Two weeks ago, I wrote about how difficult it is for R&D leaders to “pick winners,” despite the enormous incentives to do so.  I explained how we tend to underestimate the role of chance, and overestimate our ability to “domesticate uncertainty,” as Nassim Taleb and I wrote in the Financial Times in 2008. 

Mostly, efforts to systematically improve success rates seem to have come up short.

However, as The Princess Bride (the font of all knowledge, as VC Lisa Suennen explains here) reminds us, “mostly” doesn’t mean “completely.” Occasionally, at least for a period of time, it may be possible to find an “edge” (a term Nate Silver discusses at length in his recent book).  In R&D, this would mean finding an approach, an insight, a team, an organizational structure that might be able to beat the odds consistently.

Earlier this week, I suggested that perhaps Vertex’s approach to human causal biology has provided them just such an edge.  As I emphasized, their secret sauce (if it exists) certainly isn’t the invocation of “human causal biology,” a phrase that, as BioCentury’s Karen Tkach Tuzman recently observed, “is on the lips of research heads and early-stage investors,” and seems to be associated with most every current R&D program.

I argued that Vertex (unlike many competitors) is taking this concept particularly seriously, using it as an ultra-stringent criteria for target and program selection. Unless they can find compelling evidence (usually but not invariably from human genetics) that a particular protein is associated with disease, and also that targeting it is likely to improve the disease, they’re just not interested. 

Vertex’s thesis is that most programs fail because they ultimately don’t generate adequate efficacy in people, and they hope to mitigate this by ensuring that they have a very high degree of confidence in their targets. 

There are obvious tradeoffs with this approach.

For one, they are deliberately not pursuing a range of compelling conditions because they don’t believe they have adequate human causal biology to support such an effort. 

Vertex also strives to remain agnostic about modality, often partnering with platform companies that presumably bring the requisite expertise. Their successful campaign to develop an effective (combination) therapy for most CF patients is a vivid reminder of just how difficult it can be to develop small molecule drugs; deploying emerging technologies is likely to contribute additional degrees of difficulty and uncertainty.

Readers Respond

I anticipated that my two recent pieces about R&D might generate some discussion around what is actually meant by “causal human biology,” and how might this term be defined most usefully if the goal is to increase the odds of successful therapeutic development. 

I also expected some discussion around how computational efforts to quantify causality (as reviewed by Tuzman in BioCentury) might contribute to improved decision-making in pharma, particularly in the context of Vertex’s conviction that what’s required is pivotal insights from human beings, rather than more reductionist approaches that seek to garner primary insight from volumes of data derived from human cell lines cultured in a dish.

I wasn’t surprised that these two articles engaged TR readers given our shared passion for R&D.  What I didn’t expect was the emphasis of the responses, both public (via social media, mostly on Bluesky, which seems to be the new home of BioTwitter) and privately. 

Virtually all of the feedback I received boiled down to: in practice, Vertex isn’t doing anything different than what others are; they do solid science, and perhaps have been a bit lucky, so be careful not to be taken in by a tidy success narrative.

One Bluesky user wrote,

Say you have 200 small/med pharma companies, with 2-10 projects each.  I think just random statistics, if you look over say one 10-year window you would expect one company to have a high success rate and that company would be lauded as highly superior.

Experienced drug hunter Jonathan Rosenblum suggested there was nothing distinctive about how Vertex pursued their sodium channel pain target vs how other companies approached this target, adding,

What I know of their process is – it’s not unique. They haven’t cracked some code that others haven’t. An excellent, science-driven company nonetheless.

Industry veteran and advisor Frank S. David added,

In past 10y I’ve seen *nothing* unique about any pharma co’s R&D decision-making process.  Maybe there were differences in past, but now, they’re all cousins of AZ’s 5Rs….Stories of “better” cos are post hoc rationalizations.  (Note: the “5R” reference is to this paper and subsequent elaboration.)

