Every life sciences company needs to make good program choices. Big pharma creates value through smart portfolio management while small biotech companies can be defined by a single lead asset. In both cases, the opportunity cost of poor decision-making can be extremely high.
Even early-stage companies face this challenge. Here’s a typical scenario: a biotech company has raised a sizable Series A and is now charged with proving out a technology platform so capital can be raised at a meaningful step up in value. With the internal rate of return (IRR) clock ticking, investors are eager to see proof of principle and pipeline progression. This puts the management team under a lot of pressure to get something, in fact, anything into the pipeline.
Unless managers and investors are really disciplined, technology ‘push’ can take over in favor of the market ‘pull’ and the first products out of a platform end up proving the technology but do not deliver against a clear patient need e.g. yet another TNF?-targeted therapeutic.
Asking the right questions
Good portfolio choices are made all the time but I do not feel that we get this right as an industry on a consistent basis. There still seems to be a lot of luck involved and, more often than not, we end up in a situation where ten companies are focused on the same target. This herd mentality may make us feel better about our R&D decisions but such an over concentration of resources ultimately erodes profitability and increases the overall risk of the industry’s R&D portfolio.
We try to be thoughtful about target selection at Nimbus, and have developed our own flavor of decision making to reflect the strengths of our platform, but it’s still an inexact science. One advantage we have is the fact that we focus on targets where others have tried and failed. This helps us avoid being in a horse race with lots of other companies but does leave us with some hard chemistry problems to solve. When considering a new project, we seek to answer the following questions:
- Is the biology compelling? You need to be convinced that there is a good rationale for why modulating a target or biology will do something interesting in humans. Making sense of massive amounts of seemingly unrelated biological data requires the judgment of experienced drug hunters. We have found that human genetics, and evidence from biologics targeting similar pathways, increasingly underpins the targets that we have in our pipeline.
- Will our technology work where others won’t? This tends to be the most black and white criterion since experience has taught us which targets are the most amenable our discovery approach. Importantly, we need to believe that we can offer something that’s truly differentiated versus others in the marketplace (similar to the thinking described here for macrocycles). Having confidence in the tractability of a target means understanding the underlying structure-activity drivers and then seeing confirmation through initial virtual screening and validated chemical leads.
- Can we execute? This means being realistic about what it will take to create a product within the confines of your specific platform and operating model. For us, this means picking targets that are amenable to the virtual research model, which includes access high-quality collaborators and bespoke pharmacology models. This has driven our focus towards oncology, autoimmune, metabolic disease and genetically-defined disorders.
- Can we demonstrate value early? The reality is that seeing value inflection early in a program is key to creating attractive future options whether raising money at better cost-of-capital or partnering a program. It is highly desirable if our preclinical models and early clinical studies can tell us something useful that reduces overall program risk and frames up the differentiability of our programs.
- Is the market need compelling? This seems obvious but it is often incredibly difficult to answer with any precision for an early-stage drug discovery project where the exact disease and product profile are difficult to describe based on what’s known at the time.
Having spent a lot of time thinking about this over the past few years, we have seen a number of themes emerge:
Visualizing the patient need
Some would argue that the market need should be the most important question. Instead of reducing the problem to a biological target, we should start with the need that exists in patient care and then deliver solutions. In a sense, the industry needs to evolve in the same way that IBM did, from hardware to services.
The difficulty is that drug discovery hasn’t yet progressed to a point where it is as commoditized as computer technology. A lot of value can be created through the sheer act of drugging a sought-after biological target for the first time. Moreover, we are a long way from really understanding the underpinnings of human biology so cannot draw a straight line between a biological target and its utility in a specific disease or patient population.
