In my previous blog series I talked about why genetics is important in drug discovery: human genetics takes you to a target, informs on mechanism of action (MOA) for therapeutic perturbation, provides guidance for pre-clinical assays of target engagement, and facilitates indication selection for clinical trials.
Here, I provide an overview of a new blog series on how genetics influences decision-making during drug discovery. The key principle: human genetics establishes a disciplined mindset and a firm foundation – anchoring points – for advancing targets through the complicated process of drug discovery. [For those less familiar with drug discovery, the end of this blog provides a brief primer on the stages of drug discovery.]
I highlight three areas: establishing a balanced portfolio, identifying targets with novel MOA, and creating a framework for objective decision-making. In subsequent posts, I will focus primarily on how human genetics informs on the latter (decision-making), with blogs pertaining to designing assays for screens and target engagement, utilizing pre-clinical animal models, predicting on-target adverse drug events, and selecting indications for clinical trials.
1. Establish a balanced portfolio
Whether in academic research, a small biotech company (see here) or a large pharmaceutical company (such as Merck, where I work), a balanced portfolio of projects is very important. In early discovery, there are many ways to select targets and therefore establish an early discovery portfolio. Some may prioritize targets based on tractability for a particular modality (small molecule, biologics, RNAi, gene therapy, etc.), whereas others may prioritize targets that align with therapeutic areas (e.g., orphan diseases, autoimmune diseases, childhood vaccinations).
I believe that a portfolio of projects anchored in human genetics will outperform a portfolio of projects based on other principles.
From the outset let me state clearly that this is NOT to say that animal models are not important for finding new targets; this is NOT to say that epidemiology, epigenetics and other phenomenological observations are not important for finding new targets; and this is NOT to say that there are not other ways for finding new targets. (Sorry – lots of double negatives in that sentence!) Ideally, a balanced portfolio should probably include targets based on non-genetic evidence (assuming the target is rooted in causal human biology). As one example, anti-TNF drugs to treat rheumatoid arthritis (RA) and other inflammatory conditions would not have easily emerged from human genetics alone (see here).
However, I believe that the bulk of targets in a successful, diversified portfolio should come from human genetic targets, as well as other targets that have emerged from experiments of nature in humans.
What is the evidence to support this view?
First, the current model of drug discovery is inefficient and fraught with false positive findings. Thus, the field needs a new approach, and genetics represents one possible approach. That is, something needs to change!
Second, there is anecdotal evidence to suggest that human genetics predicts targets with an increased probability of success (see Table 2 in our Nature Reviews Drug Discovery review here). Examples of drug-gene pairs (and their indications) include: abatacept-CTLA4 (rheumatoid arthritis); ivacaftor-CFTR (cystic fibrosis); and ustekinumab-IL12B (psoriasis); statins-HMGCR (hyperlipidemia). Another example is PCSK9 and LDL cholesterol (although not yet FDA-approved).
Third, retrospective analyses indicate that project portfolios based on human genetics perform better than portfolios of targets without human genetic data. An example comes from the AstraZeneca pipeline: targets with human genetic evidence were approximately 2-fold more likely to demonstrate favorable efficacy in Phase II than targets without human genetic evidence (see Figure 3 of this Nature Reviews Drug Discovery publication).
And fourth, we have shown that biological pathways anchored in human genetics are enriched for approved therapies in one disease, rheumatoid arthritis (see Nature paper here).
What is important to remember is that a reduction in Phase II attrition from 66% to 50% would decrease the cost per new molecular entity by ~$0.5 billion, and a reduction in Phase III attrition from 30% to 20% would decrease costs by ~$0.3 billion (see here). That is, even modest improvements in probability of success have dramatic effects on drug development costs.
Despite this optimism, I admit that this is still an experiment in progress. There are many reasons why human genetics may not lead to increased probability of success (see “Limitations of genetics-based target validation” section in Nature Reviews Drug Discovery review here). I expect that this experiment will play out in the next 10 years, which will reveal where we are today on the “hype curve” (see here). While I believe we are on the “slope of enlightenment”, it is possible we are much earlier on the curve (e.g., “peak of inflated expectations”).
2. Identify unexpected targets and novel mechanisms of action
One of the major challenges in drug discovery is to find targets with novel mechanisms of action that differentiate from standard of care. What happens in practice, however, is that drug discovery consolidates around established biological pathways. Inevitably, this leads to the “streetlight effect” problem – drug hunters only look for new targets by looking where it is easiest (e.g., where the biology is known and where there are good pre-clinical models). Because human genetics provides an unbiased approach to discovery new targets, human genetics attempts to uncouple bias in what we know from our desire to find novel drug targets.