In addition to noting the concerns about how Vertex’s approach deliberately overlooks important conditions, and is likely to increase risk in some areas (like new modalities) while decreasing risk in others, Frank David makes another, critically important observation:

Interesting to try to predict how much of VRTX R&D decision making is hard wired into co vs dependent on judgement of top execs. I bet a lot of it is the latter. (Ditto Regeneron.) So maybe the lesson for pharma is “hire R&D execs w/ good taste & give them tons of power”? (Good luck with that…)

In other words: perhaps Vertex is a company at the sweet spot with enough resources to try a range of ambitious programs, but small enough so that it’s still guided palpably by strong, smart scientific leadership.

The private feedback I received was essentially a collective eyeroll, as readers emphasized that virtually all biopharma R&D organizations seem to be preaching from the same hymnal, and assert they are pursuing a similar strategy. 

Apparently, it’s only a matter of time before inspirational “Human Causal Biology” posters, suitable for display in your company’s cafeteria, will be available for sale from Successories.

Three Possible Conclusions

Putting it all together, I can see three potential conclusions:

1. Vertex has perhaps been lucky, but actually doesn’t have any durable secret sauce, and has managed to persuade some particularly susceptible investors and colleagues to believe their success narrative. In this view, the confidence exhibited by Vertex leaders today may be similar to that expressed by Pfizer execs in 2018 when they projected 15 blockbusters by 2022 (a pipe dream, as activist investor Starboard has recently highlighted).
2. Vertex is actually doing something different and better, than most, but the “human causal biology” is just the MacGuffin – essentially a plot device to bring together an unusually focused and capable team of physicians and scientist in an productive organizational structure, and with individual leaders capable of delivering unusually good results.
3. Vertex is actually doing something different and better than most, their organizational structure is important, but really it’s their stringent embrace of human causal biology that’s enabling them to have justifiably high confidence in the programs they advance.

And The Answer Is…

In trying to sort this out, it seems relevant to acknowledge several of my own biases. 

I am incredibly partial to compelling science and compelling scientists. I also love the idea of biopharma companies led by science and scientists, rather than managers and metrics. I’ve found it incredibly sad to watch the status of R&D leaders within big pharmas decline over the course of my career, as their inevitable struggles to generate the next blockbuster (and the one after that) has often left them on the defensive, enmeshed with operational efficiency, process metrics and the latest re-org rather than delivering great science.

I’m also especially partial to the power of genetics (which I was drawn to and pursued in graduate school), and to the unique understanding that the study of the whole person provides (see here). When I joined DNAnexus as chief medical officer in 2014, I was motivated, in part, by the knowledge that DNAnexus had worked closely with Regeneron to develop the Regeneron Genetics Center, as I had always admired Regeneron’s George Yancopoulos (see here) and was an enthusiastic supporter of the Center’s ambition to integrate genetics and medical record data to guide scientific discovery. 

In short, I am exquisitely set-up to buy into Vertex’s success narrative, and perhaps this is exactly what’s happening. 

But if it’s true that really no R&D approach is better than any other, and it really is just throwing darts at the genome, then trying not to mess up the execution…I guess this is just a worldview I find myself unable to accept. 

To make a difference, we need to find conviction around something, and I deeply believe we can leverage human causal biology to improve R&D.

I am also probably more optimistic about the opportunities to leverage powerful emerging technologies including AI than current Vertex leadership, although I share Vertex R&D head David Altshuler’s wariness about technology-first approaches.

In addition, I have seen how important organizational context and culture is for R&D.  While nearly all big pharmas describe themselves as science-led, this often isn’t the lived reality. Even at large companies with the best R&D intentions, earnest ambitions tend to dissolve rapidly in a miasma of metrics, process, and power politics.   

In contrast, mid-size companies (as I argued back in 2012, see here) with strong scientific leadership may well be the sweet spot for R&D, as exemplified most recently by Regeneron, Vertex, and Gilead while helmed by chemist John Martin.

