What If You Can’t Pick Winners in R&D? 

Peter Thiel, the contrarian investor, had a favorite question for interviewees: “What important truth do few people agree with you on?”

My answer: No one can pick winners in pharma R&D. 

When I think of the most significant blockbusters in the industry involving novel mechanisms of action (follow-ons are a different story), I see a huge amount of luck on the exploration side, followed by exceptional focus on subsequent exploitation.

Pembrolizumab (Keytruda), Merck’s oncology blockbuster is one example (see here).  Millennium’s (later Takeda’s) bortezomib (Velcade) is another (here).  The GLP-1 medicines developed by Lilly and Novo and achieving stratospheric sales for the treatment of obesity are additional examples (see here, here). 

While the researchers leading the initial development of each of these medicines were passionate about the program’s prospects, each medicine had to overcome profound skepticism within a large pharma before it was eventually embraced and exalted. When Merck acquired Schering-Plough (and when Schering-Plough acquired Organon before that), the acquiring company had no idea a future blockbuster was lurking in its portfolio. Similarly, when Millennium acquired Leukosite, no value was attributed to the bortezomib program. 

In the case of Lilly and Novo, their work on incretins like GLP-1 represented an outgrowth of the longstanding interest in and involvement with diabetes in general, including the biology of insulin secretion (modulated by incretins). While early rodent studies of GLP-1 demonstrated an impact on appetite, diabetes — not obesity — was the initial focus.

When a leading incretin expert, Dr. Daniel Drucker, reviewed the field in 2017 – three years after the first GLP-1 was approved for obesity – he lamented the “market penetration” and worried about the “clinical appeal, expense, and commercial success of newer formulations” (see here).  While his concerns about expense were on target, these medicines have emerged as outsized successes, both clinically and commercially.   

The point is that while all these companies were transformed by those successful products, no one in R&D leadership at these companies saw this coming far in advance or had shaped their R&D strategies around the anticipation of such extraordinary results. 

What each company did do successfully was (eventually) recognize the promise of the medicine and work intensively to realize this potential.

The difficulty of replicating R&D success

One measure of the role of luck in R&D success is how difficult success is to replicate – how hard it is for companies to find their next blockbuster. 

My experiences suggest that in many ways, success makes finding the next blockbuster harder, because companies invariably develop a tidy narrative around the success – a comforting series of “lessons learned” (it was our culture, it was our focus on biomarkers, it was our clinical operations, etc), and then seek to impose these learnings on future company efforts. 

Yet if we’re in a domain where luck plays a critical role in determining success (spoiler alert: we are), then (as discussed here) you need to be really cautious about assuming that the occasional success represents the manifestation of your exceptional skill, rather than involving a combination of real skill coupled with a hefty amount of luck.  As Pixar’s Ed Catmull emphasizes, there isn’t a playbook (big pharma’s go-to crutch) for creative success like an original film (or, I’d add, an innovative drug) – you need to reinvent the approach each time.

There’s also an unfortunate tendency to fall prey to “selecting on the dependent variable,” as Cass Sunstein nicely explains in How To Become Famous (see here).  This approach, so familiar in companies and among the management consultants who advise them, involves looking at a set of successful companies/products/leaders and then trying to pull out what they have in common, and then concocting a compelling narrative around this.  Yet without knowing, rigorously, if these same traits are present among the many failures, you’re just coming up with a good story, with little actual validity or predictive value.

Are dart-throwing chimps the answer?

What is to be done?  Should the head of R&D at Lilly, Dan Skovronsky, acquire a trained chimp to throw darts at potential targets and programs, akin to the blindfolded monkey that economist Burton Malkiel famously asserted (in A Random Walk Down Wall Street) would pick stocks as well as expert investors?

At a fireside chat last Tuesday at Harvard Business School (where, disclosure, I serve as an advisor to the MS/MBA program in life sciences), I had an opportunity to see how Skovronsky viewed this exact challenge, as he responded to questions posed first by Professor Amitabh Chandra, then by members of the audience.

Refreshingly, Skovronsky emphasized the contingency of R&D, the role of chance, and the futility of commercial forecasts (a topic I’ve discussed frequently, see here, here, here).  He said (only half-jokingly) that the most important trait in a Chief Science Officer was being lucky.

He also emphasized that while some might urge Lilly to take its pile of GLP-1 cash and undertake either a transformative acquisition or acquire a derisked late-stage product, he wasn’t enthusiastic about either, noting that large M&A is profoundly disruptive, requiring massive corporate reorganizations which wasn’t his focus or interest.

Meanwhile, fully derisked products, he said, were typically acquired either by the company with the most excessive sales forecast (a concept referred to by economists as the “winner’s curse”) or by the company that is the most desperate.  Neither of these seemed like especially attractive prospects.

In contrast, Skovronsky suggested that a large pharma’s greatest strength is its ability to develop drugs, a notoriously complex task with which smaller organizations often struggle.