This is good and bad. It is good because it is unbiased and provides unexpected targets, which is important in uncovering new mechanisms that will differentiate from standard of care. But it is also bad for the very same reason – because it discovers unexpected biology that may be difficult to pursue experimentally. Alas, genetics can be very inconvenient!
One example is the LRRK2 gene and Parkinson’s disease (see here). More than 100 LRRK2 gene mutations have been identified in families with late-onset Parkinson’s disease. However, it is unclear how LRRK2 mutations lead to movement and balance problems, and in particular, what pharmacodynamics biomarkers should be used to measure LRRK2 target engagement in human clinical trials. To catalyze research in this area, the Michael J. Fox Foundation is pioneering an innovative approach to LRRK2 in an effort to streamline and orchestrate drug development around the gene product (see here).
3. Create “anchoring points” for objective, focused decision-making
While there are many perspectives on how to make decisions during the development of a drug (see David Grainger post here; David Shaywitz post here), it is uniformly agreed that these decisions are not easy yet crucial for an efficient (and cost-effective) R&D process.
What I have observed is that unless there is at least one piece of data that a team strongly believes predicts success – an anchoring point – then decision-making becomes too subjective and too heavily influenced by the strong opinions of single individuals. I believe that human genetics can help make objective, focused decisions in drug discovery.
For example, one of the first question I ask my team about a target is: What is the human evidence to support a therapeutic hypothesis, with an emphasis on causality for a target and specific MOA? If a target has strong human evidence that demonstrates perturbation of a target is relevant to human disease (e.g., clinical validation via pharmacology, human genetics), then it has a greater probability of success (POS) in Phase II/III clinical trials. If a target has increased POS, then it is natural to interpret data and make decisions with that in mind.
Human data – for example, human genetics – serve as the anchoring point.
Another way to think about “anchoring points” is to imagine the number of steps it takes to progress from an idea about a drug target to an actual drug. There are literally hundreds of steps, if not more. Now, imagine having to make decisions at each of these steps about whether there is sufficient evidence to go forward (a “go” decision) or to stop the program (a “no go” decision). At each step, I believe there must be an anchoring point that creates a thread between the idea and the clinic.
I recently came across a strangely beautiful video that displays the visual artwork of 804 choreographed wooden balls (see here). Movement of each on their own would seem random; even if a few balls were moved out of place, the artwork would turn from beauty to chaos. Further, if the wooden balls were not observed from the right perspective, movement appears random. I could not help but think of drug discovery and the number of steps it takes to move from an idea to the clinic. If there were no choreography or no frame of reference – no anchoring point – then the Fibonacci spiral inspired flower would be nothing but a bunch of, well, wooden balls. With choreography and perspective, there is absolute splendor.
It is this theme – genetics-inspired decision-making – that I want to pursue in greater depth. Over the next several weeks, I will write additional blog posts on genetics and decision-making in drug discovery, with a focus on:
Part 2: genetics and assays for drug discovery
Part 3: genetics and animal models for drug discovery
Part 4: genetics and on-target ADEs for drug discovery
Part 5: genetics and indication selection for drug discovery
Brief primer on drug discovery
For those less familiar with the drug discovery process, let me briefly the general steps before large and expensive Phase II/III clinical trials (see detailed slide deck here).
target selection: choosing which target to prosecute for a particular clinical indication;
target validation: building a biological package to support the therapeutic hypothesis that perturbing a target with a specific mechanism of action (MOA) will be safe and effective in humans;
screening: generating initial molecules (“lead molecules”) that recapitulate the desired MOA; the exact steps depend on the therapeutic modality of the lead molecule (e.g., small molecule, biologic, peptide, natural products, RNAi);
lead optimization: turning the lead molecule into a molecule with appropriate drug-like properties (e.g., pharmacokinetics (PK) / pharmacodynamics (PD), safety) and appropriate biomarkers to measure how the drug is working in humans; and
first-in-human: initial tests of the drug in humans to assess toxicity, dose range, and PK/PD, often in healthy controls, with line-of-site into a particular clinical indication for studies of efficacy in patients.
What should be clear is that each step requires active decisions to advance a program forward, with go / no-go experiments at each stage-gate. And while these decisions might be objective, they often lack a firm foundation.