Bottom Line: What I Believe (about R&D)

In short: I choose to believe:

• Human causal biology, rigorously applied (which it often is not) can and should guide R&D;
• The right organizational size, structure, and leadership is essential for R&D;
• Emerging technologies like AI will help improve scientific understanding and enable better decisions – after all, it wasn’t all that long ago (1992) when critics explicitly asked if, rather than AI, it was genetics and the Human Genome Project in particular that scientists were unduly fetishizing;
• R&D will inevitably retain a huge element of chance and uncertainty, and success will always require us to be lucky as well as good.

Everybody reading this column knows that biopharma is a difficult business.  Biology is unfathomably complicated and figuring out how to introduce something into the human body that does more good than harm is a fiendishly difficult challenge.

That’s why it’s important to recognize the occasional success. It reminds us what’s possible, and inspires us to think about how to achieve it more often (even as we consciously try to avoid the risk that Cass Sunstein highlights: selecting on the dependent variable and creating tidy post-hoc narratives around rare successes).

We’ll start with what still seems like an unimaginable achievement – the development of a therapy by Vertex Pharmaceuticals that effectively treats the vast majority of patients with cystic fibrosis. 

We’ll then look at this achievement in the context of Vertex’s R&D strategy and consider how they are attempting to challenge (and hopefully defy) the distressingly low odds of drug development, and to demonstrate that, despite the concerns voiced by some wags, that maybe, just maybe, it is possible to “pick winners.”  

Curing CF

First described by Columbia University pathologist Dorothy Hansine Andersen in 1938, cystic fibrosis is a heritable, autosomal recessive disease that affects approximately 40,000 people in the United States and 100,000 people globally. The disease is characterized by thick mucus secretions that logjam the airways in particular.  Afflicted children are beset by constant coughing and lung infections.  Until recently, most endured frequent hospitalizations and constant therapy, and had a median age of survival of around 30 years. 

In 1989, the causative gene, CFTR, was (heroically) cloned by several research groups.  That discovery prompted the next set of questions. Scientists wanted to know what the CFTR gene product actually did, and how disease mutations – including the most common CF mutation, called ΔF508 – affected the protein.

The story of the journey from CF gene to CF therapy, involving both academic researchers and industry scientists, is captured magnificently in a presentation offered by the key participants, as they accepted the 2023 Wiley Prize in Biomedical Science. The introduction and summary, by Richard Lifton, a geneticist and president of Rockefeller University, is superb. 

(See also this excellent 2019 Stat piece by Matthew Herper and Adam Feuerstein.)

Michael Welsh, a physician-scientist at the University of Iowa who shared in the Wiley Prize, told the story of the first CF patient he saw when he was a third-year medical student. 

We go in to see this little girl. She’s probably 7 or 8 years old. And as I watch her, she’s speaking in short sentences. She’s using her accessory muscles, respiration in her neck because she’s short of breath.

And as we talk, we find out that she has doesn’t have a normal life. She can’t go out and do the things that normal kids do. She’s spending much of her day with postural drainage, inhalation of aerosols.  When she coughed, she had this foul sputum. I began to recognize the odor of Pseudomonas aeruginosa in the sputum.

The hard part was when, after seeing her, we went to talk with the faculty, and we learned she might make it to the teens and she was not going to make it out of her teen years. That made a huge impression on me. It stuck with me all my life.

Welsh would go on to focus on the epithelial cells lining the airway, and, with colleagues, show (prior to the identification of the gene for CF) that “there was a problem in the airway with chloride getting out.”

After the CF gene was cloned — a prodigious effort — Welsh demonstrated that defective chloride permeability in cultured cells from patients could be restored with the introduction of the normal (“wildtype”) CF gene, but not with a mutant CF gene. This established a link between the genotype and the disease phenotype.

Welsh also conducted sophisticated patch-clamp studies to demonstrate that the CF gene encoded an ion channel; he was then able to dissect how different components of the channel worked and to understand how mutations disrupted the function. 

For example, some mutations prevented the protein from ever being made; others prevented the protein from folding correctly while still others interfered with proper channel activity.  The most common mutation, ΔF508, exhibited defects in both proper folding and channel opening.

