Cancer Drug Targets: The March of the Lemmings

Posted in Biotech investment themes, Pharma industry

Just in time for the annual ASCO cancer circus, PhRMA released a new report listing the nearly 1000 projects in the industry’s pipeline for oncology – it’s an impressively long list against a whole range of cancers.  And this should be celebrated: we’re working on big problems and throwing lots of drug candidates, time, and money after solving them.

But the lemming behavior revealed by this list is frightening: a significant percentage of these programs are chasing the same targets.

We used a different database than the PhRMA report (Thomson Pipeline vs ADIS Insights) but count roughly the same number of active programs in oncology (990 vs ~981)*.  Of those, the concentration of clinical development effort around a handful of targets is staggering: 8 targets are addressed by >20% of the projects, each of which has more than 24 projects in clinical development.  Clinical projects that target VEGF lead the charge at an amazing 70 – and this only includes the one’s addressing oncology.  Here’s the stack below:

Does the industry really need 25+ clinical or commercial stage programs against each of these targets to exploit the full anti-cancer potential of those mechanisms?  Even more puzzling than the clinical development congestion on these targets, what about the huge numbers of preclinical projects addressing these targets (in red above)?  Some may be unique angles (e.g., receptor mutant-selective inhibitors that spare wildtype), but most are probably not.

A quick back of the envelope suggest there’s a ton of wasted industry resource across these programs.  Assume every clinical program has cumulatively spent $20M, and the preclinical ones at $5M (both conservative estimates), this implies well north of $5B+ in R&D dollars has been tossed at this set of programs over the past few years.

How many winners are likely to emerge from this?  Maybe a small handful per target, at most.  That implies lots of zombie programs being funded by budgets and investors that will never be of value.  This is of course always the case in R&D: programs more often than not fail.  But the concentration of industry activity on these privileged targets feels way outside the norm, and in aggregate represents a lot of wasted energy.  Beyond money and time, it also is a waste for patients.  Clinical trial recruitment is hard enough for exciting programs, but doing work on all these unlikely-to-matter programs on crowded targets seems borderline unethical frankly.

All that said, there is some merit to the principle that we should aggressively attack mechanisms that work in order to fully exploit them.  The arguments for this type of pipeline/program concentration are that: (a) smarter follow-on molecules may dial out some of the liabilities of the pioneer molecules through better selectivity, pharmacokinetics, etc… that make for better patient outcomes (after all, Lipitor was 5th to market after all, Humira was 3rd, etc…) – and this may be particularly relevant in unique “mixed” or dirty cancer agents; (b) different chemotypes could be terminated for tox liabilities so its good to have multiple shots on goal for high value targets; (c) different chemotypes will lead to differential responses by different patients for genetic/epigenetic reasons – and so personalized medicine requires a bigger arsenal of programs.  And much of the above logic is probably true to an extent.  But do they warrant, for instance, having 29 clinical and 31 preclinical programs against EGFR, many years after Tarceva and Erbitux were approved?

The real reason for this concentration isn’t about the arguments above – it’s fundamentally a reflection of our industry’s collective risk avoidance, as well as a misperception of aggregate risk.   

Portfolio decision-making in large and small companies leads to an overwhelming bias towards precedented mechanisms as a means to reduce biologic risk.  No head of discovery ever got fired for producing too many Development Candidates, and the lowest risk way of doing that is through “fast follower” (and even slow “fast follower”) incremental improvements.  In the shot on goal mentality of R&D, more of these shots are better.  Most R&D portfolio prioritizations punish novel target programs as low “confidence in mechanism”, and therefore riskier than precedented targets.  The math from these models is hard to challenge, having made some of those models in a prior life.

Sadly, the same biology risk avoidance holds for many venture capital investment decisions (“this is a risky target if no one else is working on it”…  “we don’t do drug discovery unless its close to IND”).  There’s a reason only a few VC firms do early stage innovation and venture creation like we do – many investors myopically focus on biology risk when other risk drivers are equally if not more important (which I’ve written on here).

In the end, all this leads to an industry pipeline – big and small companies alike – full of groupthink programs that follow the “hot” target trends like lemmings.