Interestingly, he suggested that because he was operating in an organization (and at a moment) where there was an uncommonly high tolerance for the inevitable failures, this represented a competitive advantage. 

Other pharmas, he suggested, might be less willing to invest in early, risky assets because leaders were worried about the career consequences if too many of these bets went south.

The notion of a large pharma arbitraging risk aversion (big if true…) seemed particularly interesting, and reminded me of PayPal’s ability to take advantage of large company risk aversion (specifically in the context of regulatory risk) to outmaneuver the combination of eBay plus Bank of America – see here.

Skovronsky also suggested that because of its location in Indianapolis, Lilly was somewhat protected from the latest hype cycles and had relatively more patience to pursue promising but difficult programs. 

Perhaps related, he also offered a decidedly reserved perspective on AI, allowing there was promise in assisting with molecule creation, but otherwise fairly guarded about the impact.

I hope Skovronsky’s approach succeeds, though it’s difficult not to look at Moderna as a concerning example. Moderna may have slipped silently into obscurity were it not for the opportunity afforded by COVID, an incredibly fortuitous (from the perspective of the company at least) event for which it was ideally positioned. 

Of course, the success narratives soon followed – it was their embrace of digital, or their adoption of AI, or their culture, that enabled them to be successful, and would surely pave the road for future success.  Betting on themselves, they invested significantly in R&D.

Unfortunately, these efforts, to date, haven’t panned out; their stock has been crushed by investors, and after much outcry from analysts, Moderna recently announced massive R&D cuts.  Mr. Market can be very unforgiving.

I hope this isn’t Lilly’s future, and I also hope that Moderna’s pipeline and approach yields future impactful medicines. But whether we should count on this happening is a more difficult question.

Contingent, but not Random

If, as I believe, there isn’t a leader of R&D on the planet who has a magical or uncanny ability to “pick winners,” how do you approach this role?  What role does good luck play?  Is it time to bring in the blindfolded chimp?

Before we answer this, we should come to terms with perhaps a second truth about R&D that can be difficult for those outside the process to appreciate: R&D programs are not discrete, static, or hermetic – it’s not like betting that a roulette wheel lands on “36.” 

Rather, drug development requires constant effort to perfect and refine a new medicine, at every stage of the process including in clinical trials, where the right patient population and dosage scheme could make the difference between a failed and successful product. 

The most significant challenge facing any head of R&D is balancing the recognition that, on the one hand, outsized success is generally impossible to predict in advance, and most projects involving novel mechanisms will fail.  On the other hand, for any project to have a chance at success, it must proceed with full and authentic conviction, with leaders absolutely convinced that there’s a path for success to be found.

Balancing these two is incredibly challenging, particularly the need to believe deeply in programs while somehow compartmentalizing enough to avoiding getting sucked entirely into the program’s narrative, and maintaining enough objectivity to make difficult, data-driven decisions (see also here).

Sometimes, as Skovronsky points out, the issue isn’t data but politics; as previously reported in the Wall Street Journal, he described how Lilly (and other pharmas) historically, would advance programs with shaky data because the program would fulfill an identified commercial need (a concern VC David Grainger has raised as well, as I’ve discussed here).

Since these ill-advised programs would generally fail in subsequent, more expensive later phase clinical studies, they are huge wastes of time and resources, and Skovronsky has worked aggressively to eliminate them.

But in many (arguably most) cases, it’s less clear whether a program is six months away from a breakthrough (as teams tend to argue) or six months away from just digging a deeper hole.  Management gurus will tell you that the ability to discern one from the other is the secret of great leaders. This is wishful thinking. 

Many top scientists, like famed Harvard surgeon-researcher Judah Folkman, acknowledge that when you’re in the midst of an impassioned pursuit, you have no way of knowing whether you are persistent or obstinate; that distinction is revealed only by the outcome. 

Given the need for R&D leaders to come to terms with the inherent uncertainty associated with their roles, they would do well to remove sterile information where possible. In a futile effort to domesticate uncertainty, many R&D organizations, especially when things seem to be going poorly, decide they will improve decision making by imposing stricter discipline, and start affixing all sorts of quantification (e.g. probability of technical success, estimated net present value [NPV]) across R&D. These tend to be falsely precise numbers that typically provide far more illusory comfort than true insight. 

I would love to see the NPVs that Merck associated with pembrolizumab when it acquired Schering-Plough, that Millenium associated with bortezomib when it acquired Leukosite, or that Novo and Lilly associated with obesity indications of GLP-1 programs during their early days (or even their not-so-early days, as the Drucker experience suggests).

Bottom Line

The fundamental challenge for R&D leaders is that while success is highly contingent, your only way to achieve it is through convicted pursuit, though such pursuit is not (at all) a guarantee of success. The ability to muster conviction in the face of inherent overwhelming uncertainty is the critical quality required for R&D leaders and others who seek to leave their mark on the world.