A critical observation Welsh and his colleagues made was that the ΔF508 mutation was temperature sensitive, meaning that while it didn’t function at normal body temperature of 37 degrees Celsius, it did seem to function, somewhat, at lower temperatures, suggesting that if a medicine could duplicate this effect, then function might be restored.

The next set of speakers — Paul Negulescu, Sabine Hadida, and Fredrick Van Goor — described the ensuing stages of the journey — how industry translated this new knowledge of biology into an effective drug.

Negulescu had been working at a San Diego-based startup called Aurora Biosciences. Aurora was founded in 1995 to develop and commercialize assays using reagents like the green fluorescent protein developed by co-founder (and future Nobel Laureate) Roger Y. Tsien. 

In 2000, Aurora received a commitment from the Cystic Fibrosis Foundation to fund $47 million worth of work over five years. A year later, in 2001, Vertex Pharmaceuticals acquired Aurora Biosciences.

As Stat notes, it wasn’t clear if the nascent CF program was initially even on Vertex’s radar. But the funding commitment from the nonprofit CF Foundation contributed to Vertex’s decision to stick with the program rather than cut it.

A self-described “assay guy,” Negulescu approached the challenge of CF by seeking two types of molecules: “correctors,” addressing the protein folding defect, and “potentiators” seeking to restore channel function. The assay also relied on a Tsien reagent that responded to changes in membrane potential (so they could see if channel function was restored), and the temperature sensitive ΔF508 mutations described above.

Building on the initial hits was a chemist named Sabine Hadida, who described the herculean effort required to develop what would become a remarkably effective three-drug regimen.  Development of the first component, a potentiator called ivacaftor, required the synthesis and evaluation of around 800 compounds; first generation correctors such as tezacaftor required synthesis of 3,000 compounds; second generation correctors (e.g. elexacaftor) required upwards of 25,000. 

Subsequent work, as Fredrick Van Goor went on to describe, revealed that these molecules were unusual in several respects; they worked at a distance from the site of the causative mutation, and each bound the CFTR protein at a distinct site.  These interactions all involved parts of the channel that were embedded within the lipid membrane, explaining why the resulting drugs exhibited properties that appeared to “bend” traditional rules.

The clinical impact of the Vertex effort has been extraordinary. The triple combination of ivacaftor, tezacaftor, and elexacaftor (Trikafta) was approved by the FDA in 2019. Patients on the triple-combo treatment are projected to live 72 years (or even longer, if the drug is started when the patient is younger than 18), according to data presented by Van Goor. This compares with an estimated lifespan of 38 years with the best standard of care without these new medicines. These patients also live far healthier lives.

This is a monumental advance for the 90 percent of CF patients who are eligible.  (A different approach will be required for patients unable to manufacture the chloride channel in the first place, and Vertex is pursuing gene therapy-based solutions to address this critical need.)

From Drugs To Strategy

As Stat notes, by 2008, Vertex’s CF efforts had gained enough momentum that, in the words of former Vertex CEO Josh Boger, he “couldn’t stop the program if I tried,” even though it “remained a sideshow” for “management and its investors.”

The CF program could still have been killed when Vertex faced a moment of crisis in the early 2010s.  The company’s sole marketed drug, a hepatitis C therapy marketed as Incivek, was successful at first, then quickly rendered obsolete by more effective competitors.

Things came to a head at a 2012 board meeting led by CEO Jeff Leiden and attended by David Altshuler, a distinguished physician-scientist and geneticist at the Broad Institute who had joined the board of directors.  (He would leave the Broad to join Vertex as head of R&D several years later, in 2015.)

As Leiden saw it, Vertex had three options:

(A) Push forward with hepatitis C;

(B) Try to get acquired by someone who could then sort out next steps; or

(C) Shift the company’s focus to the still relatively early-stage CF program.  

Leiden recommended Option C. The board agreed, and Vertex would go on to deliver remarkable medicines with the power to transform the lives of CF patients (at least those patients eligible for, and with access to these medicines).