Beyond just the biology, I’d bet the industry pipeline’s chemistry concentration on these privileged targets is also high.  With compound structures from the patent literature, simple analoguing strategies and scaffold hopping approaches can provide for a patentable chemistry around even widely-mined chemotypes.  There’s a reason most kinase inhibitors are derivatives of only a handful of scaffolds.  These chemistries are also perceived to be lower risk (“this series has been in the clinic” etc…), and maybe they are.  But they don’t provide a lot of room for novel discoveries.

But while biologic and chemical risk is often lower for projects in these crowded classes, the differentiation risks skyrocket - including the downstream Phase 3 development risk (e.g., active comparator in your drug class; refractory patients), regulatory risks (e.g., higher bar for approval with other approved agents ahead), reimbursement risks (e.g., why should payors pay for your drug), and marketing risks (e.g., how do you get share of voice).  How does one differentiate the 10th PI3K inhibitor to enter its Phase 2a program?  Very challenging.  Furthermore, if small biotechs are hoping to be acquired by Big Pharma, being in the first wave of innovative projects against a novel target is important – or certainly facilitates earlier interest.  If a biotech has to do a Phase 3 program to show differentiation before it gets acquired, hope they have deep pockets.  I can think of a few small cap examples of this today.  And, lastly, the returns from spending all this may not be there in oncology especially: at what point does society stop paying $50-100K for a “doubling of survival” that adds only 3 more months of life?   For all these reasons, the next decade will not be kind to incremental innovations against well-known, well-drugged targets, and the companies that have them.    

Importantly, I’m not advocating for big programs against totally unvalidated targets that pop out of the Human Genome (the “Fruits of Genomics” described over a decade ago).  That would be a huge waste of time and money.  But the risks can be mitigated around novel first-in-class targets through many “confidence” building approaches and the tight titration of capital into them over time: (a) early validation of an intervention’s effectiveness in the best available animal models of disease (not predictive, but better than nothing); (b) identify the possible linkages to human genetic variation and if nature has validated the target already; (c) understand if pharmacology can phenocopy the transgenic knock-out or knock-down models; (d) show that multiple chemical series achieve the same outcome in preclinical models; (e) create translational strategies with appropriate PD markers of target engagement to bridge from animals to the clinic; and many, many other strategies.  None of these are a panacea for risk – but they do help strengthen the spine for making a commitment against novel biology to move forward.  Careful deployment of resources, and the weeding out of false positives with a fast-to-fail mentality, can help manage risk in these novel approaches (btw, its hard to fast-fail a precedented program because differentiation is largely untestable for oncology in preclinical models).  And while the biology risk may remain higher than for more established targets, the downstream risks around differentiation are clearly reduced. I suspect the aggregate “net present risk profile” of a preclinically-validated but not yet to human Proof-of-Concept program is probably far less than a similar stage inhibitor of a well known target like EGFR, PI3K, or VEGF today.

I’m also all for advancements in oncology.  Many cancers still have huge unmet medical needs that we should be aspiring to tackle.  But in the mid-1990s, oncology was a far smaller percentage than the ~40% or so of the pipeline it occupies today.  Is this the right allocation of resources?  What about all those other fields (like the contrarian ones I highlighted last week)?  It’s worth questioning at R&D strategy meetings around the industry.

When we see this kind of cancer pipeline concentration, its certainly hard to argue that we as a sector don’t need to make smarter bets about what diseases, what targets, and what approaches we put our scarce industry R&D capital into – both in Big Pharma/Big Biotech (90% of the spending) and in smaller biotech (90% of the companies).

We need to stop being target lemmings, or our group-think and risk avoidance will run our industry off a cliff.

* Analysis thanks to Michael Gladstone at Atlas Venture

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  • yeastbeast

    Nice analysis, Bruce. There certainly does seem to be a surfeit of new preclinical programs for some of these targets, particularly mTOR and PI3Ks. But as we have seen recently with ridaforolimus, the risk-benefit profile of these targets is far from certain.