Genomics, enabled by large-scale sequencing, is starting to help. There are now situations where we can have a clear idea in early discovery as to which patient and which disease we want to treat. A case in point is diffuse large B-cell lymphoma where the most common driver mutation is in an adapter protein called MyD88. This mutation leads to highly aggressive disease and worse outcomes (the problem). This observation allows us to imagine how direct-acting MyD88 or IRAK4 inhibitors can be used to selectively kill tumor cells with the mutation (the solution)
Where possible, target selection should therefore start with a clear idea of the intended patient population. This allows us to translate a specific patient need into a clear drug discovery problem, against which we can then deploy our favorite discovery approach. We have done this with our lead programs and there is clear evidence that the markets reward this type of strategy with Loxo Oncology (Trk) and Clovis Oncology (EGFR) as recent examples.
Reduction to practice
To establish a rationale for patient selection early, it is important to have the right pharmacological tools. We have adopted what we refer to as a ‘rapid prototyping’ model which means coming up with reasonably potent and selective matter really quickly (in 3-6 months). These prototype chemistries can establish the link between a target and a potential patient population and can be shared with leading academics in the form of tool compounds to build excitement around the target choice. Early in the IRAK4 project, we were able to demonstrate the selective killing of tumors cells with the activating MyD88 mutation in collaboration with Lou Staudt at the National Cancer Institute, which immediately gave us confidence that such patients could be targeted in the clinic.
In reducing a hypothesis to practice in the form of a small molecule, you can learn an incredible amount of new biology in a way that reads directly on the potential of a therapeutic. These results can deviate significantly from what you learn from traditional target validation studies (such as genetic knockouts) so go a long way to establishing the rationale for a program. Taking this paradigm to the next level, we have used tissue-selective molecules to interrogate the pharmacology in the intended target organ.
Cutting your losses
The flip side of knowing what to work on is being clear about when to stop. Portfolio reviews are common in larger organizations but decision-making is neither simple nor transparent. Biases inevitably exist due to politics between different organizational silos and by what behavioral economists call loss aversion, which results in over investment in failing programs.
In small companies, a certain amount of gamesmanship also comes into play to ensure that capital is raised before critical company-defining datasets are generated. This can induce companies to postpone critical ‘killer’ experiments resulting in wasted resources and opportunity cost.
Everything else being equal, when selecting a new target to work on, it is important to define a priori the objectives of the program and the pivotal, hypothesis-bearing experiments. Answering these questions correlates well with the reduction in cost of capital. We will never have all the information we need to make a new program decision but we can at least be explicit about the underlying assumptions and the path to testing them. This means that target selection is not a single point in time but an evolving process where new data become available all the time. Organizations that can respond real time, and can even pivot rapidly based on new data, are best positioned to build long-term value.
This is an industry full of geeks (I freely admit to being one). We love cool science and do a pretty good job at understanding, and then minimizing, technical risk. After all, it can be a Herculean feat to get a new technology to work so we sometimes want to point our shiny new toy at a project that doesn’t layer on incremental target risk.
But this can lead to an undifferentiated lead program that then takes on life of its own and suddenly becomes an expensive, clinical-stage program that comprises 90% of the company’s value. Overall, risk is not reduced but is just shifted to clinical, commercial and reimbursement endpoints that are very timely and expensive to prove out … and, face it, we are much better at assessing technical risk than any other type. So we should be weary of so-called “derisked” targets if it will subsequently be hard to show differentiation versus others in the market place.
Being bought not sold
It’s often said that, “great companies get bought not sold”. I would say the same thing about R&D programs. Notably absent from this blog is any discussion around what our pharma partners are looking for. Yes, we must convince our partners that we have innovative approaches for treating disease but I do not believe that we stand to gain much by chasing what we perceive Pharma is looking for. Priorities, portfolios and personnel change far too rapidly for this to be a fruitful approach. Instead, we need to have the conviction to invest behind a compelling biology and patient need.
In conclusion, it is worth nothing that drug discovery requires us to take incredible leaps into the unknown. This is not going to change but new tools and ways of thinking about target selection are at least giving us a better idea of where to jump.