The Vertex CF story is actually the (extended) introduction to the R&D strategy topic I want to discuss: has Vertex identified a way to “pick winners?”

For context, we can turn to a fascinating talk Altshuler presented earlier this summer, and available here; many of the same points are summarized here and here, and amplified in this 2023 interview with Endpoints reporter Andrew Dunn, and in this 2024 profile by Michael Gibney.

Altshuler starts his talk by describing the challenges of R&D so familiar to readers of this column, emphasizing our limited understanding of human biology, and the challenge of predicting the impact of interventions. He then outlines Vertex’s R&D strategy, which is to limit the company’s focus, in an unusually rigorous fashion, to “causal human biology” – that is, “targets that have been validated in humans as playing a causal role in human disease.”  He has described this as “targeted conviction.”

This often, but not always, involves human genomics. 

Vertex also strives to be modality agnostic, similar to the concept of matching therapeutic modality to mechanism thoughtfully articulated and passionately advocated by Bristol-Meyer-Squibb CSO Robert Plenge.  Plenge is another champion of the use of causal human biology and a former Altshuler post-doc (see this piece about applying human genetics to drug discovery that Altshuler, Plenge, and former President of Merck Research Laboratories Ed Scolnick penned in 2013). 

The willingness to embrace any relevant modality or target reflects Altshuler’s belief that there isn’t a playbook for drug discovery – rather, “each disease has unique causal human biology, and cracking this biology presents a central challenge in the discovery of a novel therapeutic.” 

Readers will recognize an echo of former Pixar CEO Ed Catmull’s view that there isn’t a formula for successful films, and creative teams have to start from scratch each time.”

Altshuler says Vertex also seeks to “choose programs where there exist or we can invent highly predictive in vitro assays based on primary human cells, and early biomarkers that predict long-term success.”  Finally, he explains, Vertex strives to “select opportunities where the clinical and regulatory path enables efficient assessment of therapeutic potential and to potential approval.”

Altshuler contrasts this approach with many other biopharma companies, who he says tend to organize around a platform (like CRISPR or RNAi), a therapeutic area like cancer or neuroscience, or a “me too” fast follow approach. He suggests this represents commercial strategy more than a science strategy.

The heart of the Vertex approach is focused on data from people, not animal models (or AI models, for that matter).

He contends, “You can have a high success rate if you’re willing to go after human biology. It’s actually the not going after human biology that is the biggest problem in biotherapeutics.”

Altshuler cites not only the clinical success of their CF regimen, but also the recent FDA approval of their ex-vivo gene therapy program to treat sickle cell disease and beta thalassemia (by using CRISPR to excise a repressor of fetal hemoglobin); positive phase 3 data from a pain program strongly informed by human genetic insights; positive phase 2 data in a kidney disease program focused on the inhibition of the APOL1 protein; and encouraging early results from a program driven by my former post-doc mentor Doug Melton focused on transplanting pancreatic beta cells (generated by differentiating stem cells) into patients with type 1 diabetes.   

To be sure, Altshuler is not suggesting Vertex has come up with an infallible formula but argues their approach might be able to significantly improve the probability of success.

I’m not only attracted to Altshuler’s strategy, but (together with Nassim Taleb) have also advocated for it. 

As Taleb and I wrote in the Financial Times in 2008:

The next-generation pharma company will create a lean, agile organisation able to capture, consider and rapidly develop the best scientific ideas in a wide range of disease areas and aggressively guide these towards the clinic. Small market size will not deter their pursuit of promising drugs with a clear and comparatively inexpensive path to clinical development; their ideal portfolio will consist of an extensive collection of such molecules, cheap options that may offer unexpected benefit to patients and provide disproportionately large returns to investors.

Caveats

There are important caveats. FDA approval doesn’t always equate to commercial success and focusing on specialized products at extremely high prices can be tremendously challenging (particularly in the current political environment). That can be the case even if the value to the patient and the healthcare system is exceptional. 