  • http://twitter.com/MartinEglitis Martin Eglitis

    This confirms my concern that the biotech/VC industry is providing big pharma exactly what it is asking for. And big pharma isn’t asking for true innovation. It reminds me of a conversation I had at last year’s BIO, where a small company executive related a meeting he had with a big pharma. The big pharma guy said they were seeking “Innovative pre-clinical programs targeting novel mechanisms with clinical proof of principle.” Say what? Since this small company was looking at a new MoA with no clinical data, the big pharma walked. No wonder there are 150 VEGF programs…

  • http://www.biovista.com/ Aris Persidis

    It seems that groupthink is the only way where the risk of doing nothing new is less than the risk of fighting gravity, and thus it wins.

  • http://twitter.com/BusinessSnippet BusinessSnippet

    ‘Sheep’ behaviour is often a pretty good strategy for advancing one’s career in most professions.  That is true for big pharma and for investors in general.  Collective sheep behaviour becomes ‘lemming’ behaviour in some situations, as you have observed.  It’s part of what we are as a species and difficult to change.

  • http://twitter.com/JPZaragoza1 Juan P. Serrate, DVM

    Bruce, could you post some ideas about new innovative targets that should get more attention in your opinion? Thank you.

  • Sbwoodward

    You state that 20% of the projects in oncology target the same 8 compounds. If that leaves 80% focusing on other compounds, then the one could argue against the lemming proposal—i.e. a huge amount of risk taking is going on wouldn’t you say? I would be curious how that 80% is broken up. That withstanding, having at least 24 projects in each of those compounds is pretty significant.

  • David de Graaf

    This argues for proof of concept molecules that are developed quickly and potentially have liabilities that make them less than drug-like, but may be readily available or easily developable to derisk a particular target. Once derisked, the next set of molecules can be focused on idealized molecular properties, or – in case the target does not pan out – never be developed. You can even start the development of the optimized molecules at the same time as the efficacy probe. You would drive your economics from the savings for targets that do not validate.

  • http://twitter.com/liftstream Liftstream

    Back in April, Bruce wrote a great article on the culture of ‘risk’ (or the lack of), in the pharma R&D models. This article again frames the herding mentality that pervades our industry and he has once again provided an insightful analysis.
    There is also a talent discussion which relates to this. Clearly the more concentrated an industry becomes around one aspect of R&D and innovation, the shorter the supply of truly world-class expertise to drive the innovation. This is particularly true in an industry like pharma, which relies so much on theraeputic experience in drug discovery and clinical development.

  • slyrus

    It would be interesting to see these numbers weighted by how much money is actually being spent on them. Sure, there are lots of zombie projects on that list, but are they really still being funded? The not-really-possible-to-measure/gather data I’d like to see are amounts (per program) 1) invested to date, 2) spent in the last year and 3) committed to future development.

  • Smerchant40k

    My name is Sohail Merchant.  I am a student at Florida State University.  We just won a competition at FSU, and its for a business proposal I wrote on a bio”widget” for Drug Discovery.  Anyone know anything about miniaturization for throughput?  I suggest correction at our throughput order.  I think that is where real results come from.

    http://www.fsu.edu/news/2012/04/16/science.innolevation/ 

  • Joshua Anderson

    Even more shocking, is that each and
    every one of these eight molecules is a tyrosine kinase or tyrosine kinase
    receptor! Not only are these eight targets presumably garnering over 20% of the
    funding, they all belong to the same class of molecules! From this graph, there are over 250 programs
    currently targeting tyrosine kinases and tyrosine kinase receptors, and this
    doesn’t even include several other tyrosine kinases that I’m sure are also
    being studied! All of this is happening after several tyrosine kinase
    inhibitors have already been approved for many types of cancers, and while
    different types of cancers respond differently to various drugs necessitating
    several treatment options, 250+ therapies all targeting the same class of
    molecules is excessive. In addition, when current tyrosine kinase inhibitors
    prove ineffective in a patient, the doctor needs to find a second-line
    treatment that does not fall into the same class of molecules. All the more
    reason why researchers, venture capital, and big pharma should all be trying to
    buck the trend and find new classes of anti-cancer therapies!

    Nice post! I just thought I’d add my
    2 cents to the mix when I saw that the targets on the list all fell into the
    same class of molecules.

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