decision-making.  This is why pharma’s embedded institutional knowledge should be the source of considerable intangible value: most great drugs spend years working their way through complex Gannt charts, with lots of bumps, bruises, and causalities along the way, often under several regimes of R&D leadership.  There are tons of lessons to be had through the thoughtful mining of this knowledge base.

While I’m sure there’s real value in a big analytics approach to this, I also think there’s a lot to be gained through the appreciation of some simple truisms accumulated by the truly seasoned practitioners of drug R&D.  One of those practitioners is Dr Phillip Needleman.

Phil was the Chief Scientist of Pharmacia when it merged with Pfizer, and before that held the same role at Searle, and before that Monsanto; he’s overseen a bunch of great drug programs, including COX2.  He’s also a National Academy of Sciences and Institute of Medicine member, an accomplished scientist at heart.  I’ve had the pleasure over the past three years of getting to know Phil though our role together on UCB Pharma’s Scientific Advisory Board.

Never one to shy away from sharing his candid feedback about R&D programs, his impressive catalogue of experience gives him a unique perspective.  I don’t always agree with him, nor do others, but his opinions are always grounded in a thoughtfully data-driven, experience-based rationale.  In talking with him last week, he shared his “ten commandments or ten platitudes” with me – and I thought they were worth sharing more generally, as many are still as relevant to Pharma R&D today as they were a decade ago when Phil (in theory) retired and distilled this list.

“There’s only one Nobel prize…” and industry researchers aren’t likely to get it.  While great science is an important foundation, the true strength of pharmaceutical industry is in the inventions required in generating clinical proof of concept (PoC) and development of new products.  Those tend not to be what Nobel’s are about, but then again Nobel’s don’t help treat patients.

“Phenomenology is very different than pharmacology”.  Phil’s admonition is to only take drugs into patients where you know the mechanism of action and can therefore optimize the drug’s SAR rationally.  Phenotypic screens are fine as starting points, but be sure to deconvolute the mechanism before spending a ton of resources on it.  Pfizer’s “3-pillar analysis” earlier last year supports and extends this view (here), and we certainly share this view at Atlas.

“ Anything put on hold is dead".   Projects that get parked or slowed down dramatically in a resource-constrained world are very hard to revive.  If you don’t have the resources inside, and it’s a good program, find a partner on the outside to fund it – patients deserve it.

“Define and do the Killer experiments”.   This speaks for itself.  But, in Phil’s words, “you need ice in your veins – if a killer experiment doesn’t work then kill the program”.  This does take a lot of discipline, especially for a team that may have given its heart and soul to a project for 3-4 years in drug discovery.  Defining the right killer experiment is the key skill: too stringent could lead to a false negative, which kills good programs, and vice versa.

“If you don’t know where you are going, all roads will get you there”.  I’ve heard Phil use this quote from the Cheshire Cat in Alice in Wonderland, and its very true – strategic direction and very well-defined endpoints are critical to measuring success.  While lots of clinical studies don’t need to focus on registrational endpoints, like early experimental medicine PoC studies, that doesn’t mean having loose endpoints; have a clear sense in advance of what you are after in a project.

“Make sure it’s doable in my lifetime”.  If the PoC study or pivotal endpoints will take “many years without a convincing marker, surrogate, or a unique insight opportunity, then don’t bother trying to be patient”: go invest your time and energy someplace else until the field finds more realistic measures.

“Find the shortest route to heaven”.  In discovery, don’t spend years doing every preclinical pharmacology model – do a few, not half-a-dozen or more – and then with confidence sprint quickly to the drug’s PoC in patients.  In the clinic, if you need to focus on a limited-use first, go for it and get approved with a narrow label fast, even over the cries of your commercial colleagues.  Get to heaven and you can...