(For now, at least, investors seem to like what they are seeing.  The company’s stock is near its all-time high, and the current market cap is north of $120B – ahead of Gilead Sciences, whose transformative hepatitis C products compelled Vertex to focus elsewhere).

Furthermore, while remaining agnostic about modality does maximize optionality, this approach may underestimate the difficulty of utilizing an emerging technology, where many of the details are still being worked out; presumably Vertex is hedging their risk in these areas by partnering with platform companies like CRISPR Therapeutics and Moderna.

Another key limitation – which Altshuler acknowledges – is that the human causal biology approach (“our quest to go where causal biology demands”), as Vertex applies it, will only work in conditions for which there are compelling data; it’s essentially like looking only where the (causal) light is.  

A Not-So-Secret Sauce?

Even so, the idea of leaning into causal human biology, as Vertex is, seems intuitive and increasingly supported by data. Why doesn’t everyone adopt the Vertex approach? 

Two responses spring to mind. 

First, large pharma organizations are invariably guided by market size projections and are perhaps unlikely to embrace the specialized markets Vertex tends to focus on. 

But this is unlikely the whole answer.

What I really think is happening is something similar to what we’re seeing in tech, where every tech company claims it’s embracing AI, whether it’s OpenAI actually pursuing artificial general intelligence or the many entrepreneur wannabes creating a “glut of scam companies that are little more than wrappers on OpenAI’s GPT tech,” as one Hacker News commenter aptly observed.

In biopharma, as BioCentury astutely noted, and as many readers have probably experienced, “casual human biology” is all the rage. 

“Expectations are rising for researchers to show newly proposed drug targets have a causal role in driving or preventing disease,” writes BioCentury’s Karen Tkach Tuzman, adding that there’s a “mandate to provide proof of causal human biology for novel targets.” 

Tuzman continues,

The phrase is on the lips of research heads and early-stage investors, who use it to mean that a target or pathway plays a role in causing or preventing a human disease, such that modulating it will cause an intended effect in patients. Its rise has paralleled a shift in which the traditional strategy of proposing target hypotheses based on animal studies is taking a back seat to human-first approaches.

What’s more, AI approaches, as BioCentury also notes, increasingly seek to provide computational insight into networks and relationships, quantify causality, and increase probabilities of success. 

In theory, this suggests we’re likely to see a marked increase in translational success, but in practice, what actually seems to be happening across the industry is that “human causal biology” is invoked almost universally to justify any given approach to any given target. 

I don’t think there’s a single program in biopharma R&D that doesn’t have a “causal human biology” narrative to which they can point.

My sense is that Altshuler and Vertex have far more stringent criteria for “causal human biology” than most others, and place particular emphasis on primary insights from human beings rather than what J.S. Haldane called “scraps and fragments” of people (a patient-centric framework Joe Martin, Denny Ausiello, and I advocated here in 2000).  This deliberately high bar may contribute to Vertex’s apparently high success rate. 

By analogy, I’d point to the example of Danaher and its rigorous application of the principle of “kaizen” – continuous improvement. While most every company claims to embrace kaizen, I don’t know of an organization that is more rigorous about it than Danaher, or, over time, more successful. Vertex is as serious about causal human biology as Danaher is about kaizen – a commitment that may be associated with achieving better than expected performance.

Getting Better?

The hope, of course, is that:

• The Vertex approach demonstrates consistent, long-term success in picking winners at a significantly higher rate than average, leading to both clinical and (perhaps underestimated) commercial success.
• Other firms learn to adopt a similarly rigorous approach, and ideally make valuable refinements of their own. (To be sure, Regeneron and Amgen, in particular, have also leaned emphatically into human genetics.  However, as Tuzman writes, the “scarcity of clean genetic signals” raises “a question among players,” namely “how strongly to prioritize genetics relative to other data types.”)
• Most importantly, the science of causal human biology (potentially assisted by AI, as Tuzman describes) advances so that the ability to select and prosecute promising biological targets with Vertex-level rigor and discrimination continues to grow, expanding the group of patients who could benefit from impactful new medicines.

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.